The Economic Journal

Yi,, Junjian;Heckman, James, J.;Zhang,, Junsen;Conti,, Gabriella

doi: 10.1111/ecoj.12291pmid: 27019517

Abstract In response to health shocks, parents make compensatory and reinforcing investments in different dimensions of human capital across children. Using household data on Chinese child twins whose average age is 11, we find that, compared with the twin sibling who did not suffer from negative early health shocks at age 0–3, the other twin sibling who did received 305 yuan more health investment, but received 182 yuan less educational investment. Overall, the family acts as a net equaliser in response to child early health shocks across children. The importance of the family in fostering child human capital is well understood by economists. How parents invest in children with different endowments is not well‐studied and there is no consensus in the literature. Becker and Tomes (1976) and Tomes (1981) suggest that parental investments reinforce initial endowments and that such behaviour increases inequality. Griliches (1979) conjectures that parental human capital investments compensate for gaps in children’s endowments and that the family is an equalising agent. A number of empirical studies find evidence for reinforcing behaviour (Behrman et al., 1994; Rosenzweig and Zhang, 2009). Other studies find empirical support for compensating behaviour (Behrman et al., 1982; Pitt et al., 1990). This article studies how early health shocks to children affect intra‐household resource allocation and the human capital formation of children. For two reasons, early health shocks in developing countries are likely to affect children’s human capital accumulation and long‐run outcomes negatively (Strauss and Thomas, 2007; Currie and Vogl, 2013). First, young children are especially vulnerable to health shocks in developing countries. For example, more than 10% of children suffer from diarrhoea in many developing countries such as Bangladesh (Strauss and Thomas, 1998). Second, in the absence of public health insurance and in the presence of pervasive poverty, a child affected by a negative health shock may not receive appropriate medical treatment. Consequently, early health shocks may have long‐lasting consequences. In the absence of a well‐functioning public education system, the consequences of an early health shock may be exacerbated and thus impair human capital formation (Glewwe and Miguel, 2007). This article formulates and estimates a model with two channels through which early health shocks affect child human capital formation. The first is a biological channel operating directly through the production function for human capital. The second is an intra‐household resource allocation effect arising from parental responses to the shock. Parental responses to early health shocks on children may be more important in developing countries with weaker health infrastructure and less well‐established credit markets and social protection systems. The absence of an old‐age pension system and the presence of tight credit constraints may drive parents to base their intra‐household resource allocation decisions on efficiency rather than on equity concerns. In this case, parents are more likely to reinforce the harmful effects of an early health shock by devoting less resources to the less‐endowed child. The role of the family must be considered when designing public policies to remedy the effects of inequality at birth or the early childhood stage. Following recent developments in the economics of human capital (Cunha and Heckman, 2007; Heckman, 2007; Cunha et al., 2010), our theoretical analysis extends the conventional literature on intra‐household resource allocation in two ways. First, we allow for multidimensionality in human capital. The conventional literature assumes a single dimension of human capital on which parents can compensate or reinforce. Borghans et al. (2008), Cunha et al. (2010) and Almlund et al. (2011) extend the analysis of human capital from a single dimension to multiple dimensions and emphasise the cross‐productivity of different types of human capital. These studies focus on the human capital production process of individuals and do not explore the implications of multidimensionality of human capital for the intra‐household resource allocation across children. Second, we examine the interaction of parental preferences and the human capital production function in the intra‐household resource allocation process. The conventional literature focuses on parental preferences and has made special assumptions about the role of human capital production in the intra‐household resource allocation process. For example, Becker and Tomes (1976) and Pitt et al. (1990) assume a linear production function with respect to child endowments, whereas Behrman et al. (1982, 1986) assume a Cobb–Douglas technology. Under both specifications, parental investment strategies are determined only by parental inequality aversion across children. Our study combines the traditional literature on intra‐household resource allocation with recent developments in the economics of human capital. We demonstrate that parents make reinforcing and compensatory investments in different dimensions of human capital in children in response to health shocks. Whether parents exhibit a reinforcing, compensating or neutral investment strategy is ultimately an empirical question. We shed light on these mechanisms by estimating the effect of child early health shocks on family investments. We use data from the Chinese Child Twins Survey (CCTS), which contains detailed information on family health and educational investments separately for each child whose average age is 11. Our data are described in greater detail below. To the best of our knowledge, CCTS is the first census‐type household survey on child twins around the world. We find evidence of compensating investments in child health and reinforcing investments in education in response to early health shocks for one twin child in the family. Our empirical results show that, compared with the twin sibling who did not suffer from negative early health shocks at ages 0–3, the other twin sibling who did received 305 yuan more health investments in the 12 months prior to the survey. This amount is substantial and is more than one third of the average family investment in child education per year or about one half of maternal monthly wage. Offsetting this in a different dimension, on average, the sick child received 182 yuan less on educational investments than its twin sibling. We estimate the child human capital production function. Holding constant family investments, the estimated coefficient on early health shocks in the production function reflects only a biological effect. We separate the biological effect from the intra‐household resource allocation effect. Because family investments are chosen, and unobservables in choice and outcome equations are likely to be correlated, we correct for spurious correlation bias using 2SLS with price and non‐labour income as instruments. Our estimates show that family investments have positive productivity effects and that early health insults negatively affect child outcomes, including health, education and socio emotional skills. We also estimate a human capital production function excluding family investments. These reduced‐form estimates correspond to the total effects of early health shocks on child human capital. From them we can infer the importance of the intra‐household resource allocation effect by comparing the reduced‐form estimates with the estimates from the structural production function. We find that reduced‐form estimates understate the biological effect by one‐half for anthropometric measures, such as body mass index (BMI), but overstate the biological effect by one‐third for a number of educational outcome measures. Our findings have important policy implications. When parents simultaneously compensate in health investments and reinforce in educational investments across their children, the effect of family investments on inequality in the society becomes more nuanced. A multidimensional perspective on inequality is warranted. The overall level of inequality is overestimated if one focuses solely on inequality in education because inequality in health is reduced by family investments. Our estimates suggest that the Chinese family appears to be a net equaliser in terms of the aggregate investment response in value terms child human capital investment when both education and health are combined. Parental responses should be considered when designing intervention policies to remedy disadvantages among children because parents can exacerbate or eliminate these effects by reallocating resources within the family. Our results shed light on recent literature on the effect of early‐life conditions on late‐life outcomes (Case et al., 2005; Almond and Currie, 2011). Although the literature has achieved a consensus on the negative effects of early‐life health insults on both short‐run (Currie et al., 2010) and long‐run outcomes (Smith, 2009), the role played by parental behaviour remains unclear. The reduced‐form estimates of the effect of early‐life shocks that disregard intra‐household responses do not necessarily represent a biological effect. When parents make compensating and reinforcing investments along different dimensions of human capital, the reduced‐form estimates cannot be unambiguously interpreted as upper or lower bounds of biological effects. Our empirical analysis suggests that reduced‐form estimates of early health shocks on child health understate the biological effect, whereas those for child education overstate the biological effect. These results imply that caution must be taken in interpreting reduced‐form estimates as biological effects and confirms the importance of considering parental behavioural responses when studying the consequences of early‐life health insults. The remainder of the article is organised as follows. We derive our theoretical model in Section 1. In Section 2, we describe the CCTS data used to test our theoretical prediction. Our econometric specification is presented in Section 3. We present the estimation results in Section 4 and conclude in Section 5. 1. The Conceptual Framework This Section analyses child early health shocks, intra‐household resource allocation and child human capital formation. We show that an early health shock can affect child human capital through two channels: a direct channel (the biological effect through the production of human capital) and an indirect one (the intra‐household resource allocation effect through parental responses). By introducing the multidimensionality of child human capital, we show that parents can compensate and reinforce along different dimensions of a child’s human capital with respect to an early health shock to one child. 1.1. The Model We assume that each family has two children (⁠ ι=i,j ⁠).1 Each child has two components of human capital: health (H) and a bundle of cognitive and socio‐emotional skills (C). We treat the latter as an aggregate in this subsection. Child prenatal endowment such as birthweight is ωι,τk ⁠; parental human capital investments is Iι,τk ⁠, and child human capital is θι,τk ⁠, where k=H,C ⁠. We further denote a child’s characteristics such as gender and ethnicity by ξι,τ, and parental characteristics by hτ. The human capital production function of type k for child ι in family τ is specified as follows: θi,τk=fk(ωi,τH,ωi,τC,Ii,τk,ei,τH;ξi,τ,hτ),(1) where ei,τH is defined as a postnatal negative health shock affecting child i at early stages, and ∂θi,τk/∂ei,τH<0 ⁠. Child human capital is determined by the child’s endowments, human capital investment and health shocks. Parental and individual characteristics also affect the formation of child human capital. The production technology of health differs from that of cognitive skills. The production function is the same for all children in family τ, but may differ from one family to another.2 In (1), we assume that the health shock of child j does not directly enter child i ’s human capital production function, although ejH can indirectly affect child i ’s human capital through parental investment. Thus, we assume away a contagious effect of early health shocks in the model, but we provide evidence for this assumption in online Appendix A.3 Second, we focus on health shocks; our data show that the most prevalent health shock is diarrhoea. Parents are assumed to value child outcomes. They also care about their own consumption and leisure. Parental preferences are represented by the utility function: U=U(c,l,qi,qj),(2) where c is parental consumption, l is parental leisure time and qι is the quality of child ι. Denoting T as the parental labour supply and normalising the parental time endowment to one, we have l + T = 1.4 Child quality is a combination of health and cognitive skills such that qι=q(θιH,θιC) ⁠. Both children have the same quality function. However, they may have different qualities because the endowments, early health shocks and human capital investments could be different. The budget constraint is specified as follows: pI∑ι∑kIιk+c+wl=Y+w,(3) where pI is the price of human capital investment and is assumed to be independent of the type of investment; w and Y are parents’ wage rate multiplied by time available (assumed to equal 1) and non‐labour income. The price of parental consumption is normalised to one. We further assume that parents provide all the resources for their children’s human capital.5 1.2. Child Early Health Shock and Parental Responses We now analyse how parents adjust intra‐household resource allocation in response to an early health shock on their children. The parents’ problem is to maximise the utility function (2) subject to the budget constraint (3) and the production technology (1). If the utility function and the production function are strictly concave and continuously twice‐differentiable, then the existence, uniqueness and continuity of the solution to the intra‐household resource allocation problem directly follow. Deleting family subscripts, we denote the optimal human capital investment of type k in child i as a function of the following form: Iik*=ψk(ωiH,ωiC,ωjH,ωjC,eiH,ejH,ξi,ξj,h,pI,w,Y).(4) A reinforcement strategy for investment of type k arises if ∂Iik*/∂eiH≤0 and ∂Iik*/∂ejH≥0 ⁠, i.e., parents put less investment of type k in the child who has suffered from an early health shock and place more investment in his or her twin sibling who has not suffered. In this case, (∂Iik*/∂eiH)−(∂Iik*/∂ejH)≤0 ⁠. In contrast, if ∂Iik*/∂eiH≥0 and ∂Iik*/∂ejH≤0 ⁠, we say that parents use a compensatory strategy in investment of type k in children. Thus, (∂Iik*/∂eiH)−(∂Iik*/∂ejH)≥0 ⁠. The definition of reinforcing or compensating strategies does not presuppose any specific model of intra‐household resource allocation. The parameters determining which type of strategy parents adopt depends on the specific model employed. For example, Behrman et al. (1982) assume a Cobb–Douglas production function and a constant elasticity of substitution (CES) parental utility function. They show that the optimal investment strategy is uniquely determined by parental preference parameters. Almond and Currie (2011) assume a CES production function and a Cobb–Douglas parental utility function. In their case, the optimal investment strategy is uniquely determined by production technology parameters. In a more general model with multidimensional human capital, the child human capital investment strategy reflects not only parental preferences but also the production technology available to them. Parents can compensate and reinforce along different dimensions of human capital with respect to early health shocks. Family investment can exacerbate inequality in one dimension but, at the same time, ameliorate inequality in another dimension. Our analysis does not impose particular functional forms. Online Appendix B discusses the consequences of specific choices of functional forms further. 1.3. Early Health Shocks, Parental Responses and Child Human Capital Early health shocks affect child human capital through two different channels: a biological effect and a behavioural effect. From (1), the total effect of an early health shock on child i on the child’s human capital k can be decomposed as follows: dθikdeiH⏟A=∂θik∂eiH⏟B+∂θik∂Iik⏟C×∂Iik∂eiH⏟D.(5) The term on the left‐hand side (A) is the total effect of an early health shock, which corresponds to the reduced‐form estimate in the literature. The first term on the right‐hand side (B) is a biological effect that directly operates through the production function and is assumed to be negative. The second term (C×D) is a behavioural effect that operates through parental responses in adjusting family investment. The behavioural effect is the product of the productivity effect of the investment (C) and the intra‐household resource allocation effect (D). In general, the effect of an early health shock is not the same as the biological effect. We assume that the productivity effect of family investment is positive, an assumption tested below. The sign of the behavioural effect is determined by the intra‐household resource allocation effect, which cannot be determined a priori, and can vary across different dimensions of human capital. The reduced‐form estimate (A) is interpreted as an upper (lower) bound of the biological effect if we know that the parents adopt a reinforcing (compensatory) strategy (which is characterised by the sign of D). We can separate the biological effect (B) from the behavioural effect by estimating (1) controlling for family investment. By comparing the estimate of the biological effect (B) with the reduced‐form estimate of the total effect (A), we can quantify the importance of the behavioural response in family investments to account for the total effect of early health shocks on child human capital. 1.4. Early Health Shocks, Parental Labour Supply and Consumption Early health shocks to children could result in external effects on other family members. In this article, we study the effect of early health shocks on parental labour supply and consumption. The optimal parental labour supply (⁠ T* ⁠) and parental consumption (⁠ c* ⁠) is a vector function of the following form: y=y(ωiH,ωiC,ωjH,ωjC,eiH,ejH,ξi,ξj,h,pI,w,Y),(6) where y=(T*,c*) ⁠. Adopting specific functional forms in the example presented in online Appendix B, we show that a child’s early health shock decreases parental consumption and increases parental labour supply. 2. Data 2.1. The Chinese Child Twins Survey (CCTS) The CCTS was conducted by the Urban Survey Unit (USU) of the National Bureau of Statistics in late 2002 and early 2003 in Kunming, China. Kunming, which is the capital city of Yunnan Province, has a total population of approximately 5 million. Yunnan is a relatively underdeveloped province located in the far south‐western corner of China. To the best of our knowledge, CCTS is the first census‐type household survey on twin children. The survey includes almost all households with twins aged between 6 and 18 years living in Kunming in 2002. The average age of the twin children is 11. The households have been initially identified by the USU on the basis of the 2000 population census according to whether the children have the same birth year and month and whether they have the same relationship with the household head. The addresses of these households are then obtained from the census office, and the presence of twins is verified with a visit to the household. Starting from 2,300 pairs of potential twins identified in the census, 1,694 households with twins are successfully interviewed. The survey covers an extensive range of information about family investment in each child separately and child outcomes, in addition to a wide range of demographic, social and economic information at the household level. See Rosenzweig and Zhang (2009) for a detailed description of the CCTS. 2.2. Descriptive Statistics We now describe the variables in our data that are the empirical counterparts of those in the theoretical analysis. Table 1 tabulates the descriptive statistics. Early health shocks (⁠ eH ⁠) are defined by a dummy variable that indicates whether a child suffered from a serious disease from ages 0 to 3. The complete list of diseases include serious diarrhoea, calcium deficiency, asthma, fracture, attention deficit disorder, heart disease, serious hearing difficulties, whooping cough, stammer and serious eyesight problems. The first three constitute 92% of the serious diseases suffered by children, and such a number is consistent with the evidence for children in developing countries (Strauss and Thomas, 1998).6 Table 1 shows that the prevalence rate of early health shocks in our sample is 9%. We address potential concerns with various types of measurement errors in constructing the variable of child early health shocks in online Appendix C. Table 1 Descriptive Statistics Theoretical variables . Empirical counterparts . Mean . SD . Within‐twin SD/overall SD . (1) . (2) . (3) . (4) . (5) . eH Early health shocks (dummy) 0.09 0.28 0.35 IH Health investment (⁠ ¥/year) 225.83 772.00 0.62 IC Educational investment (⁠ ¥/year) 910.44 1,225.73 0.20 θH Height (cm) 137.33 19.30 0.13 Weight (kg) 33.60 11.82 0.16 BMI 17.39 3.22 0.27 General health status* 2.92 0.63 0.34 θC Literature (score: 1–100) 81.93 13.79 0.42 Literature (relative measure)† 3.53 0.84 0.48 Mathematics (score: 1–100) 80.90 16.41 0.43 Mathematics (relative measure)† 3.48 0.92 0.50 Good student awards (dummy) 0.24 0.43 0.51 Awards in contests (dummy) 0.07 0.25 0.49 Grade repetition (dummy) 0.04 0.21 0.52 Doing minor actions in class‡ 1.73 0.76 0.49 Always feel lonely§ 1.20 0.50 0.34 Easily distracted§ 1.59 0.68 0.34 Easily frightened§ 1.37 0.60 0.28 Emotionally unstable§ 1.12 0.35 0.28 T Paternal labour supply (days/month) 25.51 4.68 Maternal labour supply (days/month) 25.32 4.72 c Paternal consumption (⁠ ¥/six months) 700.33 869.38 Maternal consumption (⁠ ¥/six months) 283.81 736.59 ω Birthweight (kg) 2.46 0.47 0.36 ξ Male 0.49 0.50 0.50 Age 11.19 3.09 Born at the first parity 0.79 0.40 h Maternal age 36.85 4.84 Maternal ethnicity (Han = 1) 0.86 0.35 Maternal schooling years 8.65 3.28 w, pI Maternal working sector (Public = 1) 0.08 0.27 Rural 0.53 0.50 Y Household asset (score) −0.05 1.73 Theoretical variables . Empirical counterparts . Mean . SD . Within‐twin SD/overall SD . (1) . (2) . (3) . (4) . (5) . eH Early health shocks (dummy) 0.09 0.28 0.35 IH Health investment (⁠ ¥/year) 225.83 772.00 0.62 IC Educational investment (⁠ ¥/year) 910.44 1,225.73 0.20 θH Height (cm) 137.33 19.30 0.13 Weight (kg) 33.60 11.82 0.16 BMI 17.39 3.22 0.27 General health status* 2.92 0.63 0.34 θC Literature (score: 1–100) 81.93 13.79 0.42 Literature (relative measure)† 3.53 0.84 0.48 Mathematics (score: 1–100) 80.90 16.41 0.43 Mathematics (relative measure)† 3.48 0.92 0.50 Good student awards (dummy) 0.24 0.43 0.51 Awards in contests (dummy) 0.07 0.25 0.49 Grade repetition (dummy) 0.04 0.21 0.52 Doing minor actions in class‡ 1.73 0.76 0.49 Always feel lonely§ 1.20 0.50 0.34 Easily distracted§ 1.59 0.68 0.34 Easily frightened§ 1.37 0.60 0.28 Emotionally unstable§ 1.12 0.35 0.28 T Paternal labour supply (days/month) 25.51 4.68 Maternal labour supply (days/month) 25.32 4.72 c Paternal consumption (⁠ ¥/six months) 700.33 869.38 Maternal consumption (⁠ ¥/six months) 283.81 736.59 ω Birthweight (kg) 2.46 0.47 0.36 ξ Male 0.49 0.50 0.50 Age 11.19 3.09 Born at the first parity 0.79 0.40 h Maternal age 36.85 4.84 Maternal ethnicity (Han = 1) 0.86 0.35 Maternal schooling years 8.65 3.28 w, pI Maternal working sector (Public = 1) 0.08 0.27 Rural 0.53 0.50 Y Household asset (score) −0.05 1.73 Notes ¥ stands for Chinese Yuan. The sample includes 1,456 pairs of twins. Column (5) presents the share of the within‐twin standard deviation out of the overall sample standard deviation. *4‐point Likert scale: 1 (worst) to 4 (best). †1 (top quintile in the class) to 5 (lowest quintile). ‡4‐point Likert scale: 1 (never) to 4 (always). §3‐point Likert scale: 1 (disagree), 2 (agree), 3 (strongly agree). Open in new tab Table 1 Descriptive Statistics Theoretical variables . Empirical counterparts . Mean . SD . Within‐twin SD/overall SD . (1) . (2) . (3) . (4) . (5) . eH Early health shocks (dummy) 0.09 0.28 0.35 IH Health investment (⁠ ¥/year) 225.83 772.00 0.62 IC Educational investment (⁠ ¥/year) 910.44 1,225.73 0.20 θH Height (cm) 137.33 19.30 0.13 Weight (kg) 33.60 11.82 0.16 BMI 17.39 3.22 0.27 General health status* 2.92 0.63 0.34 θC Literature (score: 1–100) 81.93 13.79 0.42 Literature (relative measure)† 3.53 0.84 0.48 Mathematics (score: 1–100) 80.90 16.41 0.43 Mathematics (relative measure)† 3.48 0.92 0.50 Good student awards (dummy) 0.24 0.43 0.51 Awards in contests (dummy) 0.07 0.25 0.49 Grade repetition (dummy) 0.04 0.21 0.52 Doing minor actions in class‡ 1.73 0.76 0.49 Always feel lonely§ 1.20 0.50 0.34 Easily distracted§ 1.59 0.68 0.34 Easily frightened§ 1.37 0.60 0.28 Emotionally unstable§ 1.12 0.35 0.28 T Paternal labour supply (days/month) 25.51 4.68 Maternal labour supply (days/month) 25.32 4.72 c Paternal consumption (⁠ ¥/six months) 700.33 869.38 Maternal consumption (⁠ ¥/six months) 283.81 736.59 ω Birthweight (kg) 2.46 0.47 0.36 ξ Male 0.49 0.50 0.50 Age 11.19 3.09 Born at the first parity 0.79 0.40 h Maternal age 36.85 4.84 Maternal ethnicity (Han = 1) 0.86 0.35 Maternal schooling years 8.65 3.28 w, pI Maternal working sector (Public = 1) 0.08 0.27 Rural 0.53 0.50 Y Household asset (score) −0.05 1.73 Theoretical variables . Empirical counterparts . Mean . SD . Within‐twin SD/overall SD . (1) . (2) . (3) . (4) . (5) . eH Early health shocks (dummy) 0.09 0.28 0.35 IH Health investment (⁠ ¥/year) 225.83 772.00 0.62 IC Educational investment (⁠ ¥/year) 910.44 1,225.73 0.20 θH Height (cm) 137.33 19.30 0.13 Weight (kg) 33.60 11.82 0.16 BMI 17.39 3.22 0.27 General health status* 2.92 0.63 0.34 θC Literature (score: 1–100) 81.93 13.79 0.42 Literature (relative measure)† 3.53 0.84 0.48 Mathematics (score: 1–100) 80.90 16.41 0.43 Mathematics (relative measure)† 3.48 0.92 0.50 Good student awards (dummy) 0.24 0.43 0.51 Awards in contests (dummy) 0.07 0.25 0.49 Grade repetition (dummy) 0.04 0.21 0.52 Doing minor actions in class‡ 1.73 0.76 0.49 Always feel lonely§ 1.20 0.50 0.34 Easily distracted§ 1.59 0.68 0.34 Easily frightened§ 1.37 0.60 0.28 Emotionally unstable§ 1.12 0.35 0.28 T Paternal labour supply (days/month) 25.51 4.68 Maternal labour supply (days/month) 25.32 4.72 c Paternal consumption (⁠ ¥/six months) 700.33 869.38 Maternal consumption (⁠ ¥/six months) 283.81 736.59 ω Birthweight (kg) 2.46 0.47 0.36 ξ Male 0.49 0.50 0.50 Age 11.19 3.09 Born at the first parity 0.79 0.40 h Maternal age 36.85 4.84 Maternal ethnicity (Han = 1) 0.86 0.35 Maternal schooling years 8.65 3.28 w, pI Maternal working sector (Public = 1) 0.08 0.27 Rural 0.53 0.50 Y Household asset (score) −0.05 1.73 Notes ¥ stands for Chinese Yuan. The sample includes 1,456 pairs of twins. Column (5) presents the share of the within‐twin standard deviation out of the overall sample standard deviation. *4‐point Likert scale: 1 (worst) to 4 (best). †1 (top quintile in the class) to 5 (lowest quintile). ‡4‐point Likert scale: 1 (never) to 4 (always). §3‐point Likert scale: 1 (disagree), 2 (agree), 3 (strongly agree). Open in new tab Our main dependent variables are measures of the family investments in children in the 12 months prior to the survey Ik ⁠. The investments are separately recorded for each child. Health investments include money spent on medical treatments and on the purchase of medicine or health products.7 Educational investments include school tuition and money spent on purchasing books and stationery, hiring home tutors and attending tutoring classes. We note that the medical and educational investments on children constitute a substantial fraction of the family income. Educational investments on one child alone amount to 912 yuan per year out of a per capita family income of 3,030 yuan per year. The CCTS has rich information measuring child human capital. As measures of child health θH ⁠, we use anthropometric indicators (i.e. height, weight and BMI) and general health status, which are all reported by both parents. We use child academic and schooling performance to measure child educational outcomes. As measures of academic performance (components of θC ⁠), we use both objective (examination transcripts) and subjective (self‐reported evaluations in comparison with the class norm) measures in two different subjects: literature and mathematics. They are compulsory courses from primary school to high school (from age 6 to 18). We also analyse several outcomes related to school performance, which are recorded from transcripts. They include good student awards, awards in contests, grade repetition and whether the child often does naughty actions in class as reported by teachers. Our data are also rich in terms of socio‐emotional measures, which are categorical and reported by both parents. We have four measures: always feels lonely, easily distracted, easily frightened and emotionally unstable. These variables are derived from the Strengths and Difficulties Questionnaire (SDQ) used by CCTS. The SDQ is one of the most commonly used instruments for screening child psychiatric morbidities. See Du et al. (2008) for the discussion on the reliability and validity on Asian children of SDQ. We also analyse the effect of early health shocks on parental labour supply (T) and consumption (c). Parental labour supply is measured as days worked per month. Parental consumption is measured as the total expenditure on cigarettes, alcohol, clothes and cosmetics in the past six months prior to the survey. Consumption is separately recorded for mothers and fathers. Birthweight is used to proxy child pre‐birth endowments (ω). This variable is used to measure both health and cognitive endowments. We have three variables for measuring child characteristics (ξ): age, gender and birth order.8 The variables of maternal age, ethnicity and schooling years are used to proxy parental characteristics (h). We use both the rural hukou and maternal working sector to proxy wages (w) and medical and educational prices (⁠ pI ⁠). The rural indicator is commonly used to proxy for wages in studies in developing countries because of the large wage gap between rural and urban areas (Johnson, 1947; Rosenzweig, 1980). We also use hukou to proxy the price of health services. At the time of the survey, the medical insurance system was almost completely absent in rural areas, whereas medical expenditures on children could be partly reimbursed for urban residents. Although public education is not free in both urban and rural areas at the time of the survey, the quality of education in urban areas is higher than that in rural areas. Note that Chinese residents find it difficult to change their hukou. The maternal working sector is a good variable proxying for prices on health and educational investments. Child medical treatment and education are usually subsidised by the government if mothers are working in the public sector. Moreover, job turnover from public to private sectors is rare for Chinese women. We use household assets as a proxy for non‐labour income (Y). ‘Household asset’ is a score generated by using principal component analysis (Kolenikov and Angeles, 2009). The durable goods used to generate the household asset scores include washing machines, refrigerators, air‐conditioners, shower heaters, water dispensers, sterilised cupboards, motorcycles, cars, radios/recorders, televisions, video recorders, video displayers, hi‐fi’s, cameras, telephones and mobile phones. Finally, column (5) of Table 1 shows substantial within‐twin‐pair variations in early health shocks, family investments and child outcomes. For example, the within‐twin standard deviations accounts for about 35% of the total sample standard deviations of child early health shocks. This ratio is as high as 62% for child health investments. 3. Our Econometric Model and Its Identification This Section presents our econometric model and a discussion of how we identify it. We first analyse how parents respond to early child health shocks. We linearise the optimal human capital investment (4) as a first‐order approximation and add a disturbance term (⁠ ϵi,τk ⁠), which is assumed to reflect measurement errors in the investment of type k specific to child i in family τ; and assume that children are treated symmetrically (so that statistically they are exchangeable): Ii,τk=α1kei,τH+α2kej,τH+α3kωi,τ+α4kωj,τ+α5kξi,τ+α6kξj,τ+α7kζτ+(μτ)+ϵi,τk.(7) The assumption of symmetry implies that the coefficients are the same across children. We normalise the coefficient on parental preferences (⁠ μτ ⁠) to be 1. ζτ is a vector of variables including the price for human capital investment (⁠ pI ⁠), the wage rate (w), non‐labour income (Y) and other observable parental characteristics, which is denoted as κ. We denote μ as the unobserved parental characteristics or preferences. Thus, h = (κ,μ). Both ζτ and μτ are shared by twin siblings. Unlike (4), we do not make any distinction between health and cognitive endowments because we have only one variable – birthweight – to measure prenatal endowment in our data set. Conditioning on the unobservable μτ ⁠, we further assume ϵi,τk to be i.i.d. The major problem in identifying the own effect (⁠ α1k ⁠) and cross effect (⁠ α2k ⁠) of an early health shock on family investment is that the early health shock may reflect unobserved parental preferences μτ ⁠. For example, on the one hand, parents who prefer child human capital may be more likely to report that their children have suffered from early health shocks even if their children did not. On the other hand, these parents may spend more on human capital investments. In this case, the least squares estimates of (7), ignoring unobserved parental characteristics or preferences, would be biased. If the cross‐sibling effects are symmetric and equal, we can eliminate this source of bias by the following within‐twin fixed‐effects (FE) estimator: ΔIτk=(α1k−α2k)ΔeτH+(α3k−α4k)Δωτ+(α5k−α6k)Δξτ+Δϵτk,(8) where Δ is an operator forming within‐twin differences. We test the symmetric regression assumption of cross‐sibling effects below and find that it is not rejected in our data. We are interested in the estimates of α1k−α2k in (8) which reflect parental investment strategy or the intra‐household resource allocation effect of human capital investment of type k. If parents reinforce investment of type k in response to an early health shock on child i, then α1k−α2k<0 ⁠; compensation implies that α1k−α2k>0 ⁠. The self and cross effects reflect the interaction between parental preference and production technology. Our theory predicts that parents could make compensating and reinforcing investments along different dimensions of human capital in response to an early health shock. Therefore, the signs of α1H−α2H and α1C−α2C are not necessarily the same. Our basic identifying assumption is that the within‐twin variation in the error term of (8) is uncorrelated with the within‐twin variation in early health shocks. This assumption may not necessarily hold. For example, the within‐twin difference in individual specific prenatal endowment might not be fully controlled for by Δω, leading to a correlation between Δe and Δε. If so, Δe would be endogenous in (8), and the OLS estimates of (8) would be biased.9 We measure early health shocks by incidence of serious diseases at ages 0–3 as discussed in the Section above. Diseases can either reflect a random shock which is consistent with the definition of early health shocks in the model, or be an indication of an individual‐specific health endowment. In other words, though early health shocks may or may not be exogenous in (7), what we need for identification is that the within‐twin variation in early health shocks is random and exogenous in (8). We propose and implement a test to examine the identifying assumption. We assume that the unobserved in health shocks are uniform across children within a family and that elimination of a family fixed effect eliminates any spurious correlation. A test of this assumption compares the OLS estimates of the coefficients of (7) for the sick and healthy child. The difference in the OLS estimates should accord with the fixed‐effect estimates assuming all other covariates are equally correlated with the health shocks. Specifically, under the null hypothesis that within‐twin variations in early health shocks are exogenous such that eιH and ε are uncorrelated in (7) after controlling for the unobservable μτ ⁠, we have: (i) plimα^1k=α1k+(σμ,eiH/σeiH2) and plimα^2k=α2k+(σμ,ejH/σejH2) in (7), where σμ,eιH is the covariance of μ (family fixed effects) and eιH (early health shock for child τ), and σeιH2 is the variance of eιH ⁠;10 (ii) σμ,eiH/σeiH2=σμ,ejH/σejH2 by symmetry; and (iii) plim(α1k−α2k)^=α1k−α2k in (8). Therefore, the null hypothesis of symmetry (really exchangeability) gives the cross‐equation restriction: plim(α^1k−α^2k)=plim(α1k−α2k)^,(9) where α^1k and α^2k are the OLS estimates of (7), and (α1k−α2k)^ are the fixed‐effects estimates of (8). Thus, we test differences of estimates obtained from OLS versus estimates obtained from a fixed‐effects procedure. If there are unobserved, individual‐specific prenatal endowments and eιH and ε are correlated in (7), the null hypothesis of symmetry and the equality in (9) would not hold.11 We test and do not reject this restriction in our empirical analysis reported below. We analyse the effect of early health shocks on child human capital. By linearising the production function (1) as a first‐order approximation and by adding a disturbance term that reflects measurement errors (⁠ vi,τ ⁠), which are individual‐specific, we specify the following regression equation: θi,τk=β1kei,τH+β2kωi,τ+β3kIi,τk+β4kξi,τ+β5kκτ+μτ+vi,τ,(10) where κ denotes observable parental characteristics. The cross‐sectional variation in early health shocks may reflect the unobservable parental characteristics. For example, better child‐rearing practices may lead to fewer early health shocks and, at the same time, more child human capital. To remove the possible bias induced by unobserved parental characteristics, we use the following fixed effect (FE) specification: Δθτk=β1kΔeτH+β2kΔIτk+β3kΔωτ+β4kΔξτ+Δvτ,(11) where β1k captures the biological effects corresponding to the first term on the right‐hand side of (5), which is expected to be negative; β2k measures the productivity effect of family investments, which is expected to be positive. Because family investment is a parental choice, we need to worry about simultaneous equations bias. We use 2SLS to estimate (11). Our theoretical analysis guides us to choose instrumental variables (IV). The price of investments (⁠ pI ⁠), wage rate (w) and non‐labour income (Y) in the family investment (4) are excluded from the production function (1). However, these variables drop out from the within‐twin differences of (11). We thus use pI ⁠, w and Y interacted with the within‐twin variation in child prenatal endowment and characteristics (Δω × Y, Δω×pI ⁠, Δω × h, Δξ × Y, Δξ×pI ⁠, and Δξ × h) as IVs for within‐twin variation in investments (⁠ ΔIk (k = H,C)) in (11). Specifically, we use two types of interaction terms as IVs for within‐twin differences in health or educational investments. The first type includes the interaction terms between the within‐twin difference in birthweight and the household and parental level variables; the second type includes the interaction terms between the within‐twin difference in gender and the household and parental‐level variables. The household and parental‐level variables include a rural indicator, maternal working sector, age, ethnicity and schooling years. Administrative data usually do not have information on family investments in children’s human capital. Thus, the recent literature in health economics does not estimate health production functions. Instead, the literature specifies a reduced‐form regression equation that ignores the intra‐household response such as: Δθτk=ϕ1kΔeτH+ϕ2kΔωτ+ϕ3kΔξτ+Δuτ.(12) The reduced‐form estimate of ϕ1k captures the total effect of an early health shock on child human capital, and corresponds to the left hand side of (5). When β2k≠0 and α1k−α2k≠0 ⁠, β1k differs from ϕ1k ⁠. The total effect deviates from the biological effect. To compare our results with those in the literature, we also perform reduced‐form estimation. By comparing β1k with ϕ1k ⁠, we can infer the importance of the intra‐household resource allocation effects by using (5). 4. Empirical Evidence 4.1. Child Early Health Shock and Family Investments Before presenting our estimation results of the investment equation, we first examine the determinants of early health shocks. The results are reported in Table 2. Column (1) reports the OLS estimates. We find that low birthweight is positively correlated with the probability of suffering early health shocks. We also observe that males are more likely to suffer. Results also show a positive correlation between maternal schooling and the probability of reporting children suffering from early health shock. We interpret this positive correlation as a reporting bias that is commonly found in he literature in the health economics (Strauss and Thomas, 1998). If the reporting bias is determined by parental observed and unobserved characteristics, the issue of reporting bias can be addressed by the within‐twin FE estimation because these parental characteristics are removed by within‐twin differences. The FE estimates in column (2) show that the occurrence of an early health shock is unrelated to birthweight. In column (3), we report a regression of the within‐twin difference in early health shocks on both within‐twin differences in birthweight and gender and other level covariates. We find that the within‐twin variations in early health shocks are uncorrelated with the level variables. Therefore, the results in Table 2 do not reject our identifying assumption of the randomness of within‐twin variation in early health shocks. Table 2 Determinants of Child Early Health Shocks . Dependent variable: early health shocks . . (1) . (2) . (3) . Birthweight: < 2 kg 0.044** 0.020 0.021 (0.020) (0.022) (0.022) Birthweight: 2–2.5 kg 0.008 −0.000 0.001 (0.016) (0.018) (0.018) Birthweight: 2.5–3 kg −0.012 −0.024 −0.022 (0.016) (0.015) (0.015) Male 0.040*** 0.020* 0.020* (0.010) (0.010) (0.010) Age −0.001 0.001 (0.002) (0.002) Born at the first parity 0.008 −0.007 (0.014) (0.014) Maternal age −0.002 −0.000 (0.001) (0.001) Maternal ethnicity (Han = 1) −0.014 0.013 (0.015) (0.015) Maternal schooling years 0.007*** −0.000 (0.002) (0.002) Maternal working sector (public = 1) 0.009 0.012 (0.022) (0.021) Rural −0.019 −0.014 (0.013) (0.013) Household asset −0.007* 0.004 (0.004) (0.004) R2 0.024 0.009 0.015 No. of pair of twins 1,456 1,456 1,456 . Dependent variable: early health shocks . . (1) . (2) . (3) . Birthweight: < 2 kg 0.044** 0.020 0.021 (0.020) (0.022) (0.022) Birthweight: 2–2.5 kg 0.008 −0.000 0.001 (0.016) (0.018) (0.018) Birthweight: 2.5–3 kg −0.012 −0.024 −0.022 (0.016) (0.015) (0.015) Male 0.040*** 0.020* 0.020* (0.010) (0.010) (0.010) Age −0.001 0.001 (0.002) (0.002) Born at the first parity 0.008 −0.007 (0.014) (0.014) Maternal age −0.002 −0.000 (0.001) (0.001) Maternal ethnicity (Han = 1) −0.014 0.013 (0.015) (0.015) Maternal schooling years 0.007*** −0.000 (0.002) (0.002) Maternal working sector (public = 1) 0.009 0.012 (0.022) (0.021) Rural −0.019 −0.014 (0.013) (0.013) Household asset −0.007* 0.004 (0.004) (0.004) R2 0.024 0.009 0.015 No. of pair of twins 1,456 1,456 1,456 Notes Columns (1) and (2) report the OLS and within‐twin fixed‐effects estimates, respectively. In column (3), we regress the within‐twin differences in early health shock on both within‐twin differences in birthweight and gender and other variables at the household level. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab Table 2 Determinants of Child Early Health Shocks . Dependent variable: early health shocks . . (1) . (2) . (3) . Birthweight: < 2 kg 0.044** 0.020 0.021 (0.020) (0.022) (0.022) Birthweight: 2–2.5 kg 0.008 −0.000 0.001 (0.016) (0.018) (0.018) Birthweight: 2.5–3 kg −0.012 −0.024 −0.022 (0.016) (0.015) (0.015) Male 0.040*** 0.020* 0.020* (0.010) (0.010) (0.010) Age −0.001 0.001 (0.002) (0.002) Born at the first parity 0.008 −0.007 (0.014) (0.014) Maternal age −0.002 −0.000 (0.001) (0.001) Maternal ethnicity (Han = 1) −0.014 0.013 (0.015) (0.015) Maternal schooling years 0.007*** −0.000 (0.002) (0.002) Maternal working sector (public = 1) 0.009 0.012 (0.022) (0.021) Rural −0.019 −0.014 (0.013) (0.013) Household asset −0.007* 0.004 (0.004) (0.004) R2 0.024 0.009 0.015 No. of pair of twins 1,456 1,456 1,456 . Dependent variable: early health shocks . . (1) . (2) . (3) . Birthweight: < 2 kg 0.044** 0.020 0.021 (0.020) (0.022) (0.022) Birthweight: 2–2.5 kg 0.008 −0.000 0.001 (0.016) (0.018) (0.018) Birthweight: 2.5–3 kg −0.012 −0.024 −0.022 (0.016) (0.015) (0.015) Male 0.040*** 0.020* 0.020* (0.010) (0.010) (0.010) Age −0.001 0.001 (0.002) (0.002) Born at the first parity 0.008 −0.007 (0.014) (0.014) Maternal age −0.002 −0.000 (0.001) (0.001) Maternal ethnicity (Han = 1) −0.014 0.013 (0.015) (0.015) Maternal schooling years 0.007*** −0.000 (0.002) (0.002) Maternal working sector (public = 1) 0.009 0.012 (0.022) (0.021) Rural −0.019 −0.014 (0.013) (0.013) Household asset −0.007* 0.004 (0.004) (0.004) R2 0.024 0.009 0.015 No. of pair of twins 1,456 1,456 1,456 Notes Columns (1) and (2) report the OLS and within‐twin fixed‐effects estimates, respectively. In column (3), we regress the within‐twin differences in early health shock on both within‐twin differences in birthweight and gender and other variables at the household level. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab We now turn to our main estimation results about child early health shocks and family investments in children. Column (1) in Table 3 reports the OLS estimates of (7) with respect to health investments. We find that the own effect of an early health shock on health investment is significantly positive, whereas the cross‐sibling effect is almost zero. We also find that being a male, being born at first parity, maternal schooling years and household asset are positively correlated with child health investments. By contrast, the variable of ‘born in rural areas’ is negatively correlated with child health investment. Table 3 Child Early Health Shocks and Parental Investment in Health . Dependent variable: . Health investment in child i (log) . Health investment in child j (log) . Difference in health investment . (1) . (2) . (3) . Early health shocks (i) 1.192*** −0.288 1.349*** (0.325) (0.312) (0.243) Early health shocks (j) 0.001 1.194*** (0.322) (0.309) Birthweight: < 2 kg (i) 0.113 −0.297 0.534*** (0.286) (0.275) (0.204) Birthweight: 2–2.5 kg (i) 0.237 −0.286 0.484*** (0.232) (0.223) (0.163) Birthweight: 2.5–3 kg (i) 0.248 −0.192 0.418*** (0.213) (0.204) (0.139) Birthweight: < 2 kg (j) 0.203 0.889*** (0.289) (0.277) Birthweight: 2–2.5 kg (j) 0.054 0.463** (0.227) (0.218) Birthweight: 2.5–3 kg (j) −0.073 0.317* (0.200) (0.192) Male (i) 0.291** 0.226* 0.071 (0.137) (0.132) (0.095) Male (j) 0.021 0.087 (0.137) (0.132) Age −0.041* −0.046** (0.024) (0.023) Born at the first parity 0.387** 0.361** (0.162) (0.155) Maternal age 0.007 0.003 (0.015) (0.015) Maternal ethnicity (Han = 1) 0.006 0.102 (0.173) (0.166) Maternal schooling years 0.083*** 0.114*** (0.024) (0.023) Maternal working sector (public = 1) −0.286 −0.378 (0.246) (0.237) Rural −0.298** 0.047 (0.145) (0.139) Household asset 0.124*** 0.067 (0.045) (0.043) χ2 18.87 0.14 p‐values 0.34 0.71 No. of pair of twins 1,456 1,456 1,456 . Dependent variable: . Health investment in child i (log) . Health investment in child j (log) . Difference in health investment . (1) . (2) . (3) . Early health shocks (i) 1.192*** −0.288 1.349*** (0.325) (0.312) (0.243) Early health shocks (j) 0.001 1.194*** (0.322) (0.309) Birthweight: < 2 kg (i) 0.113 −0.297 0.534*** (0.286) (0.275) (0.204) Birthweight: 2–2.5 kg (i) 0.237 −0.286 0.484*** (0.232) (0.223) (0.163) Birthweight: 2.5–3 kg (i) 0.248 −0.192 0.418*** (0.213) (0.204) (0.139) Birthweight: < 2 kg (j) 0.203 0.889*** (0.289) (0.277) Birthweight: 2–2.5 kg (j) 0.054 0.463** (0.227) (0.218) Birthweight: 2.5–3 kg (j) −0.073 0.317* (0.200) (0.192) Male (i) 0.291** 0.226* 0.071 (0.137) (0.132) (0.095) Male (j) 0.021 0.087 (0.137) (0.132) Age −0.041* −0.046** (0.024) (0.023) Born at the first parity 0.387** 0.361** (0.162) (0.155) Maternal age 0.007 0.003 (0.015) (0.015) Maternal ethnicity (Han = 1) 0.006 0.102 (0.173) (0.166) Maternal schooling years 0.083*** 0.114*** (0.024) (0.023) Maternal working sector (public = 1) −0.286 −0.378 (0.246) (0.237) Rural −0.298** 0.047 (0.145) (0.139) Household asset 0.124*** 0.067 (0.045) (0.043) χ2 18.87 0.14 p‐values 0.34 0.71 No. of pair of twins 1,456 1,456 1,456 Notes Columns (1) and (2) report the OLS estimates; column (3) reports the within‐twin fixed‐effect estimates. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab Table 3 Child Early Health Shocks and Parental Investment in Health . Dependent variable: . Health investment in child i (log) . Health investment in child j (log) . Difference in health investment . (1) . (2) . (3) . Early health shocks (i) 1.192*** −0.288 1.349*** (0.325) (0.312) (0.243) Early health shocks (j) 0.001 1.194*** (0.322) (0.309) Birthweight: < 2 kg (i) 0.113 −0.297 0.534*** (0.286) (0.275) (0.204) Birthweight: 2–2.5 kg (i) 0.237 −0.286 0.484*** (0.232) (0.223) (0.163) Birthweight: 2.5–3 kg (i) 0.248 −0.192 0.418*** (0.213) (0.204) (0.139) Birthweight: < 2 kg (j) 0.203 0.889*** (0.289) (0.277) Birthweight: 2–2.5 kg (j) 0.054 0.463** (0.227) (0.218) Birthweight: 2.5–3 kg (j) −0.073 0.317* (0.200) (0.192) Male (i) 0.291** 0.226* 0.071 (0.137) (0.132) (0.095) Male (j) 0.021 0.087 (0.137) (0.132) Age −0.041* −0.046** (0.024) (0.023) Born at the first parity 0.387** 0.361** (0.162) (0.155) Maternal age 0.007 0.003 (0.015) (0.015) Maternal ethnicity (Han = 1) 0.006 0.102 (0.173) (0.166) Maternal schooling years 0.083*** 0.114*** (0.024) (0.023) Maternal working sector (public = 1) −0.286 −0.378 (0.246) (0.237) Rural −0.298** 0.047 (0.145) (0.139) Household asset 0.124*** 0.067 (0.045) (0.043) χ2 18.87 0.14 p‐values 0.34 0.71 No. of pair of twins 1,456 1,456 1,456 . Dependent variable: . Health investment in child i (log) . Health investment in child j (log) . Difference in health investment . (1) . (2) . (3) . Early health shocks (i) 1.192*** −0.288 1.349*** (0.325) (0.312) (0.243) Early health shocks (j) 0.001 1.194*** (0.322) (0.309) Birthweight: < 2 kg (i) 0.113 −0.297 0.534*** (0.286) (0.275) (0.204) Birthweight: 2–2.5 kg (i) 0.237 −0.286 0.484*** (0.232) (0.223) (0.163) Birthweight: 2.5–3 kg (i) 0.248 −0.192 0.418*** (0.213) (0.204) (0.139) Birthweight: < 2 kg (j) 0.203 0.889*** (0.289) (0.277) Birthweight: 2–2.5 kg (j) 0.054 0.463** (0.227) (0.218) Birthweight: 2.5–3 kg (j) −0.073 0.317* (0.200) (0.192) Male (i) 0.291** 0.226* 0.071 (0.137) (0.132) (0.095) Male (j) 0.021 0.087 (0.137) (0.132) Age −0.041* −0.046** (0.024) (0.023) Born at the first parity 0.387** 0.361** (0.162) (0.155) Maternal age 0.007 0.003 (0.015) (0.015) Maternal ethnicity (Han = 1) 0.006 0.102 (0.173) (0.166) Maternal schooling years 0.083*** 0.114*** (0.024) (0.023) Maternal working sector (public = 1) −0.286 −0.378 (0.246) (0.237) Rural −0.298** 0.047 (0.145) (0.139) Household asset 0.124*** 0.067 (0.045) (0.043) χ2 18.87 0.14 p‐values 0.34 0.71 No. of pair of twins 1,456 1,456 1,456 Notes Columns (1) and (2) report the OLS estimates; column (3) reports the within‐twin fixed‐effect estimates. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab To test the symmetry assumption of cross‐sibling effects, we use the same sample as in column (1) but employ the family health investment in child j as a dependent variable. The results are reported in column (2). We then conduct a Wald test. The χ2 statistic is 18.87 and the p‐value is 0.34. These findings indicate that we cannot reject the symmetry assumption. Therefore, we conduct an FE estimation of (8) with respect to health investments. The results are reported in column (3). On the basis of these estimates, we find that the gap in health expenditures on average increases by 305 yuan (1.39 × 225) in favour of the sick twin child, which amounts to more than one third of the average family investment in child education per year. To test the null hypothesis that within‐twin variations in early health shocks are exogenous such that Δe and Δε are uncorrelated in (8), we conduct a Wald test on (9). If any individual specific component is omitted from (8) such that Δe and Δε are correlated, within‐twin variations in early health shocks would be endogenous. Thus, the equality in (9) would break down. We report the test result at the base of column (3). The χ2 statistic is 0.14, and the p‐value is 0.71. Therefore, the null hypothesis is not rejected. Table 4 presents the estimates of child early health shocks and family educational investment. Column (1) reports the ordinary least square (OLS) estimates of (7) with respect to educational investments. In contrast to the estimates with health investments (column 1 in Table 3), we find that the own effect of an early health shock on educational investment is not statistically significant, although the estimate is negative. In contrast, we find that the cross‐sibling effect is positive. The other covariates, namely, child age, maternal age, maternal schooling years and household asset are significantly positively correlated with child educational investments, whereas the covariate ‘born in rural areas’ is negatively correlated with child educational investment. Table 4 Child Early Health Shocks and Parental Investment in Education . Dependent variables: . Education investment in child i (log) . Education investment in child j (log) . Difference in education investment . (1) . (2) . (3) . Early health shocks (i) −0.142 0.065 −0.204*** (0.131) (0.124) (0.047) Early health shocks (j) 0.213 0.008 (0.130) (0.123) Birthweight: < 2 kg (i) 0.012 0.059 −0.015 (0.115) (0.110) (0.039) Birthweight: 2–2.5 kg (i) 0.131 0.123 0.016 (0.094) (0.089) (0.031) Birthweight: 2.5–3 kg (i) 0.007 0.031 −0.013 (0.086) (0.081) (0.027) Birthweight: <2 kg (j) −0.143 −0.127 (0.117) (0.111) Birthweight: 2–2.5 kg (j) −0.060 −0.045 (0.091) (0.087) Birthweight: 2.5–3 kg (j) −0.098 −0.103 (0.081) (0.077) Male (i) −0.042 −0.014 −0.024 (0.055) (0.053) (0.018) Male (j) 0.027 0.008 (0.055) (0.053) Age 0.083*** 0.088*** (0.010) (0.009) Born at the first parity 0.042 0.041 (0.065) (0.062) Maternal age 0.014** 0.014** (0.006) (0.006) Maternal ethnicity (Han = 1) 0.090 0.111* (0.070) (0.066) Maternal schooling years 0.038*** 0.041*** (0.010) (0.009) Maternal working sector (public = 1) 0.083 0.024 (0.099) (0.094) Rural −0.150** −0.184*** (0.058) (0.055) Household asset 0.130*** 0.124*** (0.018) (0.017) χ2 19.39 0.70 p‐values 0.31 0.41 No. of pair of twins 1,456 1,456 1,456 . Dependent variables: . Education investment in child i (log) . Education investment in child j (log) . Difference in education investment . (1) . (2) . (3) . Early health shocks (i) −0.142 0.065 −0.204*** (0.131) (0.124) (0.047) Early health shocks (j) 0.213 0.008 (0.130) (0.123) Birthweight: < 2 kg (i) 0.012 0.059 −0.015 (0.115) (0.110) (0.039) Birthweight: 2–2.5 kg (i) 0.131 0.123 0.016 (0.094) (0.089) (0.031) Birthweight: 2.5–3 kg (i) 0.007 0.031 −0.013 (0.086) (0.081) (0.027) Birthweight: <2 kg (j) −0.143 −0.127 (0.117) (0.111) Birthweight: 2–2.5 kg (j) −0.060 −0.045 (0.091) (0.087) Birthweight: 2.5–3 kg (j) −0.098 −0.103 (0.081) (0.077) Male (i) −0.042 −0.014 −0.024 (0.055) (0.053) (0.018) Male (j) 0.027 0.008 (0.055) (0.053) Age 0.083*** 0.088*** (0.010) (0.009) Born at the first parity 0.042 0.041 (0.065) (0.062) Maternal age 0.014** 0.014** (0.006) (0.006) Maternal ethnicity (Han = 1) 0.090 0.111* (0.070) (0.066) Maternal schooling years 0.038*** 0.041*** (0.010) (0.009) Maternal working sector (public = 1) 0.083 0.024 (0.099) (0.094) Rural −0.150** −0.184*** (0.058) (0.055) Household asset 0.130*** 0.124*** (0.018) (0.017) χ2 19.39 0.70 p‐values 0.31 0.41 No. of pair of twins 1,456 1,456 1,456 Notes Columns (1) and (2) report the OLS estimates; column (3) reports the within‐twin fixed‐effect estimates. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab Table 4 Child Early Health Shocks and Parental Investment in Education . Dependent variables: . Education investment in child i (log) . Education investment in child j (log) . Difference in education investment . (1) . (2) . (3) . Early health shocks (i) −0.142 0.065 −0.204*** (0.131) (0.124) (0.047) Early health shocks (j) 0.213 0.008 (0.130) (0.123) Birthweight: < 2 kg (i) 0.012 0.059 −0.015 (0.115) (0.110) (0.039) Birthweight: 2–2.5 kg (i) 0.131 0.123 0.016 (0.094) (0.089) (0.031) Birthweight: 2.5–3 kg (i) 0.007 0.031 −0.013 (0.086) (0.081) (0.027) Birthweight: <2 kg (j) −0.143 −0.127 (0.117) (0.111) Birthweight: 2–2.5 kg (j) −0.060 −0.045 (0.091) (0.087) Birthweight: 2.5–3 kg (j) −0.098 −0.103 (0.081) (0.077) Male (i) −0.042 −0.014 −0.024 (0.055) (0.053) (0.018) Male (j) 0.027 0.008 (0.055) (0.053) Age 0.083*** 0.088*** (0.010) (0.009) Born at the first parity 0.042 0.041 (0.065) (0.062) Maternal age 0.014** 0.014** (0.006) (0.006) Maternal ethnicity (Han = 1) 0.090 0.111* (0.070) (0.066) Maternal schooling years 0.038*** 0.041*** (0.010) (0.009) Maternal working sector (public = 1) 0.083 0.024 (0.099) (0.094) Rural −0.150** −0.184*** (0.058) (0.055) Household asset 0.130*** 0.124*** (0.018) (0.017) χ2 19.39 0.70 p‐values 0.31 0.41 No. of pair of twins 1,456 1,456 1,456 . Dependent variables: . Education investment in child i (log) . Education investment in child j (log) . Difference in education investment . (1) . (2) . (3) . Early health shocks (i) −0.142 0.065 −0.204*** (0.131) (0.124) (0.047) Early health shocks (j) 0.213 0.008 (0.130) (0.123) Birthweight: < 2 kg (i) 0.012 0.059 −0.015 (0.115) (0.110) (0.039) Birthweight: 2–2.5 kg (i) 0.131 0.123 0.016 (0.094) (0.089) (0.031) Birthweight: 2.5–3 kg (i) 0.007 0.031 −0.013 (0.086) (0.081) (0.027) Birthweight: <2 kg (j) −0.143 −0.127 (0.117) (0.111) Birthweight: 2–2.5 kg (j) −0.060 −0.045 (0.091) (0.087) Birthweight: 2.5–3 kg (j) −0.098 −0.103 (0.081) (0.077) Male (i) −0.042 −0.014 −0.024 (0.055) (0.053) (0.018) Male (j) 0.027 0.008 (0.055) (0.053) Age 0.083*** 0.088*** (0.010) (0.009) Born at the first parity 0.042 0.041 (0.065) (0.062) Maternal age 0.014** 0.014** (0.006) (0.006) Maternal ethnicity (Han = 1) 0.090 0.111* (0.070) (0.066) Maternal schooling years 0.038*** 0.041*** (0.010) (0.009) Maternal working sector (public = 1) 0.083 0.024 (0.099) (0.094) Rural −0.150** −0.184*** (0.058) (0.055) Household asset 0.130*** 0.124*** (0.018) (0.017) χ2 19.39 0.70 p‐values 0.31 0.41 No. of pair of twins 1,456 1,456 1,456 Notes Columns (1) and (2) report the OLS estimates; column (3) reports the within‐twin fixed‐effect estimates. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab The result of testing the symmetry assumption of cross‐sibling effects is reported at the base of column (2). The χ2 statistic is 19.39 with a p‐value of 0.31. We cannot reject the symmetry assumption. Therefore, we conduct the FE estimation of (8) with respect to educational investments. The results are reported in column (3). We find that, in contrast to the estimates with health investment, the gap in educational expenditures increases by 182 yuan (0.2 × 910), on average, in favour of the healthy child. The χ2 statistic of testing the cross‐equation restriction (9) is 0.70, and the p‐value is 0.41. We cannot reject the null hypothesis that no endogenous within‐twin variation exists in early health shock. Summarising Tables 3 and 4, our results indicate that parents adopt a compensating strategy with respect to health investment and a reinforcing strategy with respect to educational investment in response to an early health shock which affects one of the twin children. We also estimate the family investment equation by different subsamples based on hukou status, maternal education, household wealth and gender composition of twin children. We find significant differences in the compensating and reinforcing patterns across subsamples. First, the increase in health expenditures in favour of the sick twin in rural areas is not accompanied by a corresponding decrease in educational expenditures. In urban areas, instead, the fall in the amount of educational resources on the sick child almost exactly offsets, in monetary terms, the amount redistributed to pay for the medical expense. Second, both the compensating health investment and the reinforcing education investment are more precisely determined when mothers have a higher education level. Third, there is no significant difference in the compensating health investment behaviour between poor and rich households. In contrast, the reinforcing education investment behaviour is more significant in rich households than that in poor households. Finally, we find significant differences by gender. The compensating health investment and the reinforcing education investment are more significant in the female twin than male twin samples. The results are reported and discussed in online Appendix D. Our results have important implications. First, the results are consistent with our two major observations in the theoretical analysis on the intra‐household resource allocation. The reinforcement or compensatory child human capital investment strategy reflects not only parental preferences but also production technology. Furthermore, parents can compensate and reinforce along different dimensions of human capital with respect to an early health shock on one child, which helps us reconcile the seemingly conflicting findings in the literature. Second, the results deepen our understanding of the role of family investment in the overall level of inequality in a society. Our estimates indicate that intra‐household resource reallocation in child investment is not trivial. The gap in educational investment between sick and healthy children accounts for up to one‐fifth of the average educational investment per person. The gap in health investment is even larger. Therefore, the family plays an important role in accounting for the difference in investment in children. However, the role of the family in this case is complicated. On the one hand, parents increase the gap in educational investment by allocating more resources to the child suffering from an early health shock. In this regard, the family increases the overall level of inequality in the economy. On the other hand, parents decrease the gap in health investment by allocating more resource on the sick child. Thus, in terms of health investment, the family decreases inequality. If we focus on educational investment, the role of the family as an inequality mitigator will be understated. Finally, our empirical results clarify the interpretation of the recent reduced‐form estimates on early‐life conditions and late‐life outcomes. When parents make compensating and reinforcing investments along different dimensions of human capital, these reduced‐form estimates cannot be unambiguously interpreted as upper or lower‐bounds on the biological effects. Our estimates on intra‐household resource allocation suggest that the reduced‐form estimates underestimate the biological effect of an early health shock on health but overestimate the biological effect on education. To verify this prediction empirically, we estimate the child human capital production function below. 4.2. Early Health Shocks and Child Human Capital 4.2.1. Child health We next examine the effects of early health shocks on child human capital by estimating production function (11). Health investment is an endogenous variable in the child human capital equation. As discussed above, we use a 2SLS estimator. Guided by our theoretical model, we use Δω × Y, Δω×pI ⁠, Δω × h, Δξ × Y, Δξ×pI and Δξ × h as the IVs for ΔIk (k = H,C) in (11). Specifically, the IVs include the interaction terms between the within‐twin variations in birthweights and gender and the level variables, which include a rural indicator, maternal working sector, age, ethnicity and schooling. The results in Table 2 show that these level variables are uncorrelated with the within‐twin variation in early health shocks. Panel (a) in Table 5 reports the 2SLS estimates of the child health production function.12 Conditional on health investments, the estimate of early health shocks captures the biological effect. We find a long‐lasting negative biological effect of early health shocks on the child’s later health status. The estimates are statistically significant at a high level of 1% for three out of four measures. We also find that the productivity effects of the health investment are consistently positive. The estimates are statistically significant at the 5% level for current weight and BMI. Table 5 Early Health Shocks and Child Health . Dependent variables: . . Height . Weight . BMI . Health status . . z‐score . z‐score . z‐score . . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −0.100 −0.422*** −0.395*** −0.513*** (0.130) (0.118) (0.151) (0.078) Health investments† 0.070 0.118** 0.160** 0.047 (0.064) (0.059) (0.077) (0.039) Panel (b): reduced‐form estimates Early health shocks −0.004 −0.263*** −0.201* −0.449*** (0.096) (0.086) (0.113) (0.057) No. of pair of twins 1,418 1,430 1,408 1,450 . Dependent variables: . . Height . Weight . BMI . Health status . . z‐score . z‐score . z‐score . . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −0.100 −0.422*** −0.395*** −0.513*** (0.130) (0.118) (0.151) (0.078) Health investments† 0.070 0.118** 0.160** 0.047 (0.064) (0.059) (0.077) (0.039) Panel (b): reduced‐form estimates Early health shocks −0.004 −0.263*** −0.201* −0.449*** (0.096) (0.086) (0.113) (0.057) No. of pair of twins 1,418 1,430 1,408 1,450 Notes Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Birthweight and child gender are controlled for in each regression. †Endogenous variable. The instrumental variables include two types of interaction terms. The first type includes the interaction terms between the within‐twin difference in birthweight and the household and parental level variables, and the second type includes the interaction terms between the within‐twin difference in gender and the level variables. The household and parental level variables include a rural indicator, maternal working sector, age, ethnicity and schooling years. Open in new tab Table 5 Early Health Shocks and Child Health . Dependent variables: . . Height . Weight . BMI . Health status . . z‐score . z‐score . z‐score . . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −0.100 −0.422*** −0.395*** −0.513*** (0.130) (0.118) (0.151) (0.078) Health investments† 0.070 0.118** 0.160** 0.047 (0.064) (0.059) (0.077) (0.039) Panel (b): reduced‐form estimates Early health shocks −0.004 −0.263*** −0.201* −0.449*** (0.096) (0.086) (0.113) (0.057) No. of pair of twins 1,418 1,430 1,408 1,450 . Dependent variables: . . Height . Weight . BMI . Health status . . z‐score . z‐score . z‐score . . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −0.100 −0.422*** −0.395*** −0.513*** (0.130) (0.118) (0.151) (0.078) Health investments† 0.070 0.118** 0.160** 0.047 (0.064) (0.059) (0.077) (0.039) Panel (b): reduced‐form estimates Early health shocks −0.004 −0.263*** −0.201* −0.449*** (0.096) (0.086) (0.113) (0.057) No. of pair of twins 1,418 1,430 1,408 1,450 Notes Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Birthweight and child gender are controlled for in each regression. †Endogenous variable. The instrumental variables include two types of interaction terms. The first type includes the interaction terms between the within‐twin difference in birthweight and the household and parental level variables, and the second type includes the interaction terms between the within‐twin difference in gender and the level variables. The household and parental level variables include a rural indicator, maternal working sector, age, ethnicity and schooling years. Open in new tab To compare our results with those from the recent literature in health economics and to qualitatively gauge the importance of intra‐household resource allocation effects, we also estimate the reduced‐form of (12). Table 3 shows that parents adopt a compensatory strategy in health investments, and the intra‐household resource allocation effect is positive. Panel (a) of Table 5 shows a significantly positive productivity effect of health investment. By using the formula of (5), we expect that the reduced‐form estimates understate the biological effect of early health shock on later health status. This prediction is confirmed by the reduced‐form estimates, which are reported in panel (b) of Table 5. The reduced‐form estimates are also consistently negative, indicating that the direct biological effects, which are negative, outweigh the positive intra‐household resource allocation effects. We find that the reduced‐form estimates substantially underestimate the biological effects. Taking the dependent variable of BMI as an example (column 3), the reduced‐form estimate (−0.20) accounts for one half of the biological effect (−0.40). Almost the same proportion of the negative biological effect (−0.42) is accounted for by the reduced‐form estimate (−0.26) with respect to weight (column 2). The results have important implications, suggesting that although the negative effect of an early health shock may persist throughout the life cycle of children, remediation is possible. In other words, the negative effects can be partly offset by compensating investments within the household. 4.2.2. Child education and socio‐emotional skills We next examine the effects of an early health shock on child education by estimating the child education production function (11). The same set of variables are used as IVs for educational investment as discussed above. Panel (a) in Table 6 reports the 2SLS estimates of early health shocks on child educational achievements, both perceived and actual. We find that the twin child affected by an early health sock has poorer academic achievement compared with the healthy child. The productivity effects of educational investments on academic achievements are consistently positive across the four measures but are generally imprecisely estimated. We also conduct a 2SLS estimation of the effect of early health shocks on child schooling performance. The results are reported in panel (c) of the Table, which shows that an early health shock negatively affects the child’s schooling performance. We further observe that educational investments exert a positive productivity effect on the child’s schooling performance. Table 6 Early Health Shocks and Child Education . Dependent variables: . . Literature . Mathematics . . Score . Relative measure . Score . Relative measure . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −3.990* −0.168 −4.697* −0.496*** (2.045) (0.145) (2.432) (0.157) Educational investments† 6.124 0.904** 3.598 0.170 (6.313) (0.426) (7.459) (0.466) Panel (b): reduced‐form estimates Early health shocks −5.142*** −0.352*** −5.372*** −0.531*** (1.665) (0.110) (1.996) (0.127) No. of pair of twins 1,355 1,426 1,332 1,420 . Dependent variables: . . Literature . Mathematics . . Score . Relative measure . Score . Relative measure . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −3.990* −0.168 −4.697* −0.496*** (2.045) (0.145) (2.432) (0.157) Educational investments† 6.124 0.904** 3.598 0.170 (6.313) (0.426) (7.459) (0.466) Panel (b): reduced‐form estimates Early health shocks −5.142*** −0.352*** −5.372*** −0.531*** (1.665) (0.110) (1.996) (0.127) No. of pair of twins 1,355 1,426 1,332 1,420 . Dependent variables: . . Good student awards . Awards in contests . Grade repetition . Doing minor actions in class . . (5) . (6) . (7) . (8) . Panel (c): 2SLS estimates Early health shocks −0.199*** −0.067 0.025 0.296** (0.072) (0.042) (0.038) (0.121) Educational investments† 0.075 0.103 −0.235** −0.639* (0.216) (0.126) (0.113) (0.387) Panel (d): reduced‐form estimates Early health shocks −0.215*** −0.088*** 0.073** 0.396*** (0.058) (0.033) (0.029) (0.101) No. of pair of twins 1,456 1,456 1,456 1,440 . Dependent variables: . . Good student awards . Awards in contests . Grade repetition . Doing minor actions in class . . (5) . (6) . (7) . (8) . Panel (c): 2SLS estimates Early health shocks −0.199*** −0.067 0.025 0.296** (0.072) (0.042) (0.038) (0.121) Educational investments† 0.075 0.103 −0.235** −0.639* (0.216) (0.126) (0.113) (0.387) Panel (d): reduced‐form estimates Early health shocks −0.215*** −0.088*** 0.073** 0.396*** (0.058) (0.033) (0.029) (0.101) No. of pair of twins 1,456 1,456 1,456 1,440 Notes Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Birthweight and child gender are controlled for in each regression. †Endogenous variable. The instrumental variables include two types of interaction terms. The first type includes the interaction terms between the within‐twin difference in birthweight and the household and parental‐level variables; the second type includes the interaction terms between the within‐twin difference in gender and the level variables. The household and parental level variables include a rural indicator, maternal working sector, age, ethnicity and schooling years. Open in new tab Table 6 Early Health Shocks and Child Education . Dependent variables: . . Literature . Mathematics . . Score . Relative measure . Score . Relative measure . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −3.990* −0.168 −4.697* −0.496*** (2.045) (0.145) (2.432) (0.157) Educational investments† 6.124 0.904** 3.598 0.170 (6.313) (0.426) (7.459) (0.466) Panel (b): reduced‐form estimates Early health shocks −5.142*** −0.352*** −5.372*** −0.531*** (1.665) (0.110) (1.996) (0.127) No. of pair of twins 1,355 1,426 1,332 1,420 . Dependent variables: . . Literature . Mathematics . . Score . Relative measure . Score . Relative measure . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks −3.990* −0.168 −4.697* −0.496*** (2.045) (0.145) (2.432) (0.157) Educational investments† 6.124 0.904** 3.598 0.170 (6.313) (0.426) (7.459) (0.466) Panel (b): reduced‐form estimates Early health shocks −5.142*** −0.352*** −5.372*** −0.531*** (1.665) (0.110) (1.996) (0.127) No. of pair of twins 1,355 1,426 1,332 1,420 . Dependent variables: . . Good student awards . Awards in contests . Grade repetition . Doing minor actions in class . . (5) . (6) . (7) . (8) . Panel (c): 2SLS estimates Early health shocks −0.199*** −0.067 0.025 0.296** (0.072) (0.042) (0.038) (0.121) Educational investments† 0.075 0.103 −0.235** −0.639* (0.216) (0.126) (0.113) (0.387) Panel (d): reduced‐form estimates Early health shocks −0.215*** −0.088*** 0.073** 0.396*** (0.058) (0.033) (0.029) (0.101) No. of pair of twins 1,456 1,456 1,456 1,440 . Dependent variables: . . Good student awards . Awards in contests . Grade repetition . Doing minor actions in class . . (5) . (6) . (7) . (8) . Panel (c): 2SLS estimates Early health shocks −0.199*** −0.067 0.025 0.296** (0.072) (0.042) (0.038) (0.121) Educational investments† 0.075 0.103 −0.235** −0.639* (0.216) (0.126) (0.113) (0.387) Panel (d): reduced‐form estimates Early health shocks −0.215*** −0.088*** 0.073** 0.396*** (0.058) (0.033) (0.029) (0.101) No. of pair of twins 1,456 1,456 1,456 1,440 Notes Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Birthweight and child gender are controlled for in each regression. †Endogenous variable. The instrumental variables include two types of interaction terms. The first type includes the interaction terms between the within‐twin difference in birthweight and the household and parental‐level variables; the second type includes the interaction terms between the within‐twin difference in gender and the level variables. The household and parental level variables include a rural indicator, maternal working sector, age, ethnicity and schooling years. Open in new tab The reduced‐form estimates are reported in panels (b) and (d). We find that the reduced‐form estimates are consistently larger than the 2SLS estimates in terms of absolute values. The result suggests that the reduced‐form estimates overstate the negative biological effect of early health shocks on child education. By comparing the 2SLS estimates with the reduced‐form estimates, we find that the biological effects constitute a major part of the total effect for most measures of child educational outcomes. The result suggests a strong cross‐productivity effect of health shocks on education, broadly consistent with Cunha et al. (2010). The intra‐household resource allocation effect has also played an important role. Take the transcript recorded score of literature as an example (column 1), the intra‐household resource allocation effect accounts for about one‐third of the total negative effect of an early health shock. With regard to the effect of early health shocks on child socio‐emotional skills, panel (a) in Table 7 reports the 2SLS estimates. The importance of these skills in determining an individual’s income and other measures of well‐being has been increasingly recognised by economists (Borghans et al., 2008). We find that the twin child who suffered from an early health shock at age 0–3 has inferior personality traits. When we use the SDQ to measure the child’s socio‐emotional skills, the estimates show that children who experienced an early health shock are more likely to feel lonely, be easily distracted, easily frightened and be emotionally unstable. Although the estimates of the productivity of educational investment are consistently negative, the estimates are only statistically significant in column (3) with the measure of ‘being easily frightened’. The results suggest that educational investment may not be an important determinant of the development of socio‐emotional skills.13 Panel (b) reports the reduced‐form estimates. By comparing the reduced‐form estimates with the 2SLS estimates, we find that biological effects constitute a major part of the total effects except for the measure of being easily frightened (column 3). Table 7 Early Health Shocks and Child Socio‐economic Skills . Dependent variables: . . Feel lonely . Easilydistracted . Easily frightened . Emotionally unstable . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks 0.132*** 0.121** 0.066 0.085*** (0.041) (0.056) (0.046) (0.024) Educational investments† −0.158 −0.150 −0.383*** −0.113 (0.123) (0.166) (0.139) (0.073) Panel (b): Reduced‐form estimates Early health shocks 0.165*** 0.151*** 0.144*** 0.108*** (0.032) (0.044) (0.033) (0.019) No. of pair of twins 1,456 1,456 1,456 1,456 . Dependent variables: . . Feel lonely . Easilydistracted . Easily frightened . Emotionally unstable . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks 0.132*** 0.121** 0.066 0.085*** (0.041) (0.056) (0.046) (0.024) Educational investments† −0.158 −0.150 −0.383*** −0.113 (0.123) (0.166) (0.139) (0.073) Panel (b): Reduced‐form estimates Early health shocks 0.165*** 0.151*** 0.144*** 0.108*** (0.032) (0.044) (0.033) (0.019) No. of pair of twins 1,456 1,456 1,456 1,456 Notes Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Birthweight and child gender are controlled for in each regression. †Endogenous variable. The instrumental variables include two types of interaction terms. The first type includes the interaction terms between the within‐twin difference in birthweight and the household and parental‐level variables; the second type includes the interaction terms between the within‐twin difference in gender and the level variables. The household and parental level variables include a rural indicator, maternal working sector, age, ethnicity and schooling years. Open in new tab Table 7 Early Health Shocks and Child Socio‐economic Skills . Dependent variables: . . Feel lonely . Easilydistracted . Easily frightened . Emotionally unstable . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks 0.132*** 0.121** 0.066 0.085*** (0.041) (0.056) (0.046) (0.024) Educational investments† −0.158 −0.150 −0.383*** −0.113 (0.123) (0.166) (0.139) (0.073) Panel (b): Reduced‐form estimates Early health shocks 0.165*** 0.151*** 0.144*** 0.108*** (0.032) (0.044) (0.033) (0.019) No. of pair of twins 1,456 1,456 1,456 1,456 . Dependent variables: . . Feel lonely . Easilydistracted . Easily frightened . Emotionally unstable . . (1) . (2) . (3) . (4) . Panel (a): 2SLS estimates Early health shocks 0.132*** 0.121** 0.066 0.085*** (0.041) (0.056) (0.046) (0.024) Educational investments† −0.158 −0.150 −0.383*** −0.113 (0.123) (0.166) (0.139) (0.073) Panel (b): Reduced‐form estimates Early health shocks 0.165*** 0.151*** 0.144*** 0.108*** (0.032) (0.044) (0.033) (0.019) No. of pair of twins 1,456 1,456 1,456 1,456 Notes Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Birthweight and child gender are controlled for in each regression. †Endogenous variable. The instrumental variables include two types of interaction terms. The first type includes the interaction terms between the within‐twin difference in birthweight and the household and parental‐level variables; the second type includes the interaction terms between the within‐twin difference in gender and the level variables. The household and parental level variables include a rural indicator, maternal working sector, age, ethnicity and schooling years. Open in new tab 4.3. Child Early Health Shock and Parental Labour Supply and Consumption Finally, we investigate how an early health shock on one child affects parental labour supply and consumption. We specify the following regression equation: yτ=φ1d+φ2ω¯τ+φ3ξτ+ζτφ4+υτ,(13) where yτ measures parental labour supply or consumption in household τ; d is a dummy variable indicating whether the household has only one twin child who suffered from early health shock; ω¯ is the average birthweight of the twin children. Equation (13) is a linear approximation of the optimal parental labour supply or consumption function (6) with slight modifications. First, we estimate (13) for mothers and fathers separately. We use the mean of birthweights to measure child prenatal endowments. Child characteristics are the same between twin siblings except for gender. We use two dummy variables to measure the gender composition. The first variable indicates that both children are boys, and the other variable indicates that both are girls. Second, given that within‐twin variation in early health shocks is uncorrelated with unobservable characteristics, which is tested above (Table 2), we add d in the regression equation. Thus, φ1 gives a causal interpretation even if we ignore the unobservable parental characteristics when estimating (13). Finally, the added disturbance term υτ reflects measurement errors. The estimation results are reported in Table 8. We find that in households with only one twin child who suffered from an early health shock, the father is significantly less likely to spend money on goods for himself, and the mother is significantly more likely to work. Therefore, if we take other family members except the twin children into account, our results imply that the within‐twin FE estimates of child outcomes understate the overall negative effect of an early health shock in a family. Table 8 Child Early Health Shocks and Parental Labour Supply and Consumption . Dependent variables: . . Labour supply . Consumption . . Father . Mother . Father . Mother . . (1) . (2) . (3) . (4) . Early health shocks −0.048 0.054** −128.808* 27.751 (0.078) (0.024) (77.978) (73.685) Child birthweight (mean) 0.015 0.002 77.850* 27.692 (0.020) (0.014) (44.919) (30.173) Child age −0.000 0.005 −8.672 −9.728 (0.004) (0.005) (7.799) (7.860) Male twins 0.005 −0.017 −60.571 −22.393 (0.023) (0.021) (54.827) (28.318) Female twins −0.023 −0.034 −28.210 42.148 (0.022) (0.021) (57.334) (38.050) Born at the first parity −0.003 −0.049** −15.817 4.098 (0.026) (0.023) (43.038) (30.684) Age −0.003 −0.005 −13.630*** −5.438** (0.002) (0.004) (3.359) (2.629) Ethnicity (Han = 1) −0.028* −0.030* −47.481 −127.626 (0.016) (0.016) (59.532) (97.041) Schooling years −0.007 0.001 0.218 29.564* (0.005) (0.004) (11.718) (16.167) Working in public sector −0.012 −0.054*** 21.079 294.633** (0.028) (0.021) (101.420) (141.145) Rural 0.017 0.017 40.632 82.299 (0.018) (0.016) (55.064) (58.220) Household asset −0.004 −0.010 230.205*** 125.220*** (0.006) (0.007) (29.027) (13.827) No. of households 1,158 1,044 1,416 1,437 . Dependent variables: . . Labour supply . Consumption . . Father . Mother . Father . Mother . . (1) . (2) . (3) . (4) . Early health shocks −0.048 0.054** −128.808* 27.751 (0.078) (0.024) (77.978) (73.685) Child birthweight (mean) 0.015 0.002 77.850* 27.692 (0.020) (0.014) (44.919) (30.173) Child age −0.000 0.005 −8.672 −9.728 (0.004) (0.005) (7.799) (7.860) Male twins 0.005 −0.017 −60.571 −22.393 (0.023) (0.021) (54.827) (28.318) Female twins −0.023 −0.034 −28.210 42.148 (0.022) (0.021) (57.334) (38.050) Born at the first parity −0.003 −0.049** −15.817 4.098 (0.026) (0.023) (43.038) (30.684) Age −0.003 −0.005 −13.630*** −5.438** (0.002) (0.004) (3.359) (2.629) Ethnicity (Han = 1) −0.028* −0.030* −47.481 −127.626 (0.016) (0.016) (59.532) (97.041) Schooling years −0.007 0.001 0.218 29.564* (0.005) (0.004) (11.718) (16.167) Working in public sector −0.012 −0.054*** 21.079 294.633** (0.028) (0.021) (101.420) (141.145) Rural 0.017 0.017 40.632 82.299 (0.018) (0.016) (55.064) (58.220) Household asset −0.004 −0.010 230.205*** 125.220*** (0.006) (0.007) (29.027) (13.827) No. of households 1,158 1,044 1,416 1,437 Notes Columns (1)–(4) reports the OLS estimates. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab Table 8 Child Early Health Shocks and Parental Labour Supply and Consumption . Dependent variables: . . Labour supply . Consumption . . Father . Mother . Father . Mother . . (1) . (2) . (3) . (4) . Early health shocks −0.048 0.054** −128.808* 27.751 (0.078) (0.024) (77.978) (73.685) Child birthweight (mean) 0.015 0.002 77.850* 27.692 (0.020) (0.014) (44.919) (30.173) Child age −0.000 0.005 −8.672 −9.728 (0.004) (0.005) (7.799) (7.860) Male twins 0.005 −0.017 −60.571 −22.393 (0.023) (0.021) (54.827) (28.318) Female twins −0.023 −0.034 −28.210 42.148 (0.022) (0.021) (57.334) (38.050) Born at the first parity −0.003 −0.049** −15.817 4.098 (0.026) (0.023) (43.038) (30.684) Age −0.003 −0.005 −13.630*** −5.438** (0.002) (0.004) (3.359) (2.629) Ethnicity (Han = 1) −0.028* −0.030* −47.481 −127.626 (0.016) (0.016) (59.532) (97.041) Schooling years −0.007 0.001 0.218 29.564* (0.005) (0.004) (11.718) (16.167) Working in public sector −0.012 −0.054*** 21.079 294.633** (0.028) (0.021) (101.420) (141.145) Rural 0.017 0.017 40.632 82.299 (0.018) (0.016) (55.064) (58.220) Household asset −0.004 −0.010 230.205*** 125.220*** (0.006) (0.007) (29.027) (13.827) No. of households 1,158 1,044 1,416 1,437 . Dependent variables: . . Labour supply . Consumption . . Father . Mother . Father . Mother . . (1) . (2) . (3) . (4) . Early health shocks −0.048 0.054** −128.808* 27.751 (0.078) (0.024) (77.978) (73.685) Child birthweight (mean) 0.015 0.002 77.850* 27.692 (0.020) (0.014) (44.919) (30.173) Child age −0.000 0.005 −8.672 −9.728 (0.004) (0.005) (7.799) (7.860) Male twins 0.005 −0.017 −60.571 −22.393 (0.023) (0.021) (54.827) (28.318) Female twins −0.023 −0.034 −28.210 42.148 (0.022) (0.021) (57.334) (38.050) Born at the first parity −0.003 −0.049** −15.817 4.098 (0.026) (0.023) (43.038) (30.684) Age −0.003 −0.005 −13.630*** −5.438** (0.002) (0.004) (3.359) (2.629) Ethnicity (Han = 1) −0.028* −0.030* −47.481 −127.626 (0.016) (0.016) (59.532) (97.041) Schooling years −0.007 0.001 0.218 29.564* (0.005) (0.004) (11.718) (16.167) Working in public sector −0.012 −0.054*** 21.079 294.633** (0.028) (0.021) (101.420) (141.145) Rural 0.017 0.017 40.632 82.299 (0.018) (0.016) (55.064) (58.220) Household asset −0.004 −0.010 230.205*** 125.220*** (0.006) (0.007) (29.027) (13.827) No. of households 1,158 1,044 1,416 1,437 Notes Columns (1)–(4) reports the OLS estimates. Standard errors are in parenthesis; *significant at 10%; **significant at 5%; ***significant at 1%. Open in new tab 5. Conclusions This article studies how child early health shocks affect intra‐household resource allocation and child human capital formation. We formulate a theoretical model that early health shocks can affect human capital through two channels: a direct channel – the biological effect through the production of human capital – and an indirect one – the intra‐household resource allocation effect through parental responses. By introducing multidimensionality of human capital, parents could compensate and reinforce along different dimensions with respect to early health shocks on children. By using the CCTS data, we find evidence of compensating investment in child health but of reinforcing investment in education. We further estimate the child human capital production function. The results confirm that early health shocks negatively affect child human capital, ranging from health and education to socio‐emotional skills. Reduced‐form estimates, which ignore the intra‐household allocation process, understate the biological effect for health but overstate the biological effect for some educational outcomes. Our results have important implications for evaluating the role of the family in creating overall inequality in the economy. When parents can simultaneously make reinforcing and compensating family investments on children along different dimensions of human capital, the effects of intra‐household resource allocation on inequality becomes complicated. On the basis of our estimates, we conclude that the family appears to be a net equaliser in terms of family investment in financial terms. Our findings also emphasise the importance of accounting for parental behavioural responses to early health shocks. Intra‐household responses should be considered when designing public interventions to remediate negative health shocks on children, because parents can partly offset the effect of public interventions by reallocating resources within the family. Further research on the intra‐household resource allocation and human capital formation is desirable. First, in line with recent progress on human capital production technology, estimating a structural model separating production technology from parental preference would be valuable. Second, consistent with the empirical literature based on sibling or twin data, our regression analyses use linear specifications. Relaxing the linearity specification in the estimation would be fruitful. However, this approach relies on the development of the econometrics of non‐linear fixed‐effects estimators. Finally, fertility decisions should be explicitly introduced in the next generation of models of intra‐household resource allocation. Footnotes 1 " It is straightforward to extend the model to a general case with n children in the family. 2 " We suppress the family subscript τ on the technology to simplify notation. 3 " In online Appendix A, we show that early health shocks measured in our empirical analysis are non‐infectious diarrhoea. 4 " Economists have stressed the importance of parental tutoring time as a determinant of child human capital production. We ignore this argument in our analysis because the parental tutoring time in our sample is small, and we find little effect of early health shocks on parental tutoring time. 5 " This assumption is approximately valid in the context of developing countries where public education and medical insurance are absent, which is discussed in later Sections. 6 " Unfortunately, we cannot distinguish between mental and physical diseases because the former has low prevalence in our sample. 7 " Grossman (2000) also measures medical care by personal medical expenditures on doctors, dentists, hospital care, prescribed and non‐prescribed drugs, non‐medical practitioners and medical appliances. 8 " The one‐child policy is strictly implemented in urban areas in Kunming. However, households in rural areas are encouraged to have one child, but are exempted from the strict one‐child policy, although they are allowed to have two children at most (Family Planning Commission of Yunnan Province, 2003). 9 " A similar issue has been extensively investigated in the literature on twin‐based estimation of returns to schooling (Griliches, 1979; Bound and Solon, 1999; Neumark, 1999). 10 " We ignore other covariates in the equation to simplify our discussion. We further assume no contagious effect of early health shocks. The result below holds if the contagious effect is symmetric within twin sibling pairs. 11 " The cross‐equation restriction also applies if eH is measured with errors which are related to family investment behaviour. See the discussion in online Appendix C. 12 " We report only the estimated coefficients on early health shock and health investment in the article. The full results are reported in online Appendix E. 13 " Cunha et al. (2010) also use educational investments as one argument in the production function of socio‐emotional skills. References Almlund , M. , Duckworth , A.L., Heckman , J.J. and Kautz , T. ( 2011 ). ‘Personality psychology and economics’, in ( E. Hanushek, S. Machin and L. Woessman, eds.), Handbook of the Economics of Education , pp. 1 – 181 , vol. 4, Amsterdam : Elsevier . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Almond , D. and Currie , J. ( 2011 ). ‘Human capital development before age five’, in ( D. Card and O. Ashenfelter, eds.), Handbook of Labor Economics , vol. 4B , pp. 1315 – 486 , Amsterdam : Elsevier . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Becker , G.S. and Tomes , N. ( 1976 ). ‘ Child endowments and the quantity and quality of children ’, Journal of Political Economy , vol. 84 ( 4 ), pp. S143 – 62 . Google Scholar Crossref Search ADS WorldCat Behrman , J.R. , Pollak , R.A. and Taubman , P. ( 1982 ). ‘ Parental preferences and provision for progeny ’, Journal of Political Economy , vol. 90 ( 1 ), pp. 52 – 73 . Google Scholar Crossref Search ADS WorldCat Behrman , J.R. , Pollak , R.A. and Taubman , P. ( 1986 ). ‘ Do parents favor boys? ’, International Economic Review , vol. 27 ( 1 ), pp. 33 – 54 . Google Scholar Crossref Search ADS WorldCat Behrman , J.R. , Rosenzweig , M.R. and Taubman , P. ( 1994 ). ‘ Endowments and the allocation of schooling in the family and in the marriage market: the twins experiment ’, Journal of Political Economy , vol. 102 ( 6 ), pp. 1131 – 74 . Google Scholar Crossref Search ADS WorldCat Borghans , L. , Duckworth , A.L., Heckman , J.J. and ter Weel , B. ( 2008 ). ‘ The economics and psychology of personality traits ’, Journal of Human Resources , vol. 43 ( 4 ), pp. 972 – 1059 . Google Scholar Crossref Search ADS WorldCat Bound , J. and Solon , G. 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Schultz and J.A. Strauss, eds.), Handbook of Development Economics , vol. 4 , pp. 3375 – 474 , Amsterdam : Elsevier . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Tomes , N. ( 1981 ). ‘ The family, inheritance, and the intergenerational transmission of inequality ’, Journal of Political Economy , vol. 89 ( 5 ), pp. 928 – 58 . Google Scholar Crossref Search ADS WorldCat Author notes " The research was supported in part by the American Bar Foundation, the Pritzker Children’s Initiative, the Buffett Early Childhood Fund, NIH grants NICHD R37HD065072 and R01HD54702, an anonymous funder, a European Research Council grant (DEVHEALTH 269874), a grant for the FIS from the Chinese University of Hong Kong and a grant from the Institute for New Economic Thinking (INET) to the Human Capital and Economic Opportunity Global Working Group (HCEO)– an initiative of the Becker Friedman Institute for Research in Economics (BFI). The views expressed in this article are those of the authors and not necessarily those of the funders or persons named here. © 2015 Royal Economic Society

Hanushek, Eric, A.

doi: 10.1111/ecoj.12266pmid: N/A

At first blush it seems almost silly to have a Feature on the impact of added time in instruction on student outcomes. After all, a higher dosage of teaching should obviously produce more learning. In reality, the prior research on this question has been quite inconclusive. This Feature, however, moves knowledge forward a considerable distance. The two articles – by Victor Lavy and by Steven Rivkin and Jeffrey Schiman – advance our understanding in three different areas. First, the substantive conclusions about the positive impact of added time help to remove uncertainty about effects and provide direct policy guidance. Second, each of the articles addresses the methodological issues that have plagued prior research in a careful and thoughtful way. These ideas on approach go beyond just the evaluation of time use in the classroom. Third, by providing intriguing insights into variations of effects across countries, both underscore the value of comparative international studies. The issue of instructional time has received policy attention over a long period. The initial impetus of this attention was the easily observed fact that the number of days of attendance per school year varied dramatically, ranging from 160 to 240. Subsequently, others noted that the length of the school day also varied dramatically, leading to a different picture of the amount of overall instructional time across countries. But, while counting contact time is relatively easy, understanding its impact is less so. The analyses of Lavy and Rivkin–Shiman have a number of common features. Both employ the international PISA data: Lavy for 2006 and Rivkin–Shiman for 2009. Both make use of the variations in instructional time and performance found within individual schools. And both provide thorough discussions of the challenges faced in doing such empirical work. The findings are quite consistent. Both show that added instructional time pays off in terms of student learning. Lavy does this by developing and implementing estimation based on student fixed effects where student achievement across different subjects is compared to time spent on each of these subjects. Rivkin–Shiman follow this tactic (albeit implemented in a different way) and compare this with the results of estimation based on performance comparisons across grades in a school but within subject. The results of the two studies with respect to amount of weekly instructional time are consistent and quite precisely estimated. As such, they provide first‐order policy information. From the basic estimation of average effects, each pursues a series of added investigations, fanning out into different dimensions of potential heterogeneous effects. Lavy considers whether the effects look the same across countries at different levels of development. Here, it appears that time of instruction is more important in advanced countries as opposed to developing countries. Further, within developed countries, school‐based accountability enhances the productivity of time. Rivkin–Shiman look in different directions. Specifically, they stay at the more micro level and consider diminishing returns to added time (which seems to be present). Importantly, they also consider how time interacts with the quality of the classroom environment as measured by survey information about classroom disruptions, bullying, attendance and so forth. They show, perhaps not surprisingly, that more time is more productive in a good classroom environment than a poor environment. These substantive findings are clearly of interest to education researchers and policy makers. But there is also another aspect of these articles that is of interest to a wider audience. Specifically, they show that methodology matters. Simple running an OLS regression of time on achievement while controlling for any number of other measured attributes does a very poor job of eliminating the inherent selection bias. The OLS estimates in both studies are two to three times larger than the better identified estimates that are their focus. The better identified estimates that they provide come from a key insight in the work. Even though the PISA data come from a cross‐section of students, they contain information that can be leveraged into better identification that lessens that chance of strong selection factors. Specifically, they use within‐student information and within‐school information in order to neutralise any potential impact of student selection into different school structures and of administrative decisions by the schools. While not foolproof, it is clear that they both have improved significantly on the cross‐sectional OLS evidence that drove most prior discussions. Moreover, the approach of extracting ‘good variation’ from the cross‐section undoubtedly has lessons for other analyses. The third area of interest in these articles is developing (and advertising) the value of the ever‐expanding amount of international data that are available. Even though there has been international achievement testing for a half century, it is only in the last few years that economists have begun to exploit these data (Hanushek and Woessmann 2011). Exploiting international data presents a number of challenges but also holds promise for providing new information that is difficult if not impossible to get from individual country data – as these articles demonstrate. Perhaps the most important aspect of the international data is providing insights into the importance of various institutions. Even the best identified national study presents challenges when it comes to generalising from the results, because these national studies are imbedded within an institutional structure common to all of the observed schools. A key element of international studies is the ability to look across institutions. Lavy’s analysis shows directly, for example that the productivity of time varies by level of development. This finding in turn suggests that not all findings from developed countries will generalise to the policy situation in developing countries – and vice versa. If one pursues thoughts of these institutional differences, one immediately sees that there is a lot of work remaining. Of course, truly good papers act to stimulate the thirst for further investigations – and these clearly do that. What is it about the institutional structure that matters? Or, related to the Rivkin–Shiman analysis, what elements of classroom (and teacher) quality are most important to the productive use of time? For example, some of the productivity differences across schools and across countries may reflect variations in teacher quality that directly interact with instructional time. Or, in policy terms related to both papers, what is the cost of adding time to one subject area? These kinds of questions are just the tip of iceberg about issues inspired by these articles. Reference Hanushek , E.A. and Woessmann , L. ( 2011 ). ‘The economics of international differences in educational achievement,’ in ( E.A. Hanushek, S. Machin and L. Woessmann, eds.), Handbook of the Economics of Education, vol. 3, pp. 89 – 200 , North Holland : Amsterdam . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC © 2015 Royal Economic Society

Currie,, Janet;Duque,, Valentina;Garfinkel,, Irwin

doi: 10.1111/ecoj.12239pmid: 27212714

Abstract We use longitudinal data from the Fragile Families and Child Well‐being Study to investigate the impacts of the Great Recession on the health of mothers. We focus on a wide range of physical and mental health outcomes, as well as health behaviour. We find that increases in the unemployment rate decrease self‐reported health status and increase smoking and drug use. We also find evidence of heterogeneous impacts. Disadvantaged mothers – African American, Hispanic, less educated and unmarried – experience greater deterioration in their health than advantaged mothers – those who are white, married and college educated. The Great Recession in the US was deeper and longer than any previous recession since the 1930s. From its peak – December 2007 to June 2009 – output contracted by 4%, the employment rate fell by 6.3% and the unemployment rate went from 4.8% in April 2008 to 10.6% at its peak in January 2010 (NBER, at http://www.nber.org/cycles.html). As of June 2013, the unemployment rate was still 2.8 percentage points above what it was at the start of the recession, the labour force participation rate was 63.5%, the lowest rate since 1978 and the percentage of the population with a job, 58.7%, was stuck near levels last seen in the early 1980s (Bureau of Labor Statistics, 2013; Center for Budget Policy and Priorities, 2013). The start of the Great Recession was severe, sudden and sharp, and many people experienced some form of financial, psychological or physical strain. New evidence on the effects of the Great Recession has confirmed that losses were disproportionately concentrated among minorities, youth, low income and less‐educated workers (Hout et al., 2011; Hoynes et al., 2012) and that while men have faced higher unemployment than women, their employment recovery has been faster (Kochhar, 2011). Since the Great Recession represented a huge financial and psychological shock for many households, in particular for the most vulnerable, it may have had a significant impact on people’s health. Many studies have examined the relationship between economic downturns and health outcomes; however, the conclusions are mixed. This study aims to contribute to this discussion by investigating the impacts of the Great Recession on the physical and mental health and health behaviour of women with children. Our study contributes to the literature in several ways. First, we are one of the first studies to use longitudinal data to analyse the effects of economic fluctuations on health, and the first to do so for the case of the Great Recession. We employ panel data from the Fragile Families and Child Well‐being Study (FF) that allows to observe the same mother before and during (the start of) the financial crisis, so we are able to control for individual time‐invariant characteristics that might be correlated with both the probability of residing in an area with high unemployment and with experiencing declines in health. Second, by including data that incorporate the Great Recession (from mid‐2007 to the beginning of 2010), we are able to exploit greater exogenous variation in the unemployment rate across states and years, as compared to studies using pre‐Great Recession data that have examined macroeconomic downturns that exhibit less variation and shorter unemployment durations. Third, we focus on mothers. Most evidence regarding the link between economic fluctuations and health has focused on employed workers (usually men), who have traditionally had the strongest labour force attachment. Hence, much less is known about mothers who have varying degrees of labour force participation but may also be impacted by high unemployment in their communities. Focusing on mothers is especially interesting given recent research showing that inequality starts early in life and that the children of disadvantaged mothers are more likely to grow up to be disadvantaged themselves (Currie and Stabile, 2003; Case et al., 2005; Currie, 2009; Almond and Currie, 2011). Fourth, the FF provides a wide range of self‐reported health outcomes – including measures of physical and mental health as well as health behaviour. Fifth, we examine heterogeneity of response by race/ethnicity, education and family structure. We find that the crisis worsened mothers’ self‐reported health status and led to increases in their smoking and drug use. We also find heterogeneous responses. Blacks and Hispanics, unmarried women and mothers with a high school degree or less became less likely to report ‘excellent’ or ‘very good’ health or to have good mental health; whites, married women and highly educated mothers on the other hand, were likely to have better mental health as well as to experience some improvements in their physical health: whites were less likely to be obese and highly educated women were less likely to have health problems as unemployment increased. In other words, our results confirm that the Great Recession helped accentuate health disparities between mothers in more and less advantaged families, a result that may have disturbing implications for future disparities between their children. This article is organised as follows: Section 1 presents a summary of the related literature, Sections 2 and 3 describe the data and the empirical strategy, respectively, followed by the results in Section 4 and some extensions in Section 5. Section 6 provides a brief conclusion. 1. Background Previous studies of the effects of economic shocks on health have come to very different conclusions. A number of studies claim that health improves during economic downturns, arguing that this is largely because people change their health behaviour (e.g. smoke and drink less, lose weight, exercise more etc.) (Ruhm, 2000, 2003, 2005; Ruhm and Black, 2002; Dehejia and Lleras‐Muney, 2004). Other studies find that unemployment is associated with poorer health, a finding that is variously attributed to the stress associated with losing a job, fearing job loss and/or reductions in income and wealth (Dee, 2001; Eliason and Storrie, 2009a, b; Sullivan and von Wachter, 2009; Browning and Heinesen, 2012). The lack of consensus and the fact that most of the evidence pertains to prime‐age men suggest that additional research is warranted. Table 1 provides an overview of the previous literature. Most prior work utilises repeated cross sections of US data, often at the state level, and exploits state and year variation in the unemployment rate to examine changes in health and health behaviours. Previous studies have also concentrated on analysing health outcomes for working‐age individuals with strong labour force attachment, usually men. Thus, little is known about the impact of unemployment on other demographic groups (e.g. mothers). Almost all studies predate the Great Recession. Table 1 Effects of Unemployment Rate (UR) on Health Outcomes Outcome variable . Study and data . Health status/health problem that limits work . Weight . Use of medical care/health insurance . Smokes . Drinks . Mental health . 1. Studies examining men and women Ruhm (2000) Micro data: – BRFSS: 1987–95 N = 114,000 men and women Methods: Linear model A 1 pp rise in the UR reduces: – Underweight by 0.06 pp – Overweight by 0.17 pp – Obesity by 0.21 pp No analysis by gender A 1 pp rise in the UR reduces: – Visits to the doctor by 0.57 pp No analysis by gender A 1 pp rise in the UR: – Reduces smoking by 0.3 pp – Reduces no. of cigs per day by 0.8 pp for current smokers No analysis by gender A 1 pp rise in the UR: – Increases alcohol consumption but is non‐significant No analysis by gender Ruhm and Black (2002) Micro data: – BRFSS: 1987–99 – N = 500,000 men and women Methods: linear model A 1 pp rise in UR: – Reduces predicted drinking by 0.2 pp – Reduces log(no. of drinks) in last month by 3.1 pp for drinkers – No effect on binge drinking By gender: – No difference in the probability of drinking – Higher decline for men: no. of drinks falls by 3.4 pp versus 2.8 pp for females Ruhm (2003) Micro data: – NHIS: 1972–81 for individuals 30+ 3 samples: (1) Full sample: N = 217,471 men and women (2) 30–64‐year‐old workers: N = 115,463 observation, men and women (3) 30–55‐year‐old working males: N = 57,633 Methods: linear model A 1 pp fall in the UR: – For everyone: increases the probability of having a medical condition (chronic or acute) by 0.6 pp – Stronger effects for men of working age By gender: – For men 30–55: increases by 0.63 pp – For women 30–55: increases by 0.59 pp Hospital visit is NON‐significant in all cases A 1 pp fall in the UR: – For everyone: the probability of hospitalisation falls by 0.11 pp and doctor visits rises by 0.3 although non‐significant – Stronger effects for men of working age By gender results were non‐significant: – For men 30–55: falls by 0.11 pp – For women 30–55: falls by 0.13 pp Ruhm (2005) Micro data: – BRFSS: sample includes individuals aged 18+ from the 1987–2000 waves N = approx. 1.5 million obs, men and women Methods: linear model – A 1 pp fall in the employment rate: – Reduces obesity by 0.07 pp – Reduces severely obese by 0.4 pp – No effect on overweight No differences by gender – A 1 pp fall in the employment rate reduces: – Smoking by 0.13 pp – Smoking of at least 20 cigs/day by 0.10 pp smoking at least 40 cig/day by 0.015 pp By gender: The effect on smoking is stronger for females (0.17 pp) than for males (0.09 pp) Dee (2001) Micro data: – BRFSS, 1984–95 – N > 700,000, ‘prime‐age’ men and women 18+ (average age is 45) Methods: linear model A 5 pp increase in UR: – Reduces drinks per month by 3.5% and chronic drinking participation (60 or more drinks/month) by 19% – Binge drinking rises by 8% By gender: – The probability of binge drinking for males is >3 times larger than that for females Tekin et al. (2013) Micro data: – BRFSS sample: N = 849,594, individuals in the Labour force, ages 25–55 Methods: linear model A 1 pp drop in ER: – Probability of being in poor health rises by 0.00067 pp (4.8%) By gender: – Strongest effects on females: ‘excellent health’ falls by 0.0044 pp (1.8%) and poor health increases by 0.0015 pp (1.0%) A 1 pp drop in ER: – Binge drinking (respondent reports had 60 or more drinks during the past month) falls by 0.0023 pp By gender: – Effect on binge drinking is driven by women (0.0022 pp) 2. Studies Examining Men Only Charles and DeCicca (2008) Micro data: – NHIS: sample of working‐aged men in the US living in ‘large’ MSAs: 1997–2001 N = 30,000–35,000 men of working age Methods: linear model A 1 pp rise in the UR: – Men with low ex ante employment probabilities experience an increase in underweight by 0.5 pp, in overweight by 3.5 pp, and in obesity by 2 pp No effects on men with high employment probability A 1 pp rise in the UR: – Smoking rises by 2.7 pp for those in the lowest employment decile – 2.3 pp reduction for those most likely to be employed A 1 pp rise in the UR: – Only for the group with highest employment probability drinking rises (3.6 pp) – no. of days with 5 drinks or more declines for all but it is not statistically significant A 1 pp rise in the UR: – Leads to rises in: sadness (1.5 pp), hopelessness (1.1 pp), worthlessness (0.9 pp), restlessness (1.2 pp), nervousness (1.3 pp) and feelings of effort (2.5 pp) – Strongest effects for those least likely to be employed Xu and Kaestner (2010) Micro data: – BRFSS (1984–2005, N = 506,753) and NHIS (1976–2001, N = 216,113), men between 25 and 55 Methods: linear model A 2.5% increase in employment: – Decreases doctor visits by 1.5 pp A 2.5% increase in employment: – Increases smoking by 1 pp – Increases smoking intensity (smokes >19 cigarettes a day y/n) by 2 pp A 2.5% increase in employment: – Increases drinking by 0.1 pp – Decreases binge drinking by 0.2 pp 3. Sample: Longitudinal data Davalos and French (2011) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed 78%; N = 26,313 Methods: linear model, individual fixed‐effects A 1% increase in UR: OLS: – non‐significant effects on physical health score Individual FE: – reduces physical health score by 0.9% No differences by gender A 1% increase in UR: OLS: – reduces mental health score by 1.3% Individual FE: – reduces mental health score by 1.2% No differences by gender Davalos et al. (2012) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed = 64%; N = 34,120 Methods: – Logit, logit individual fixed‐effects A 1 pp increase in state UR: Individual‐FE: – Leads to a 1 binge drinking day increase per year – A 1.350 increase in the odds of driving after too much drink – A 1.167 increase in the odds of alcohol abuse/dependence No differences by gender (not shown) Outcome variable . Study and data . Health status/health problem that limits work . Weight . Use of medical care/health insurance . Smokes . Drinks . Mental health . 1. Studies examining men and women Ruhm (2000) Micro data: – BRFSS: 1987–95 N = 114,000 men and women Methods: Linear model A 1 pp rise in the UR reduces: – Underweight by 0.06 pp – Overweight by 0.17 pp – Obesity by 0.21 pp No analysis by gender A 1 pp rise in the UR reduces: – Visits to the doctor by 0.57 pp No analysis by gender A 1 pp rise in the UR: – Reduces smoking by 0.3 pp – Reduces no. of cigs per day by 0.8 pp for current smokers No analysis by gender A 1 pp rise in the UR: – Increases alcohol consumption but is non‐significant No analysis by gender Ruhm and Black (2002) Micro data: – BRFSS: 1987–99 – N = 500,000 men and women Methods: linear model A 1 pp rise in UR: – Reduces predicted drinking by 0.2 pp – Reduces log(no. of drinks) in last month by 3.1 pp for drinkers – No effect on binge drinking By gender: – No difference in the probability of drinking – Higher decline for men: no. of drinks falls by 3.4 pp versus 2.8 pp for females Ruhm (2003) Micro data: – NHIS: 1972–81 for individuals 30+ 3 samples: (1) Full sample: N = 217,471 men and women (2) 30–64‐year‐old workers: N = 115,463 observation, men and women (3) 30–55‐year‐old working males: N = 57,633 Methods: linear model A 1 pp fall in the UR: – For everyone: increases the probability of having a medical condition (chronic or acute) by 0.6 pp – Stronger effects for men of working age By gender: – For men 30–55: increases by 0.63 pp – For women 30–55: increases by 0.59 pp Hospital visit is NON‐significant in all cases A 1 pp fall in the UR: – For everyone: the probability of hospitalisation falls by 0.11 pp and doctor visits rises by 0.3 although non‐significant – Stronger effects for men of working age By gender results were non‐significant: – For men 30–55: falls by 0.11 pp – For women 30–55: falls by 0.13 pp Ruhm (2005) Micro data: – BRFSS: sample includes individuals aged 18+ from the 1987–2000 waves N = approx. 1.5 million obs, men and women Methods: linear model – A 1 pp fall in the employment rate: – Reduces obesity by 0.07 pp – Reduces severely obese by 0.4 pp – No effect on overweight No differences by gender – A 1 pp fall in the employment rate reduces: – Smoking by 0.13 pp – Smoking of at least 20 cigs/day by 0.10 pp smoking at least 40 cig/day by 0.015 pp By gender: The effect on smoking is stronger for females (0.17 pp) than for males (0.09 pp) Dee (2001) Micro data: – BRFSS, 1984–95 – N > 700,000, ‘prime‐age’ men and women 18+ (average age is 45) Methods: linear model A 5 pp increase in UR: – Reduces drinks per month by 3.5% and chronic drinking participation (60 or more drinks/month) by 19% – Binge drinking rises by 8% By gender: – The probability of binge drinking for males is >3 times larger than that for females Tekin et al. (2013) Micro data: – BRFSS sample: N = 849,594, individuals in the Labour force, ages 25–55 Methods: linear model A 1 pp drop in ER: – Probability of being in poor health rises by 0.00067 pp (4.8%) By gender: – Strongest effects on females: ‘excellent health’ falls by 0.0044 pp (1.8%) and poor health increases by 0.0015 pp (1.0%) A 1 pp drop in ER: – Binge drinking (respondent reports had 60 or more drinks during the past month) falls by 0.0023 pp By gender: – Effect on binge drinking is driven by women (0.0022 pp) 2. Studies Examining Men Only Charles and DeCicca (2008) Micro data: – NHIS: sample of working‐aged men in the US living in ‘large’ MSAs: 1997–2001 N = 30,000–35,000 men of working age Methods: linear model A 1 pp rise in the UR: – Men with low ex ante employment probabilities experience an increase in underweight by 0.5 pp, in overweight by 3.5 pp, and in obesity by 2 pp No effects on men with high employment probability A 1 pp rise in the UR: – Smoking rises by 2.7 pp for those in the lowest employment decile – 2.3 pp reduction for those most likely to be employed A 1 pp rise in the UR: – Only for the group with highest employment probability drinking rises (3.6 pp) – no. of days with 5 drinks or more declines for all but it is not statistically significant A 1 pp rise in the UR: – Leads to rises in: sadness (1.5 pp), hopelessness (1.1 pp), worthlessness (0.9 pp), restlessness (1.2 pp), nervousness (1.3 pp) and feelings of effort (2.5 pp) – Strongest effects for those least likely to be employed Xu and Kaestner (2010) Micro data: – BRFSS (1984–2005, N = 506,753) and NHIS (1976–2001, N = 216,113), men between 25 and 55 Methods: linear model A 2.5% increase in employment: – Decreases doctor visits by 1.5 pp A 2.5% increase in employment: – Increases smoking by 1 pp – Increases smoking intensity (smokes >19 cigarettes a day y/n) by 2 pp A 2.5% increase in employment: – Increases drinking by 0.1 pp – Decreases binge drinking by 0.2 pp 3. Sample: Longitudinal data Davalos and French (2011) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed 78%; N = 26,313 Methods: linear model, individual fixed‐effects A 1% increase in UR: OLS: – non‐significant effects on physical health score Individual FE: – reduces physical health score by 0.9% No differences by gender A 1% increase in UR: OLS: – reduces mental health score by 1.3% Individual FE: – reduces mental health score by 1.2% No differences by gender Davalos et al. (2012) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed = 64%; N = 34,120 Methods: – Logit, logit individual fixed‐effects A 1 pp increase in state UR: Individual‐FE: – Leads to a 1 binge drinking day increase per year – A 1.350 increase in the odds of driving after too much drink – A 1.167 increase in the odds of alcohol abuse/dependence No differences by gender (not shown) Open in new tab Table 1 Effects of Unemployment Rate (UR) on Health Outcomes Outcome variable . Study and data . Health status/health problem that limits work . Weight . Use of medical care/health insurance . Smokes . Drinks . Mental health . 1. Studies examining men and women Ruhm (2000) Micro data: – BRFSS: 1987–95 N = 114,000 men and women Methods: Linear model A 1 pp rise in the UR reduces: – Underweight by 0.06 pp – Overweight by 0.17 pp – Obesity by 0.21 pp No analysis by gender A 1 pp rise in the UR reduces: – Visits to the doctor by 0.57 pp No analysis by gender A 1 pp rise in the UR: – Reduces smoking by 0.3 pp – Reduces no. of cigs per day by 0.8 pp for current smokers No analysis by gender A 1 pp rise in the UR: – Increases alcohol consumption but is non‐significant No analysis by gender Ruhm and Black (2002) Micro data: – BRFSS: 1987–99 – N = 500,000 men and women Methods: linear model A 1 pp rise in UR: – Reduces predicted drinking by 0.2 pp – Reduces log(no. of drinks) in last month by 3.1 pp for drinkers – No effect on binge drinking By gender: – No difference in the probability of drinking – Higher decline for men: no. of drinks falls by 3.4 pp versus 2.8 pp for females Ruhm (2003) Micro data: – NHIS: 1972–81 for individuals 30+ 3 samples: (1) Full sample: N = 217,471 men and women (2) 30–64‐year‐old workers: N = 115,463 observation, men and women (3) 30–55‐year‐old working males: N = 57,633 Methods: linear model A 1 pp fall in the UR: – For everyone: increases the probability of having a medical condition (chronic or acute) by 0.6 pp – Stronger effects for men of working age By gender: – For men 30–55: increases by 0.63 pp – For women 30–55: increases by 0.59 pp Hospital visit is NON‐significant in all cases A 1 pp fall in the UR: – For everyone: the probability of hospitalisation falls by 0.11 pp and doctor visits rises by 0.3 although non‐significant – Stronger effects for men of working age By gender results were non‐significant: – For men 30–55: falls by 0.11 pp – For women 30–55: falls by 0.13 pp Ruhm (2005) Micro data: – BRFSS: sample includes individuals aged 18+ from the 1987–2000 waves N = approx. 1.5 million obs, men and women Methods: linear model – A 1 pp fall in the employment rate: – Reduces obesity by 0.07 pp – Reduces severely obese by 0.4 pp – No effect on overweight No differences by gender – A 1 pp fall in the employment rate reduces: – Smoking by 0.13 pp – Smoking of at least 20 cigs/day by 0.10 pp smoking at least 40 cig/day by 0.015 pp By gender: The effect on smoking is stronger for females (0.17 pp) than for males (0.09 pp) Dee (2001) Micro data: – BRFSS, 1984–95 – N > 700,000, ‘prime‐age’ men and women 18+ (average age is 45) Methods: linear model A 5 pp increase in UR: – Reduces drinks per month by 3.5% and chronic drinking participation (60 or more drinks/month) by 19% – Binge drinking rises by 8% By gender: – The probability of binge drinking for males is >3 times larger than that for females Tekin et al. (2013) Micro data: – BRFSS sample: N = 849,594, individuals in the Labour force, ages 25–55 Methods: linear model A 1 pp drop in ER: – Probability of being in poor health rises by 0.00067 pp (4.8%) By gender: – Strongest effects on females: ‘excellent health’ falls by 0.0044 pp (1.8%) and poor health increases by 0.0015 pp (1.0%) A 1 pp drop in ER: – Binge drinking (respondent reports had 60 or more drinks during the past month) falls by 0.0023 pp By gender: – Effect on binge drinking is driven by women (0.0022 pp) 2. Studies Examining Men Only Charles and DeCicca (2008) Micro data: – NHIS: sample of working‐aged men in the US living in ‘large’ MSAs: 1997–2001 N = 30,000–35,000 men of working age Methods: linear model A 1 pp rise in the UR: – Men with low ex ante employment probabilities experience an increase in underweight by 0.5 pp, in overweight by 3.5 pp, and in obesity by 2 pp No effects on men with high employment probability A 1 pp rise in the UR: – Smoking rises by 2.7 pp for those in the lowest employment decile – 2.3 pp reduction for those most likely to be employed A 1 pp rise in the UR: – Only for the group with highest employment probability drinking rises (3.6 pp) – no. of days with 5 drinks or more declines for all but it is not statistically significant A 1 pp rise in the UR: – Leads to rises in: sadness (1.5 pp), hopelessness (1.1 pp), worthlessness (0.9 pp), restlessness (1.2 pp), nervousness (1.3 pp) and feelings of effort (2.5 pp) – Strongest effects for those least likely to be employed Xu and Kaestner (2010) Micro data: – BRFSS (1984–2005, N = 506,753) and NHIS (1976–2001, N = 216,113), men between 25 and 55 Methods: linear model A 2.5% increase in employment: – Decreases doctor visits by 1.5 pp A 2.5% increase in employment: – Increases smoking by 1 pp – Increases smoking intensity (smokes >19 cigarettes a day y/n) by 2 pp A 2.5% increase in employment: – Increases drinking by 0.1 pp – Decreases binge drinking by 0.2 pp 3. Sample: Longitudinal data Davalos and French (2011) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed 78%; N = 26,313 Methods: linear model, individual fixed‐effects A 1% increase in UR: OLS: – non‐significant effects on physical health score Individual FE: – reduces physical health score by 0.9% No differences by gender A 1% increase in UR: OLS: – reduces mental health score by 1.3% Individual FE: – reduces mental health score by 1.2% No differences by gender Davalos et al. (2012) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed = 64%; N = 34,120 Methods: – Logit, logit individual fixed‐effects A 1 pp increase in state UR: Individual‐FE: – Leads to a 1 binge drinking day increase per year – A 1.350 increase in the odds of driving after too much drink – A 1.167 increase in the odds of alcohol abuse/dependence No differences by gender (not shown) Outcome variable . Study and data . Health status/health problem that limits work . Weight . Use of medical care/health insurance . Smokes . Drinks . Mental health . 1. Studies examining men and women Ruhm (2000) Micro data: – BRFSS: 1987–95 N = 114,000 men and women Methods: Linear model A 1 pp rise in the UR reduces: – Underweight by 0.06 pp – Overweight by 0.17 pp – Obesity by 0.21 pp No analysis by gender A 1 pp rise in the UR reduces: – Visits to the doctor by 0.57 pp No analysis by gender A 1 pp rise in the UR: – Reduces smoking by 0.3 pp – Reduces no. of cigs per day by 0.8 pp for current smokers No analysis by gender A 1 pp rise in the UR: – Increases alcohol consumption but is non‐significant No analysis by gender Ruhm and Black (2002) Micro data: – BRFSS: 1987–99 – N = 500,000 men and women Methods: linear model A 1 pp rise in UR: – Reduces predicted drinking by 0.2 pp – Reduces log(no. of drinks) in last month by 3.1 pp for drinkers – No effect on binge drinking By gender: – No difference in the probability of drinking – Higher decline for men: no. of drinks falls by 3.4 pp versus 2.8 pp for females Ruhm (2003) Micro data: – NHIS: 1972–81 for individuals 30+ 3 samples: (1) Full sample: N = 217,471 men and women (2) 30–64‐year‐old workers: N = 115,463 observation, men and women (3) 30–55‐year‐old working males: N = 57,633 Methods: linear model A 1 pp fall in the UR: – For everyone: increases the probability of having a medical condition (chronic or acute) by 0.6 pp – Stronger effects for men of working age By gender: – For men 30–55: increases by 0.63 pp – For women 30–55: increases by 0.59 pp Hospital visit is NON‐significant in all cases A 1 pp fall in the UR: – For everyone: the probability of hospitalisation falls by 0.11 pp and doctor visits rises by 0.3 although non‐significant – Stronger effects for men of working age By gender results were non‐significant: – For men 30–55: falls by 0.11 pp – For women 30–55: falls by 0.13 pp Ruhm (2005) Micro data: – BRFSS: sample includes individuals aged 18+ from the 1987–2000 waves N = approx. 1.5 million obs, men and women Methods: linear model – A 1 pp fall in the employment rate: – Reduces obesity by 0.07 pp – Reduces severely obese by 0.4 pp – No effect on overweight No differences by gender – A 1 pp fall in the employment rate reduces: – Smoking by 0.13 pp – Smoking of at least 20 cigs/day by 0.10 pp smoking at least 40 cig/day by 0.015 pp By gender: The effect on smoking is stronger for females (0.17 pp) than for males (0.09 pp) Dee (2001) Micro data: – BRFSS, 1984–95 – N > 700,000, ‘prime‐age’ men and women 18+ (average age is 45) Methods: linear model A 5 pp increase in UR: – Reduces drinks per month by 3.5% and chronic drinking participation (60 or more drinks/month) by 19% – Binge drinking rises by 8% By gender: – The probability of binge drinking for males is >3 times larger than that for females Tekin et al. (2013) Micro data: – BRFSS sample: N = 849,594, individuals in the Labour force, ages 25–55 Methods: linear model A 1 pp drop in ER: – Probability of being in poor health rises by 0.00067 pp (4.8%) By gender: – Strongest effects on females: ‘excellent health’ falls by 0.0044 pp (1.8%) and poor health increases by 0.0015 pp (1.0%) A 1 pp drop in ER: – Binge drinking (respondent reports had 60 or more drinks during the past month) falls by 0.0023 pp By gender: – Effect on binge drinking is driven by women (0.0022 pp) 2. Studies Examining Men Only Charles and DeCicca (2008) Micro data: – NHIS: sample of working‐aged men in the US living in ‘large’ MSAs: 1997–2001 N = 30,000–35,000 men of working age Methods: linear model A 1 pp rise in the UR: – Men with low ex ante employment probabilities experience an increase in underweight by 0.5 pp, in overweight by 3.5 pp, and in obesity by 2 pp No effects on men with high employment probability A 1 pp rise in the UR: – Smoking rises by 2.7 pp for those in the lowest employment decile – 2.3 pp reduction for those most likely to be employed A 1 pp rise in the UR: – Only for the group with highest employment probability drinking rises (3.6 pp) – no. of days with 5 drinks or more declines for all but it is not statistically significant A 1 pp rise in the UR: – Leads to rises in: sadness (1.5 pp), hopelessness (1.1 pp), worthlessness (0.9 pp), restlessness (1.2 pp), nervousness (1.3 pp) and feelings of effort (2.5 pp) – Strongest effects for those least likely to be employed Xu and Kaestner (2010) Micro data: – BRFSS (1984–2005, N = 506,753) and NHIS (1976–2001, N = 216,113), men between 25 and 55 Methods: linear model A 2.5% increase in employment: – Decreases doctor visits by 1.5 pp A 2.5% increase in employment: – Increases smoking by 1 pp – Increases smoking intensity (smokes >19 cigarettes a day y/n) by 2 pp A 2.5% increase in employment: – Increases drinking by 0.1 pp – Decreases binge drinking by 0.2 pp 3. Sample: Longitudinal data Davalos and French (2011) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed 78%; N = 26,313 Methods: linear model, individual fixed‐effects A 1% increase in UR: OLS: – non‐significant effects on physical health score Individual FE: – reduces physical health score by 0.9% No differences by gender A 1% increase in UR: OLS: – reduces mental health score by 1.3% Individual FE: – reduces mental health score by 1.2% No differences by gender Davalos et al. (2012) Micro data: – NESARC, PANEL, 2001/2002 and 2004/2005, men and women, ages: 18–59, prop. employed = 64%; N = 34,120 Methods: – Logit, logit individual fixed‐effects A 1 pp increase in state UR: Individual‐FE: – Leads to a 1 binge drinking day increase per year – A 1.350 increase in the odds of driving after too much drink – A 1.167 increase in the odds of alcohol abuse/dependence No differences by gender (not shown) Open in new tab 1.1. How Could The Unemployment Rate Affect Health? In a pioneering study, Ruhm (2000) linked data on state unemployment rates with state‐level Vital Statistics mortality records from 1971 to 1992, to examine the link between economic downturns and mortality. He found that a 1 percentage point increase in the state unemployment rate was associated with a 0.5% reduction in state mortality rates, and he claimed that this result was mainly driven by men of working age.1 Ruhm (2003), Neumayer (2004), and Gerdtham and Ruhm (2006), all find that higher unemployment is associated with lower mortality, and that individuals are less healthy during economic expansions. Dehejia and Lleras‐Muney (2004) found that infant health improves in times of high unemployment.2 However, Huff‐Stevens et al. (2011) suggest that cyclical changes in mortality are concentrated in the young and old, and so are unlikely to primarily represent changes in health behaviours among working‐age adults. In contrast to most studies using aggregate data, studies using individual‐level data tend to find negative effects of unemployment on health. For example, Sullivan and von Wachter (2009) use administrative data to follow a large sample of individuals subjected to mass lay‐offs in Pennsylvania and find significantly higher mortality due to accidents and heart conditions. These findings have been confirmed in two studies using Swedish data (Eliason and Storrie, 2009a, b), and in a study using Danish data (Browning and Heinesen, 2012). The disconnect between the literature on the effects of individual job loss and the literature on the effects of unemployment on state‐level outcomes suggests that it may be fruitful to investigate the effects of unemployment using individual‐level longitudinal data, as we do in this article. 1.2. How Does The Unemployment Rate Affect Health Behaviours? While Ruhm (1995) and Ruhm and Black (2002) found that drinking is pro‐cyclical, Ruhm (2000) later found that the association between the state unemployment rate and binge drinking was positive, although non‐significant and Tekin et al. (2013) found a negligible impact. Dee (2001), Charles and DeCicca (2008), Xu and Kaestner (2010) and Deb et al. (2011) provide evidence that drinking increases significantly during recessions.3 The evidence on smoking is even less conclusive. While a number of studies have found that when the economy contracts, smoking declines (Ruhm, 2000, 2005; Xu and Kaestner, 2010), others find that smoking is counter‐cyclical (Dehejia and Lleras‐Muney, 2004) or that there is a differential impact across demographic groups. Charles and DeCicca (2008) found that smoking was counter‐cyclical for minority and less‐educated men, whereas for those most likely to be employed, smoking fell in times of high unemployment. Studies of the effect of economic fluctuations on obesity – a well‐established risk factor for cardiovascular disease, high blood pressure and diabetes – provide similarly ambiguous findings. While Ruhm (2000, 2005) argues that during recessions body mass index (BMI) declines significantly and is particularly driven by those with severe obesity, Charles and DeCicca (2008) and Deb et al. (2011) found an increase in obesity that seemed to be driven by minority and less‐educated groups. Studies have also found a strong correlation between individual job loss and clinical and subclinical depression, anxiety and substance use (Murphy and Athanasou, 1999). Several economic studies argue that as the unemployment rate rises, mental health worsens and that this is evident in outcomes such as suicides and suicide attempts (Ruhm, 2000; Browning and Heinesen, 2012); anxiety, depression, loss of confidence and self‐esteem (Theodossiou, 1997); feelings of sadness, hopelessness, worthlessness, restlessness and nervousness (Charles and DeCicca, 2008); and substance use (Dee, 2001). Nevertheless, Tekin et al. (2013) find that only better educated individuals experience more mental health problems and they argue that economic deterioration exacts a larger toll on individuals who have a higher opportunity cost of job loss. Other studies have shown that experiencing unemployment is more strongly associated with mental health problems in men than in women (Artazcoz et al., 2004). Only two studies use US longitudinal data to examine the effects of recessions on health.4 Davalos and French (2011) and Davalos et al. (2012), focus on the period 2001 to 2005 and conclude that increases in the state unemployment rate led to a decline in physical and mental health, and to a rise in drinking among male and female workers aged 18 to 59. However, the effects were rather small, which may reflect the fact that the 2001 recession was mild and of short duration (Kliesen, 2003), providing little variation in unemployment rates. 1.3. Why The Effects of Unemployment Rates Are Likely to Be Heterogeneous? There are several reasons why we expect to find heterogeneous effects of the unemployment rate on different groups of mothers. First racial and ethnic minorities, less‐educated and younger workers experience higher unemployment and more pronounced income declines during recessions than other workers (Verick, 2010; Kochhar et al., 2011; Sierminska and Takhtamanova, 2011; Hoynes et al., 2012; Pfeffer et al., 2013). Indeed, many families are not at risk of unemployment and some may even profit from recessions. Second, disadvantaged women are more likely to work in low‐quality jobs with precarious work environments, non‐standard work hours and low job satisfaction and are subject to higher physical and mental health risks, and lower access to health insurance (Kim et al., 2008; Fischer and Sousa‐Poza, 2009). In addition to being more vulnerable to changes in economic conditions, these mothers experience higher poverty, and poverty has been associated with less preventive health care and poorer overall health (Katz and Hofer, 1994; DiMatteo et al., 2002). In addition, poverty impedes cognitive function and so when the poor face monetary concerns during times of high unemployment, they may lose their capacity to give full consideration to other problems, including health issues (Mani et al., 2013). Moreover, cumulative socio‐economic disadvantage can have negative effects on physical health (Geronimus, 1992). Finally, we expect larger effects of unemployment on unmarried as compared to married mothers. Unmarried mothers are significantly more likely to be African American or Hispanic and are more disadvantaged in terms of their education, income and assets and wealth – all of which make them more vulnerable to labour market fluctuations and which also limit their capacity to buffer shocks. Over and above these disadvantages, unwed mothers are disadvantaged by having to be both primary breadwinners and primary caretakers of their families and by their lower capacity to insure against contingencies and to risk share within the household (Becker, 1981; Lam, 1988). Unmarried mothers are likely to experience more stress, which could exhaust and undermine their health (Ross and Van Willigen, 1996; Acs and Nelson, 2002). As this summary indicates, the evidence on the relationship between economic fluctuations and health is far from clear. The heavy reliance on repeated cross sections, aggregate data, lack of variation in unemployment rates in the few longitudinal studies and insufficient attention to possibly heterogenous impacts of unemployment are weaknesses of the existing literature. Moreover, most of the existing evidence pertains to prime aged men. This study will add to the literature by using longitudinal data, incorporating the dramatic increase in unemployment caused by the Great Recession, and by attending to possibly heterogeneous effects. 2. Data To investigate the impacts of the Great Recession on mother’s health, we employ the Fragile Families and Child Wellbeing Study (FF), a longitudinal study of 4,897 births that occurred in 20 large US cities (population of 200,000 or more) located in 15 states, between 1998 and 2000. Unmarried couples were oversampled and constitute about three quarters of the data. When weighted, the sample is representative of births in each of the 20 cities (a smaller sample is representative of urban births in all American cities with populations over 200,000. The mean values of variables reported are similar in the two samples). Mothers and fathers were interviewed in the hospital shortly after the birth of the focal child, and follow‐up interviews were conducted when the focal child was approximately 1, 3, 5 and 9 years old (waves 2, 3, 4 and 5 respectively). The FF data are uniquely suited to looking at the short‐term effects of the Great Recession, as the most recent data collection, year 9, occurred between May 2007 and February 2010. We pooled years 5 and 9 (periods 2003–5 and 2007–10 respectively), which are the years before and after the beginning of the Great Recession. Of the almost 5,000 mothers interviewed at baseline, 4,350 were interviewed at year 5, and 3,515 at year 9. Of these 3,500 mothers, a substantial proportion (2,003 women who represent 57% of the sample in year 9) was interviewed in 2009–10, right at the peak of the financial crisis. We focus on these last two waves of data (and exclude years 1 and 3) for two reasons. First, we are interested in examining the impacts of the Great Recession on mother’s health. Second, not all health outcomes were available for all waves.5 After restricting the sample to these two waves and to women with complete information on the outcome variables, our analytic sample includes approximately 3,500 mothers (N varies by the outcome measured).6 We investigate possible differential attrition further below. The outcomes of interest for this study include eight measures of self‐reported physical and mental health, and health behaviour that were obtained from telephone or in‐home interviews, and refer to the last 12 months.7 All measures were constructed as binary indicators that take the value of 1 when a mother reports that she has a given condition and 0 otherwise. We construct binary variables since most of the health questions in the questionnaire ask a mother to either provide a yes/no answer or a categorical response. For the cases in which we have continuous variation in a mother’s health outcome (i.e. BMI), we also explore the association between this outcome and economic conditions. These results are shown in the Extensions section. The following list describes each of the outcomes we investigate. Physical health: (i) Self‐rated health status: ‘excellent’ or ‘very good’ health status versus ‘good’, ‘fair’ or ‘poor’. (ii) Health problem that limits work: has a health problem that limits work or study‐related activities versus no problem. (iii) Obesity: mother’s BMI is equal to or more than 30 versus BMI less than 30. (iv) Health insurance: covered by either a private insurance or Medicaid versus no insurance. Health behaviour: (i) Smokes: smokes cigarettes versus no smoking in the last month. (ii) Binge drinking: drinks 4 or more glasses of alcohol on one occasion versus less than 4 glasses on one occasion or no drinking, in the last year. (iii) Drug use: uses one or more drugs (includes illegal drugs, sedatives, tranquilisers, amphetamines or other)8 ‘on your own’, versus no drug use. By ‘on your own’ is meant either without a doctor’s prescription, in larger amounts than prescribed, or for a longer period than prescribed. Mental health: (i) Depression (screener): respondent could be potentially assessed as depressed9versus not depressed. Although these eight measures are self‐reported and have not been medically verified, they have been widely used in previous studies of population health and have been found to be highly correlated with medically determined health status (Miilunpalo et al., 1997; Currie and Madrian, 1999). Also, the mental health outcome we use in this study is a robust screener for the likelihood of experiencing a psychiatric condition known as a major depressive episode (Kessler et al., 1998). This outcome is constructed based on the short form of the World Health Organisation Composite International Diagnostic Interview (CIDI‐SF) which has been commonly used in large‐scale community surveys to measure depression (Aalto‐Setälä et al., 2002).10 We expect that these measures of health could respond to changes in economic conditions that have occurred in the last 12 months, since previous studies have shown that physical and mental health and health behaviours are sensitive to short‐term changes in unemployment (i.e. monthly UR) (Ruhm and Black, 2002; Ruhm, 2005; Charles and DeCicca, 2008). Even more stable health outcomes like obesity could change over the period of one year when one considers that BMI could change enough to cause the person to cross the obesity threshold (see column 2 in Table 1). In the particular case of smoking, although it is true that few people start smoking after the age of 25, people can restart smoking after this age, and this is actually relatively common. For example, among mothers in FF, we find that 6% of sample has restarted smoking in year 9 after years of non‐smoking. From the perspective of a health production function (Grossman, 1972), it is also reasonable to expect that changes in economic conditions could affect individual health investments as they could have an impact on wages, income or on the opportunity cost of time, which in turn could lead to changes in overall health. Moreover, if we take into account that the Great Recession was deeper and longer than other recessions previously analysed, it is also reasonable to expect that more dramatic changes in the UR are more likely to be associated with changes in health. 2.1. Mother Characteristics and Health Outcomes Table 2 presents weighted summary statistics for all the women in the sample and by race/ethnicity. Descriptive statistics indicate that 62% of the sample report health that is ‘excellent’ or ‘very good’, 10% have a problem that limits their work or study activities, a third are obese and only 81% are covered by health insurance. In terms of health behaviour, 30% of the mothers smoke, 13% drink more than four glasses of alcohol on one occasion (binge drink), and 5% report drug use ‘on their own.’ Almost 15% of the mothers show depressive symptoms on the screener. Comparable figures from the Center for Disease Control and Prevention (2012) indicate that 55% of women in the US have ‘excellent’ or ‘very good’ health (whites 65%, blacks 48% and Hispanics 51%), 30% are obese, 84.4% are covered by health insurance coverage, 17% smoke cigarette, 12% binge drink each month and 11% had at least one major depressive episode (including depressed mood and markedly diminished interest or pleasure in all, or almost all, activities) in the past year.11,12 These numbers suggest that FF women have on average better or similar physical health to the average US woman, worse mental health and higher risk health behaviours.13 Table 2 Summary Statistics in FF Variable . Full . Whites . Blacks . Hispanics . UR > 6% . UR ≤ 6% . Health outcomes Health excellent/very good*† 0.612 0.750 0.547 0.530 0.607 0.613 Health limits Work*†‡ 0.103 0.072 0.130 0.113 0.106 0.101 Obesity*†‡§ 0.320 0.195 0.402 0.386 0.348 0.302 Any health insurance*†‡§ 0.809 0.910 0.861 0.640 0.793 0.820 Smokes*†‡ 0.302 0.369 0.338 0.199 0.295 0.307 ≥4 drinks 1 time last year*†‡ 0.126 0.206 0.083 0.108 0.126 0.127 Drugs use†‡§ 0.053 0.063 0.063 0.039 0.062 0.046 Depressed*‡ 0.132 0.128 0.147 0.130 0.132 0.132 Race/ethnicity White§ 0.284 1.000 0.265 0.298 Black 0.357 1.000 0.351 0.361 Hispanic§ 0.290 1.000 0.308 0.276 Other race 0.070 0.077 0.065 Immigrant†‡§ 0.239 0.073 0.075 0.460 0.263 0.221 Education <HS*†‡§ 0.271 0.116 0.286 0.455 0.284 0.262 HS*†‡ 0.329 0.219 0.436 0.320 0.327 0.331 Some college*†‡ 0.203 0.207 0.236 0.173 0.210 0.197 College or >*†‡§ 0.197 0.457 0.042 0.053 0.180 0.211 Marital status Married*†‡ 0.519 0.818 0.231 0.502 0.517 0.520 Cohabiting*†‡ 0.233 0.114 0.297 0.309 0.234 0.233 Single*†‡ 0.248 0.068 0.472 0.189 0.249 0.247 Age*† 26.9 30.0 24.9 25.6 25.1 25.1 (6.2) (6.1) (5.8) (5.7) (5.9) (6.0) Income‐to‐needs ratio <1*†‡ 0.254 0.056 0.382 0.338 0.263 0.247 1–2*†‡§ 0.276 0.161 0.315 0.329 0.297 0.260 2–4*†‡ 0.136 0.122 0.152 0.148 0.133 0.138 ≥4*†‡§ 0.334 0.661 0.151 0.185 0.306 0.354 Employment status Employed*†‡ 0.478 0.573 0.471 0.400 0.469 0.486 Unemployed*†‡ 0.175 0.070 0.274 0.185 0.171 0.177 Out of labour force*‡ 0.344 0.357 0.252 0.415 0.356 0.336 Migrated since baseline (city):*†‡ 0.204 0.280 0.166 0.203 0.217 0.196 Migrated since baseline (state):*† 0.089 0.125 0.081 0.067 0.093 0.087 Attrited from year 5 to year 9:†‡§ 0.191 0.166 0.172 0.245 0.182 0.194 N pooled sample 7,080 1,446 3,515 1,873 2,748 4,332 N year 5 3,829 773 1,887 1,035 931 2,898 N year 9 3,251 673 1,628 838 1,817 1,434 Variable . Full . Whites . Blacks . Hispanics . UR > 6% . UR ≤ 6% . Health outcomes Health excellent/very good*† 0.612 0.750 0.547 0.530 0.607 0.613 Health limits Work*†‡ 0.103 0.072 0.130 0.113 0.106 0.101 Obesity*†‡§ 0.320 0.195 0.402 0.386 0.348 0.302 Any health insurance*†‡§ 0.809 0.910 0.861 0.640 0.793 0.820 Smokes*†‡ 0.302 0.369 0.338 0.199 0.295 0.307 ≥4 drinks 1 time last year*†‡ 0.126 0.206 0.083 0.108 0.126 0.127 Drugs use†‡§ 0.053 0.063 0.063 0.039 0.062 0.046 Depressed*‡ 0.132 0.128 0.147 0.130 0.132 0.132 Race/ethnicity White§ 0.284 1.000 0.265 0.298 Black 0.357 1.000 0.351 0.361 Hispanic§ 0.290 1.000 0.308 0.276 Other race 0.070 0.077 0.065 Immigrant†‡§ 0.239 0.073 0.075 0.460 0.263 0.221 Education <HS*†‡§ 0.271 0.116 0.286 0.455 0.284 0.262 HS*†‡ 0.329 0.219 0.436 0.320 0.327 0.331 Some college*†‡ 0.203 0.207 0.236 0.173 0.210 0.197 College or >*†‡§ 0.197 0.457 0.042 0.053 0.180 0.211 Marital status Married*†‡ 0.519 0.818 0.231 0.502 0.517 0.520 Cohabiting*†‡ 0.233 0.114 0.297 0.309 0.234 0.233 Single*†‡ 0.248 0.068 0.472 0.189 0.249 0.247 Age*† 26.9 30.0 24.9 25.6 25.1 25.1 (6.2) (6.1) (5.8) (5.7) (5.9) (6.0) Income‐to‐needs ratio <1*†‡ 0.254 0.056 0.382 0.338 0.263 0.247 1–2*†‡§ 0.276 0.161 0.315 0.329 0.297 0.260 2–4*†‡ 0.136 0.122 0.152 0.148 0.133 0.138 ≥4*†‡§ 0.334 0.661 0.151 0.185 0.306 0.354 Employment status Employed*†‡ 0.478 0.573 0.471 0.400 0.469 0.486 Unemployed*†‡ 0.175 0.070 0.274 0.185 0.171 0.177 Out of labour force*‡ 0.344 0.357 0.252 0.415 0.356 0.336 Migrated since baseline (city):*†‡ 0.204 0.280 0.166 0.203 0.217 0.196 Migrated since baseline (state):*† 0.089 0.125 0.081 0.067 0.093 0.087 Attrited from year 5 to year 9:†‡§ 0.191 0.166 0.172 0.245 0.182 0.194 N pooled sample 7,080 1,446 3,515 1,873 2,748 4,332 N year 5 3,829 773 1,887 1,035 931 2,898 N year 9 3,251 673 1,628 838 1,817 1,434 Notes All characteristics are measured at baseline. Sample includes mothers interviewed in years 5 and 9. Numbers are weighted using baseline city weights. Statistically significant differences from t‐tests are noted as follows: *whites versus blacks; †whites versus Hispanics; ‡blacks versus Hispanics; and §low UR versus high UR. Open in new tab Table 2 Summary Statistics in FF Variable . Full . Whites . Blacks . Hispanics . UR > 6% . UR ≤ 6% . Health outcomes Health excellent/very good*† 0.612 0.750 0.547 0.530 0.607 0.613 Health limits Work*†‡ 0.103 0.072 0.130 0.113 0.106 0.101 Obesity*†‡§ 0.320 0.195 0.402 0.386 0.348 0.302 Any health insurance*†‡§ 0.809 0.910 0.861 0.640 0.793 0.820 Smokes*†‡ 0.302 0.369 0.338 0.199 0.295 0.307 ≥4 drinks 1 time last year*†‡ 0.126 0.206 0.083 0.108 0.126 0.127 Drugs use†‡§ 0.053 0.063 0.063 0.039 0.062 0.046 Depressed*‡ 0.132 0.128 0.147 0.130 0.132 0.132 Race/ethnicity White§ 0.284 1.000 0.265 0.298 Black 0.357 1.000 0.351 0.361 Hispanic§ 0.290 1.000 0.308 0.276 Other race 0.070 0.077 0.065 Immigrant†‡§ 0.239 0.073 0.075 0.460 0.263 0.221 Education <HS*†‡§ 0.271 0.116 0.286 0.455 0.284 0.262 HS*†‡ 0.329 0.219 0.436 0.320 0.327 0.331 Some college*†‡ 0.203 0.207 0.236 0.173 0.210 0.197 College or >*†‡§ 0.197 0.457 0.042 0.053 0.180 0.211 Marital status Married*†‡ 0.519 0.818 0.231 0.502 0.517 0.520 Cohabiting*†‡ 0.233 0.114 0.297 0.309 0.234 0.233 Single*†‡ 0.248 0.068 0.472 0.189 0.249 0.247 Age*† 26.9 30.0 24.9 25.6 25.1 25.1 (6.2) (6.1) (5.8) (5.7) (5.9) (6.0) Income‐to‐needs ratio <1*†‡ 0.254 0.056 0.382 0.338 0.263 0.247 1–2*†‡§ 0.276 0.161 0.315 0.329 0.297 0.260 2–4*†‡ 0.136 0.122 0.152 0.148 0.133 0.138 ≥4*†‡§ 0.334 0.661 0.151 0.185 0.306 0.354 Employment status Employed*†‡ 0.478 0.573 0.471 0.400 0.469 0.486 Unemployed*†‡ 0.175 0.070 0.274 0.185 0.171 0.177 Out of labour force*‡ 0.344 0.357 0.252 0.415 0.356 0.336 Migrated since baseline (city):*†‡ 0.204 0.280 0.166 0.203 0.217 0.196 Migrated since baseline (state):*† 0.089 0.125 0.081 0.067 0.093 0.087 Attrited from year 5 to year 9:†‡§ 0.191 0.166 0.172 0.245 0.182 0.194 N pooled sample 7,080 1,446 3,515 1,873 2,748 4,332 N year 5 3,829 773 1,887 1,035 931 2,898 N year 9 3,251 673 1,628 838 1,817 1,434 Variable . Full . Whites . Blacks . Hispanics . UR > 6% . UR ≤ 6% . Health outcomes Health excellent/very good*† 0.612 0.750 0.547 0.530 0.607 0.613 Health limits Work*†‡ 0.103 0.072 0.130 0.113 0.106 0.101 Obesity*†‡§ 0.320 0.195 0.402 0.386 0.348 0.302 Any health insurance*†‡§ 0.809 0.910 0.861 0.640 0.793 0.820 Smokes*†‡ 0.302 0.369 0.338 0.199 0.295 0.307 ≥4 drinks 1 time last year*†‡ 0.126 0.206 0.083 0.108 0.126 0.127 Drugs use†‡§ 0.053 0.063 0.063 0.039 0.062 0.046 Depressed*‡ 0.132 0.128 0.147 0.130 0.132 0.132 Race/ethnicity White§ 0.284 1.000 0.265 0.298 Black 0.357 1.000 0.351 0.361 Hispanic§ 0.290 1.000 0.308 0.276 Other race 0.070 0.077 0.065 Immigrant†‡§ 0.239 0.073 0.075 0.460 0.263 0.221 Education <HS*†‡§ 0.271 0.116 0.286 0.455 0.284 0.262 HS*†‡ 0.329 0.219 0.436 0.320 0.327 0.331 Some college*†‡ 0.203 0.207 0.236 0.173 0.210 0.197 College or >*†‡§ 0.197 0.457 0.042 0.053 0.180 0.211 Marital status Married*†‡ 0.519 0.818 0.231 0.502 0.517 0.520 Cohabiting*†‡ 0.233 0.114 0.297 0.309 0.234 0.233 Single*†‡ 0.248 0.068 0.472 0.189 0.249 0.247 Age*† 26.9 30.0 24.9 25.6 25.1 25.1 (6.2) (6.1) (5.8) (5.7) (5.9) (6.0) Income‐to‐needs ratio <1*†‡ 0.254 0.056 0.382 0.338 0.263 0.247 1–2*†‡§ 0.276 0.161 0.315 0.329 0.297 0.260 2–4*†‡ 0.136 0.122 0.152 0.148 0.133 0.138 ≥4*†‡§ 0.334 0.661 0.151 0.185 0.306 0.354 Employment status Employed*†‡ 0.478 0.573 0.471 0.400 0.469 0.486 Unemployed*†‡ 0.175 0.070 0.274 0.185 0.171 0.177 Out of labour force*‡ 0.344 0.357 0.252 0.415 0.356 0.336 Migrated since baseline (city):*†‡ 0.204 0.280 0.166 0.203 0.217 0.196 Migrated since baseline (state):*† 0.089 0.125 0.081 0.067 0.093 0.087 Attrited from year 5 to year 9:†‡§ 0.191 0.166 0.172 0.245 0.182 0.194 N pooled sample 7,080 1,446 3,515 1,873 2,748 4,332 N year 5 3,829 773 1,887 1,035 931 2,898 N year 9 3,251 673 1,628 838 1,817 1,434 Notes All characteristics are measured at baseline. Sample includes mothers interviewed in years 5 and 9. Numbers are weighted using baseline city weights. Statistically significant differences from t‐tests are noted as follows: *whites versus blacks; †whites versus Hispanics; ‡blacks versus Hispanics; and §low UR versus high UR. Open in new tab Women’s characteristics were all measured at baseline.14 On average, mothers in FF are 27 at the time of childbirth, a third of the sample is white and a third is African American, 60% have a high school education or less, half are married, more than half are poor or near poor (as shown by an income‐to‐needs‐ratio that is below 200%) and 50% are employed. Migration across states is relatively uncommon. For example, less than 9% of the sample has migrated across states (while 20% have migrated across cities). The unmarried and married samples are representative of out‐of‐wedlock births and married births, respectively, in 20 large US urban areas (Reichman et al., 2001). Differences by race/ethnicity indicate that whites are more educated, more likely to be married, wealthier and have a higher probability of being employed than black or Hispanic mothers. Whites also report a higher probability of migration than minorities across states (12.5% versus less than 10%). In terms of their health outcomes, whites are in better physical health (75% have health that is excellent or very good and less than a fifth are obese) and they have better mental health than Hispanic mothers. Moreover, Hispanic and black mothers are less likely to report that they smoke and drink, and Hispanics are less likely to use drugs compared to whites and blacks. All these differences are significant at the 0.95 level. In columns 5 and 6 of Table 2, we split the sample by low versus high unemployment rates with the cut‐off being 6% (the average unemployment rate for the period and states of interest in this study). The most striking difference between mothers living in areas with high unemployment and other mothers, is that they are less likely to be white and more likely to be immigrant and poor. They are also more likely to suffer from obesity and less likely to have health insurance compared to other mothers. These differences are significant at the 0.95 level. In sum, the differences in the raw data point to the importance of controlling for differences in the baseline characteristics of mothers in different areas in order to identify the effects of unemployment on health outcomes. 2.2. Economic Conditions: State Unemployment Rate We obtained data on the state unemployment rate from the Bureau of Labor Statistics’ Local Area Unemployment Statistics (LAUS).15 We constructed an average unemployment rate (UR) over the year prior to the date of a mother’s interview, in order to match our key dependent variables which are health measures over the previous year. The UR was appended to the data based on a mother’s baseline state of residence (the state in which she was initially sampled at her child’s birth) and her date of interview, for both years 5 and 9. We used the state in which she was initially sampled in order to control for the possibility of endogenous migration in response to changes in unemployment rates. Figure 1 shows the large variation in the unemployment rate in all 15 baseline states included in FF for the period 2000 to 2010, and in particular after 2007 when the Great Recession started.16 Fig. 1. Open in new tabDownload slide State Unemployment Rate (%) During Interview Note. Sample includes the 15 baseline states in FF. Fig. 1. Open in new tabDownload slide State Unemployment Rate (%) During Interview Note. Sample includes the 15 baseline states in FF. Table 3 The Effect of the UR on Mothers’ Health in FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . State UR LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) % change in health outcome due to a 1 pp increase in UR −2.9 −0.9 1.3 −0.3 5.6 8.0 2.9 −0.2 LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 City UR LOGIT 0.916 1.058 1.025 0.956 1.088 1.062 1.128 0.994 (−1.951) (1.365) (1.237) (−0.971) (1.790) (1.339) (1.576) (−0.107) % change −3.8 6.1 1.6 −0.9 5.4 4.1 12.3 −0.2 LOGIT‐FE 0.880 1.154 1.038 1.002 1.295 1.151 1.394 0.938 (−2.112) (1.451) (0.332) (0.030) (2.650) (1.640) (2.738) (−0.851) % change −4.2 7.3 1.9 0.1 4.5 5.4 9.8 −4.4 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . State UR LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) % change in health outcome due to a 1 pp increase in UR −2.9 −0.9 1.3 −0.3 5.6 8.0 2.9 −0.2 LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 City UR LOGIT 0.916 1.058 1.025 0.956 1.088 1.062 1.128 0.994 (−1.951) (1.365) (1.237) (−0.971) (1.790) (1.339) (1.576) (−0.107) % change −3.8 6.1 1.6 −0.9 5.4 4.1 12.3 −0.2 LOGIT‐FE 0.880 1.154 1.038 1.002 1.295 1.151 1.394 0.938 (−2.112) (1.451) (0.332) (0.030) (2.650) (1.640) (2.738) (−0.851) % change −4.2 7.3 1.9 0.1 4.5 5.4 9.8 −4.4 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Notes Each coefficient comes from a separate regression. Logit models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and baseline state (city) and year fixed‐effects; errors are clustered at the baseline state (city) level (see (1)). Logit‐FE models control for year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Predicted per cent change in health outcome associated with a percentage point increase in the unemployment rate in year 9. Open in new tab Table 3 The Effect of the UR on Mothers’ Health in FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . State UR LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) % change in health outcome due to a 1 pp increase in UR −2.9 −0.9 1.3 −0.3 5.6 8.0 2.9 −0.2 LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 City UR LOGIT 0.916 1.058 1.025 0.956 1.088 1.062 1.128 0.994 (−1.951) (1.365) (1.237) (−0.971) (1.790) (1.339) (1.576) (−0.107) % change −3.8 6.1 1.6 −0.9 5.4 4.1 12.3 −0.2 LOGIT‐FE 0.880 1.154 1.038 1.002 1.295 1.151 1.394 0.938 (−2.112) (1.451) (0.332) (0.030) (2.650) (1.640) (2.738) (−0.851) % change −4.2 7.3 1.9 0.1 4.5 5.4 9.8 −4.4 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . State UR LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) % change in health outcome due to a 1 pp increase in UR −2.9 −0.9 1.3 −0.3 5.6 8.0 2.9 −0.2 LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 City UR LOGIT 0.916 1.058 1.025 0.956 1.088 1.062 1.128 0.994 (−1.951) (1.365) (1.237) (−0.971) (1.790) (1.339) (1.576) (−0.107) % change −3.8 6.1 1.6 −0.9 5.4 4.1 12.3 −0.2 LOGIT‐FE 0.880 1.154 1.038 1.002 1.295 1.151 1.394 0.938 (−2.112) (1.451) (0.332) (0.030) (2.650) (1.640) (2.738) (−0.851) % change −4.2 7.3 1.9 0.1 4.5 5.4 9.8 −4.4 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Notes Each coefficient comes from a separate regression. Logit models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and baseline state (city) and year fixed‐effects; errors are clustered at the baseline state (city) level (see (1)). Logit‐FE models control for year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Predicted per cent change in health outcome associated with a percentage point increase in the unemployment rate in year 9. Open in new tab 2.3. Control Variables In models without maternal fixed‐effects, we included a number of basic socio‐economic and demographic characteristics of the mother that were measured at baseline. These measures include dummy variables for mother’s age (<20, 20–23, 24–27, 28–32, 33+), race/ethnicity (white, black, Hispanic and other race/ethnicity), education (less than high school, high school, some college and college or more), immigrant status, marital/relationship status (married, cohabiting and single), income (we use four categories of income‐to‐needs ratio17: poor is less than 1; near poor is income between 1 and less than 2; middle income is between 2 and less than 4; and high income is 4 or more), and child’s age (in months). 3. Methods We estimate the effect of the UR on mother’s health using two logistic models, one that pools data from years 5 and 9 and controls for a rich set of covariates and year and state fixed‐effects, and a second one that accounts for time‐invariant mother fixed‐effects. The following equation describes the first model: Yi,t=β0+β1URi,t+β2Xi,t−1+αs+αt+ϵi,t,(1) where Yi,t denotes mother i’s health outcome measured at time t, UR is the average unemployment rate in baseline states over the last year t from the date of interview, X is a matrix of mother characteristics measured at baseline (described above) and αs and αt are vectors of dummies for baseline state and year respectively. The baseline state dummies control for any time‐invariant state‐level factors that are correlated with both state economic conditions and women’s health. The year dummies will absorb year‐specific factors that could affect both the economy and mother’s health; ε is the disturbance term. All models are clustered at the baseline state level to account for within‐state correlation in the observations. The coefficient of interest is β1. The second logistic model controls for mother‐specific fixed‐effects and is estimated using (2). The only covariate included in this model is αt, the interview year dummy. Yi,t=βi+β1URi,t+αt+ϵi,t.(2) This model exploits the longitudinal nature of FF by including a mother‐specific fixed effect, βi, to control for observed and unobserved time‐invariant characteristics of the mother, which may be correlated with both residing in a state with high UR and experiencing health problems. For instance, if a mother belongs to a demographic group that is likely to be particularly impacted by unemployment, she may also be more likely to suffer from health problems. We estimate separate logistic fixed‐effects models by subgroups. We stratify the sample by white, blacks and Hispanics; married versus unmarried women; and mothers with a high school degree or less versus those with more than a high school degree. We do these separate analyses because we expect to find heterogeneous impacts across groups and, in particular, we hypothesise that the most disadvantaged women (minorities, unmarried and the least educated) will fare worse during the Great Recession than more advantaged women, because they are less likely to be able to insure themselves against contingencies. 4. Results 4.1. Effects of The UR Table 3 presents results from the pooled logistic and logistic fixed‐effects models of the impacts of state unemployment rate on health and health behaviour. We only report the coefficient of interest, β1, and when this coefficient is statistically significant at least at the 95% level of confidence, we show it in bold type. Under each individual estimate, we report the percentage change in the outcome that is associated with a one percentage point increase in the unemployment rate and we refer to these values to express the magnitude of the effects. The logistic estimates (1) shown in the first row, with one exception (depression), suggest that health gets worse as unemployment increases, but none of the coefficients are significantly different from zero at the 0.95 level of confidence. Self‐reported health status and binge drinking are significant at the 0.90 level. While not shown in the regressions due to space limitations, a few covariates are significantly associated with health outcomes in the pooled logistic models. Women with high levels of education report better health outcomes than those with less than a high school degree. Single and cohabiting women have significantly worse health and health behaviours than those who are married. An increase in the income‐to‐needs ratio measured at baseline is significantly associated with an increase in health status as well as with an increase in substance use. The second row of Table 3 shows models that control for individual fixed‐effects. These estimates are remarkably similar in size to those obtained from the logistic models, but are more precisely estimated. The estimates confirm that as the economy worsens, women’s physical health declines and health‐compromising behaviours increase. During the recession, a one percentage point increase in the unemployment rate was associated with a decrease in the probability of experiencing ‘excellent’ or ‘very good’ physical health by 4.3% and an increase in smoking or using drugs by 5.1% and 15.2% respectively. These effects are larger than those of Davalos and French (2011) who focus on the 2001 recession (recession in which the UR went from 4.5. to 5.5%), and found that a 1 percentage point increase in the UR reduced overall physical health by 0.9%. It is possible that the larger effects are due to the much more massive scale of the recession. No effects are observed on the probability of having health insurance. This result is consistent with Cawley et al. (2011), who also find no effect on the probability of health insurance for both the working‐age population and for the sample of women with children.18 Table 3 also shows that the unemployment rate had no effect on obesity.19 Previous studies have found mixed evidence on obesity (Ruhm, 2000, 2005; Charles and DeCicca, 2008), however, these studies have not examined the impacts of the UR on women. Moreover, no effects were observed on the probability of being depressed.20 Previous research has measured mental health with individual measures of self‐rated feelings of sadness, hopelessness, or worthlessness, or with more extreme measures such as suicides. The CIDI‐SF uses information about a list of different symptoms and their specific durations, and is used to determine a probable diagnosis of the psychiatric condition known as a major depressive episode. The fact that we do not observe an effect on this depression screener for the whole sample should not be seen as inconsistent with previous studies. For instance, a recent paper showed that while the 2008 stock market crash, which led to huge losses in wealth for many households, caused immediate declines in subjective measures of mental health, it did not increase validated measures of depressive symptoms or indicators of depression (McInerney et al., 2013). Moreover, this finding could reflect the fact that the effects of unemployment on mental health are not equally distributed across groups defined by gender, marital status and education, a hypothesis we pursue further below. The bottom panel of Table 3 shows estimates of the UR at the city level. Using the LAUS data, we construct a measure of the average unemployment rate in the mother’s original baseline city. We employ the city unemployment rate because it may be a more accurate representation of a woman’s own labour market opportunities. Results are highly consistent with those obtained using the state‐level UR. For example, a 1 percentage point increase in the city unemployment rate is associated with a 4.2% decrease in probability of having ‘excellent’ or ‘very good’ health (versus a 4.3% decline when we use the state UR), a 4.5% increase in smoking (versus 5.1%) and a 9.8% rise in drug use (versus 15.1%). For this reason and because: (i) the state unemployment rate may be more salient to a woman when she is forming her perception of economic conditions; (ii) measurement error, selective migration and selective attrition may be more likely to be problematic when focusing on local area (city) unemployment rates; and (iii) most studies have employed the state unemployment rate to measure effects on health, in what follows we focus the discussion on results that use the state UR rather than the city UR. 4.2. Heterogeneous Effects Table 3 presents the overall effects of the Great Recession. In what follows we examine differences by race/ethnicity, marital status and education groups. We present only the logistic‐fixed‐effects models since these provide the more reliable estimates and under the coefficients of the unemployment rate, we show the corresponding percentage changes in the outcome associated with a one percentage point increase in the UR. We provide a brief discussion of these results after presenting the findings. Table 4 shows the effects of the UR for the whole sample of mothers and by racial/ethnicity groups (white, black and Hispanic), by marital status (married and unmarried) and by education levels (mothers with a high school degree or less, and those with more than a high school degree). The estimates reveal significant differences in the effects of UR on women’s health across subpopulations. In general more disadvantaged mothers – minorities, unmarried and the less educated – were likely to suffer negative health impacts while more advantaged women actually experienced health improvements in certain dimensions. Table 4 Logit‐FE Estimates of Effects of State UR by Groups Using FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.848 1.073 1.087 0.993 1.256 1.14 1.4 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 White 0.909 0.939 0.508 1.034 1.512 1.594 1.23 0.663 (−0.691) (−0.252) (−2.091) (0.221) (1.571) (2.535) (0.759) (−2.402) % change −1.4 −2.2 −4.5 1.2 5.1 4.7 1.1 −11.1 Black 0.687 1.31 1.358 0.848 1.227 1.148 1.703 0.865 (−3.009) (1.532) (1.312) (−1.165) (1.121) (0.672) (2.456) (−1.002) % change −9.1 11.9 2.7 −1.9 3.6 11.5 10.1 −8.0 Hispanic 0.933 1.157 1.151 1.061 1.06 1.073 1.902 1.301 (−0.781) (0.792) (0.850) (0.651) (0.341) (0.564) (1.602) (1.982) % change −2.0 9.0 4.6 2.2 6.1 0.8 12.8 18.2 Married 1.054 0.663 0.761 1.064 0.903 1.079 1.656 0.596 (0.342) (−1.245) (−0.993) (0.334) (−0.321) (0.331) (1.340) (−2.371) % change 0.1 −7.0 −1.4 1.7 −0.1 5.3 13.3 −8.4 Unmarried 0.811 1.146 1.197 0.964 1.31 1.128 1.292 1.018 (−2.940) (1.191) (1.331) (−0.520) (2.462) (1.291) (1.732) (0.211) % change −5.7 9.9 3.2 −0.7 5.6 6.2 11.8 0.2 More than HS 0.858 0.566 1.16 0.872 1.655 1.116 1.4 0.771 (−1.301) (−2.274) (0.451) (−1.147) (2.119) (0.742) (1.291) (−1.950) % change −4.0 −6.6 1.0 −2.1 11.8 3.7 12.2 −3.8 HS or less 0.856 1.364 1.127 1.047 1.144 1.162 1.413 1.062 (−1.971) (2.353) (0.916) (0.589) (1.164) (1.391) (2.144) (0.601) % change −4.5 19.1 4.9 1.1 2.9 8.5 14.8 2.7 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.848 1.073 1.087 0.993 1.256 1.14 1.4 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 White 0.909 0.939 0.508 1.034 1.512 1.594 1.23 0.663 (−0.691) (−0.252) (−2.091) (0.221) (1.571) (2.535) (0.759) (−2.402) % change −1.4 −2.2 −4.5 1.2 5.1 4.7 1.1 −11.1 Black 0.687 1.31 1.358 0.848 1.227 1.148 1.703 0.865 (−3.009) (1.532) (1.312) (−1.165) (1.121) (0.672) (2.456) (−1.002) % change −9.1 11.9 2.7 −1.9 3.6 11.5 10.1 −8.0 Hispanic 0.933 1.157 1.151 1.061 1.06 1.073 1.902 1.301 (−0.781) (0.792) (0.850) (0.651) (0.341) (0.564) (1.602) (1.982) % change −2.0 9.0 4.6 2.2 6.1 0.8 12.8 18.2 Married 1.054 0.663 0.761 1.064 0.903 1.079 1.656 0.596 (0.342) (−1.245) (−0.993) (0.334) (−0.321) (0.331) (1.340) (−2.371) % change 0.1 −7.0 −1.4 1.7 −0.1 5.3 13.3 −8.4 Unmarried 0.811 1.146 1.197 0.964 1.31 1.128 1.292 1.018 (−2.940) (1.191) (1.331) (−0.520) (2.462) (1.291) (1.732) (0.211) % change −5.7 9.9 3.2 −0.7 5.6 6.2 11.8 0.2 More than HS 0.858 0.566 1.16 0.872 1.655 1.116 1.4 0.771 (−1.301) (−2.274) (0.451) (−1.147) (2.119) (0.742) (1.291) (−1.950) % change −4.0 −6.6 1.0 −2.1 11.8 3.7 12.2 −3.8 HS or less 0.856 1.364 1.127 1.047 1.144 1.162 1.413 1.062 (−1.971) (2.353) (0.916) (0.589) (1.164) (1.391) (2.144) (0.601) % change −4.5 19.1 4.9 1.1 2.9 8.5 14.8 2.7 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 Notes Each coefficient comes from a separate regression Logit‐FE models control for year fixed‐effects (see (2))). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Predicted percent change in health outcome associated with a percentage point increase in the unemployment rate in year 9. Open in new tab Table 4 Logit‐FE Estimates of Effects of State UR by Groups Using FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.848 1.073 1.087 0.993 1.256 1.14 1.4 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 White 0.909 0.939 0.508 1.034 1.512 1.594 1.23 0.663 (−0.691) (−0.252) (−2.091) (0.221) (1.571) (2.535) (0.759) (−2.402) % change −1.4 −2.2 −4.5 1.2 5.1 4.7 1.1 −11.1 Black 0.687 1.31 1.358 0.848 1.227 1.148 1.703 0.865 (−3.009) (1.532) (1.312) (−1.165) (1.121) (0.672) (2.456) (−1.002) % change −9.1 11.9 2.7 −1.9 3.6 11.5 10.1 −8.0 Hispanic 0.933 1.157 1.151 1.061 1.06 1.073 1.902 1.301 (−0.781) (0.792) (0.850) (0.651) (0.341) (0.564) (1.602) (1.982) % change −2.0 9.0 4.6 2.2 6.1 0.8 12.8 18.2 Married 1.054 0.663 0.761 1.064 0.903 1.079 1.656 0.596 (0.342) (−1.245) (−0.993) (0.334) (−0.321) (0.331) (1.340) (−2.371) % change 0.1 −7.0 −1.4 1.7 −0.1 5.3 13.3 −8.4 Unmarried 0.811 1.146 1.197 0.964 1.31 1.128 1.292 1.018 (−2.940) (1.191) (1.331) (−0.520) (2.462) (1.291) (1.732) (0.211) % change −5.7 9.9 3.2 −0.7 5.6 6.2 11.8 0.2 More than HS 0.858 0.566 1.16 0.872 1.655 1.116 1.4 0.771 (−1.301) (−2.274) (0.451) (−1.147) (2.119) (0.742) (1.291) (−1.950) % change −4.0 −6.6 1.0 −2.1 11.8 3.7 12.2 −3.8 HS or less 0.856 1.364 1.127 1.047 1.144 1.162 1.413 1.062 (−1.971) (2.353) (0.916) (0.589) (1.164) (1.391) (2.144) (0.601) % change −4.5 19.1 4.9 1.1 2.9 8.5 14.8 2.7 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.848 1.073 1.087 0.993 1.256 1.14 1.4 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) % change −4.3 7.3 2.4 −0.1 5.1 6.9 15.2 −3.4 White 0.909 0.939 0.508 1.034 1.512 1.594 1.23 0.663 (−0.691) (−0.252) (−2.091) (0.221) (1.571) (2.535) (0.759) (−2.402) % change −1.4 −2.2 −4.5 1.2 5.1 4.7 1.1 −11.1 Black 0.687 1.31 1.358 0.848 1.227 1.148 1.703 0.865 (−3.009) (1.532) (1.312) (−1.165) (1.121) (0.672) (2.456) (−1.002) % change −9.1 11.9 2.7 −1.9 3.6 11.5 10.1 −8.0 Hispanic 0.933 1.157 1.151 1.061 1.06 1.073 1.902 1.301 (−0.781) (0.792) (0.850) (0.651) (0.341) (0.564) (1.602) (1.982) % change −2.0 9.0 4.6 2.2 6.1 0.8 12.8 18.2 Married 1.054 0.663 0.761 1.064 0.903 1.079 1.656 0.596 (0.342) (−1.245) (−0.993) (0.334) (−0.321) (0.331) (1.340) (−2.371) % change 0.1 −7.0 −1.4 1.7 −0.1 5.3 13.3 −8.4 Unmarried 0.811 1.146 1.197 0.964 1.31 1.128 1.292 1.018 (−2.940) (1.191) (1.331) (−0.520) (2.462) (1.291) (1.732) (0.211) % change −5.7 9.9 3.2 −0.7 5.6 6.2 11.8 0.2 More than HS 0.858 0.566 1.16 0.872 1.655 1.116 1.4 0.771 (−1.301) (−2.274) (0.451) (−1.147) (2.119) (0.742) (1.291) (−1.950) % change −4.0 −6.6 1.0 −2.1 11.8 3.7 12.2 −3.8 HS or less 0.856 1.364 1.127 1.047 1.144 1.162 1.413 1.062 (−1.971) (2.353) (0.916) (0.589) (1.164) (1.391) (2.144) (0.601) % change −4.5 19.1 4.9 1.1 2.9 8.5 14.8 2.7 N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 Notes Each coefficient comes from a separate regression Logit‐FE models control for year fixed‐effects (see (2))). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Predicted percent change in health outcome associated with a percentage point increase in the unemployment rate in year 9. Open in new tab Results by race/ethnicity indicate two patters that are: (i) minorities faced more pronounced declines in their physical and mental health compared to whites and (ii) whites experienced, at least in some respects, improvements in their health. As the unemployment rate increased, white women were less likely to be obese (the probability declined by 4.5%) and to report feelings of depression (the probability decreased by 11.1%). Whites were also 4.7% more likely to binge drink as the economy deteriorated. The estimates for African Americans (shown in the third row of Table 4) indicate that for each percentage point that the UR increased the probability of having ‘excellent’ or ‘very good’ health fell by 9.1% and that for using drugs rose by 10.1%. Hispanics also show a marginal increase in drug use and a significant deterioration in mental health (the probability of being depressed increased by 18.2%). This last result contradicts that found in Tekin et al. (2013), in which the Hispanic populations showed an improvement in mental health when state employment rate declined. We now examine differences by marital status. We exploit the fact that the Fragile Families data set oversamples births to unwed parents, and as a result, it is possible to study differences by mother’s relationship status (married versus unmarried), which is usually difficult to examine in other surveys. The findings indicate that unmarried mothers were hard hit by the Great Recession, whereas it may have actually improved the mental health of married mothers. Logistic fixed‐effects estimates show that a percentage point rise in the UR was associated with a decrease in the probability of being depressed among married women (by 8.4%), whereas unmarried women were 5.7% less likely to have ‘excellent’ or ‘very good’ health and were more likely to adopt health compromising behaviours (the probability of smoking rose by a significant 5.6%). Finally, results by education indicate that more educated women suffered less during the Great Recession as they were less likely to have problems that limited their work‐related activities (the probability fell by 6.6% per one percentage point increase in unemployment) and were less likely to be depressed (a 3.8% reduction in this probability, although only significant at the 90% level of confidence). However, more educated women were also more likely to smoke (experiencing an 11.8% rise in their probability). Mothers with a high school degree or less on the other hand, faced a significant decline in their physical health as they were more likely to report ‘good’, ‘fair’ or ‘poor’ health (4.5%) and more likely to have had problems that limited their work (the probability increased by 19.1%). In terms of health behaviour, less‐educated women faced a significant increase in drug use (14.8%). The most surprising aspect of the results discussed above is that white, highly educated and married women appear to suffer less from depression when the unemployment rate rises. A possible explanation is that groups with relatively low unemployment or risk of spousal unemployment feel themselves to be relatively better off in bad times. Of course these more advantaged women also drank and smoke more with high unemployment. It is possible that this finding reflects within group heterogeneity. For example, it could be that within the group of more educated mothers, a small minority of women increased their smoking and drinking enough to affect the group mean. We compare the results shown in Table 4 to those in previous literature and we confirm that even differences across subgroups were larger during the Great Recession. For example, while we found that a 1 percentage point increase in the state UR reduced the probability of having ‘excellent’ or ‘very good’ health by 9.5% for African Americans, Davalos and French (2011) estimate a 1.2% reduction. Moreover, among more educated individuals our results show a non‐significant 3.6% decline in physical health, while they find a 0.9% decrease. 5. Extensions 5.1. Heterogeneity in the Timing of the Great Recession In this Section, we ask whether the impacts of the Great Recession can be identified in the subsample of mothers who were interviewed for the last wave of the data after 2008, the year in which the Great Recession had already hit the economy. This group was definitely exposed to the crisis. This subsample includes 2,003 women (1,866 were interviewed in 2009 and 137 in 2010, representing 57% of the sample in year 9), of which 489 were married at their child’s birth. We estimate models 1 and 2 for this group of mothers and we find substantially similar effects of the UR on their health and health behaviour, although the effects are less precisely estimated than in the whole sample of women. Appendix Table A1 shows these results. 5.2. Heterogeneity in The Sample of States We now explore whether the impacts of the UR could be driven by certain states, for example larger states such as California or Texas that together represent 30% of the sample, or states that experienced the effects of the crisis more strongly such as Michigan or Ohio (i.e. the average unemployment rate for these two states, in the period of interest, is 7.5% while for the full sample it is 5.9%). We found no evidence of this. Estimating our baseline regressions in different subsamples provides estimates that were consistent in size and direction to the effects shown in Table 3, but with relatively weaker power. These results are shown in Appendix Table A2. 5.3. Using Discrete Versus Continuous Health Outcomes Since logistic fixed‐effects models are only identified by mothers who change their health status across waves, cases in which a mother experiences little change in her latent health condition (and for whom the change is not enough to generate a move from one ‘status’ to another), are discarded. In this Section, we ask whether our results are robust to including these cases. We do this by investigating whether a mother’s BMI – a more sensitive measure than obesity that captures both small and large changes in weight – could be affected by the unemployment rate. BMI increased substantially in the four years between the waves, from 27.1 to 29.2 (an increase of approx. 8%), while obesity increased from 27.9% to 37.1% (an increase of approx. 33%).21 Results are shown in Appendix Table A3 and they indicate that, although the UR is positively associated with changes in mother’s BMI, the coefficient is not statistically significant. This finding is consistent with the result we found on mother’s obesity – a positive but non‐significant effect of the UR. 5.4. Other Measures of Economic Fluctuations: Employment‐to‐population Ratio Unemployed workers who grow discouraged in their job search and do not actively participate in the labour market are not officially counted as unemployed. Hence, reductions in the unemployment rate may sometimes overstate improvements in the labour market. Alternatively, the unemployment rate may remain high even as employment is rising if discouraged workers come back to the labour market. Thus, in order to capture fluctuations in the labour market more adequately, we also investigate how the state employment‐to‐population ratio (ER) has affected women’s health. The ER is defined as the number of employed workers as a proportion of the total population aged 18–64 in a given state. We constructed an annual average ER measure using employment data from the LAUS that come from the Current Population Survey, and we appended it to FF data based on a mother’s baseline state of residence and her date of interview (see footnote 15). Appendix Table A4 shows logistic fixed‐effects estimates of the effects of the state employment‐to‐population ratio on health outcomes. We find consistent but weaker estimates compared to those obtained when using the state unemployment rate. That is, as the economy expands, women’s physical health tends to improve and substance use declines. We also find heterogeneous impacts across demographic groups, indicating that the positive effects of economic recovery (an increase in ER) are mostly experienced by minority, unmarried and less‐educated mothers as they are more likely to have improvements in their physical and mental health as well as a decrease in the odds of using of drugs. Table A4 Logit‐FE Estimates of Effects of State ER Using FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 1.043 0.995 0.924 1.023 0.956 0.919 0.902 1.015 (1.164) (−0.09) (−1.191) (0.530) (−0.774) (−1.365) (−1.576) (0.341) White 0.812 1.342 0.927 1.030 0.961 0.800 0.920 1.430 (−1.700) (1.708) (−0.331) (0.238) (−0.265) (−1.862) (−0.531) (2.611) Black 1.006 0.967 0.975 1.081 0.983 1.022 0.873 1.021 (0.142) (−0.492) (−0.312) (1.396) (−0.228) (0.261) (−1.676) (0.352) Hispanic 1.043 0.995 0.821 0.835 1.044 0.878 1.009 0.706 (1.155) (−0.094) (−1.142) (−1.844) (0.249) (−1.075) (0.031) (−2.764) Married 0.932 1.045 0.783 0.877 1.075 0.843 – 1.278 (−0.857) (0.337) (−1.292) (−1.183) (−0.421) (−1.261) (2.004) Unmarried 1.070 0.990 0.940 1.062 0.930 0.961 0.874 0.981 (1.643) (−0.165) (−0.863) (1.281) (−1.132) (−0.660) (−1.772) (−0.381) More than HS 0.963 1.284 1.006 0.999 0.995 0.891 0.966 1.291 (−0.588) (2.279) (0.043) (−0.013) (−0.04) (−1.190) (0.281) (2.742) HS or less 1.080 0.899 0.895 1.031 0.941 0.953 0.871 0.934 (1.714) (−1.599) (−1.439) (0.621) (−0.904) (−0.718) (0.070) (−1.241) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 1.043 0.995 0.924 1.023 0.956 0.919 0.902 1.015 (1.164) (−0.09) (−1.191) (0.530) (−0.774) (−1.365) (−1.576) (0.341) White 0.812 1.342 0.927 1.030 0.961 0.800 0.920 1.430 (−1.700) (1.708) (−0.331) (0.238) (−0.265) (−1.862) (−0.531) (2.611) Black 1.006 0.967 0.975 1.081 0.983 1.022 0.873 1.021 (0.142) (−0.492) (−0.312) (1.396) (−0.228) (0.261) (−1.676) (0.352) Hispanic 1.043 0.995 0.821 0.835 1.044 0.878 1.009 0.706 (1.155) (−0.094) (−1.142) (−1.844) (0.249) (−1.075) (0.031) (−2.764) Married 0.932 1.045 0.783 0.877 1.075 0.843 – 1.278 (−0.857) (0.337) (−1.292) (−1.183) (−0.421) (−1.261) (2.004) Unmarried 1.070 0.990 0.940 1.062 0.930 0.961 0.874 0.981 (1.643) (−0.165) (−0.863) (1.281) (−1.132) (−0.660) (−1.772) (−0.381) More than HS 0.963 1.284 1.006 0.999 0.995 0.891 0.966 1.291 (−0.588) (2.279) (0.043) (−0.013) (−0.04) (−1.190) (0.281) (2.742) HS or less 1.080 0.899 0.895 1.031 0.941 0.953 0.871 0.934 (1.714) (−1.599) (−1.439) (0.621) (−0.904) (−0.718) (0.070) (−1.241) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 Notes Each coefficient comes from a separate regression. Logit‐FE models include year fixed‐effects (see (2)). t‐statistics are shown in parentesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A4 Logit‐FE Estimates of Effects of State ER Using FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 1.043 0.995 0.924 1.023 0.956 0.919 0.902 1.015 (1.164) (−0.09) (−1.191) (0.530) (−0.774) (−1.365) (−1.576) (0.341) White 0.812 1.342 0.927 1.030 0.961 0.800 0.920 1.430 (−1.700) (1.708) (−0.331) (0.238) (−0.265) (−1.862) (−0.531) (2.611) Black 1.006 0.967 0.975 1.081 0.983 1.022 0.873 1.021 (0.142) (−0.492) (−0.312) (1.396) (−0.228) (0.261) (−1.676) (0.352) Hispanic 1.043 0.995 0.821 0.835 1.044 0.878 1.009 0.706 (1.155) (−0.094) (−1.142) (−1.844) (0.249) (−1.075) (0.031) (−2.764) Married 0.932 1.045 0.783 0.877 1.075 0.843 – 1.278 (−0.857) (0.337) (−1.292) (−1.183) (−0.421) (−1.261) (2.004) Unmarried 1.070 0.990 0.940 1.062 0.930 0.961 0.874 0.981 (1.643) (−0.165) (−0.863) (1.281) (−1.132) (−0.660) (−1.772) (−0.381) More than HS 0.963 1.284 1.006 0.999 0.995 0.891 0.966 1.291 (−0.588) (2.279) (0.043) (−0.013) (−0.04) (−1.190) (0.281) (2.742) HS or less 1.080 0.899 0.895 1.031 0.941 0.953 0.871 0.934 (1.714) (−1.599) (−1.439) (0.621) (−0.904) (−0.718) (0.070) (−1.241) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 1.043 0.995 0.924 1.023 0.956 0.919 0.902 1.015 (1.164) (−0.09) (−1.191) (0.530) (−0.774) (−1.365) (−1.576) (0.341) White 0.812 1.342 0.927 1.030 0.961 0.800 0.920 1.430 (−1.700) (1.708) (−0.331) (0.238) (−0.265) (−1.862) (−0.531) (2.611) Black 1.006 0.967 0.975 1.081 0.983 1.022 0.873 1.021 (0.142) (−0.492) (−0.312) (1.396) (−0.228) (0.261) (−1.676) (0.352) Hispanic 1.043 0.995 0.821 0.835 1.044 0.878 1.009 0.706 (1.155) (−0.094) (−1.142) (−1.844) (0.249) (−1.075) (0.031) (−2.764) Married 0.932 1.045 0.783 0.877 1.075 0.843 – 1.278 (−0.857) (0.337) (−1.292) (−1.183) (−0.421) (−1.261) (2.004) Unmarried 1.070 0.990 0.940 1.062 0.930 0.961 0.874 0.981 (1.643) (−0.165) (−0.863) (1.281) (−1.132) (−0.660) (−1.772) (−0.381) More than HS 0.963 1.284 1.006 0.999 0.995 0.891 0.966 1.291 (−0.588) (2.279) (0.043) (−0.013) (−0.04) (−1.190) (0.281) (2.742) HS or less 1.080 0.899 0.895 1.031 0.941 0.953 0.871 0.934 (1.714) (−1.599) (−1.439) (0.621) (−0.904) (−0.718) (0.070) (−1.241) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 Notes Each coefficient comes from a separate regression. Logit‐FE models include year fixed‐effects (see (2)). t‐statistics are shown in parentesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab 5.5. Association Between The Effects of UR and Self‐reported Physical and Mental Health A question that arises from using self‐reported health measures is whether the effects of the UR on self‐reported physical health could be driven by differences in perceived health that result from changes in mental health. In supplemental analyses (not shown here), we explored the sensitivity of the estimated effects of UR on physical health to including measures of a mother’s mental health as a control variable in the main specification (model 2). The estimates indicate that controlling for a mother’s depression in our main specification, does not significantly change the estimated coefficient on UR for other outcomes. 5.6. Selective Migration Less than 10% of sample mothers have migrated from the state in which they were first sampled at childbirth by year 9, so it seems unlikely that selective migration is driving our results. Moreover, when we ask how the unemployment rate affects the probability that a mother migrated to a different state, we find little overall effect. In order to investigate this issue, we constructed a dummy variable equal to one if a mother changed her state of residence from year 5 to year 9 and zero otherwise, and we regressed this indicator on the UR she experienced in year 5 controlling for her observable baseline characteristics, as well as on dummies for the baseline state and year fixed‐effects. We did not find a significant overall relationship between unemployment in year 5 and having migrated between year 5 and year 9. We do, however, find some evidence of heterogeneity in the migration response to unemployment: mothers with some college education, immigrants and those in better health at baseline are less likely to have migrated in response to changes in unemployment. This result suggests that using unemployment in the baseline state introduces some measurement error, and that this measurement error is not entirely random. Random measurement error in the unemployment rate would tend to attenuate its estimated effect on ill health. If measured unemployment is systematically too large for the unhealthiest people (because they have moved to places with lower unemployment), then this will tend to overstate the effect of unemployment on ill health. In order to investigate this possible bias, we estimate an alternative set of models using the unemployment rate in the actual state of residence in both waves. So for instance, if a mother who was originally (at baseline) sampled in Florida, moves to New York, between year 5 and year 9, then her UR measure will be the UR in Florida in year 5 and the UR in New York in year 9. In these models, there is no systematic measurement error in unemployment. However, since whether or not the mother moves between waves is a choice, these estimates may be biased instead by endogeneity. For example, if less healthy women are more likely to move, and if they move to lower unemployment states, then we would tend to underestimate the relationship between unemployment and poor health in these models. Appendix Table A6 shows logistic fixed‐effects estimates of these alternative models using the unemployment in the mother’s actual state of residence in both waves. The estimates are very similar to those presented above, which suggest that our estimates are not greatly affected by selective migration.22 Table A6 Logit‐FE Estimates of Effects of Current State of Residence UR in Using FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.853 1.091 1.073 0.992 1.220 1.108 1.355 1.019 (−2.644) (0.827) (0.632) (−0.125) (2.046) (1.251) (2.509) (0.258) White 0.931 1.086 0.824 1.008 1.459 1.216 1.232 0.767 (−0.442) (0.328) (−0.722) (0.052) (1.616) (1.152) (0.899) (−1.593) Black 0.706 1.321 1.175 0.933 1.149 1.276 1.480 0.955 (−3.138) (1.644) (0.772) (−0.558) (0.832) (1.338) (2.134) (−0.372) Hispanic 0.925 1.067 1.072 1.046 1.076 1.058 1.942 1.339 (−0.915) (0.359) (0.434) (0.495) (0.423) (0.455) (1.669) (2.170) Married 1.080 0.588 0.782 0.983 1.019 0.951 1.734 0.715 (0.547) (−1.622) (−1.030) (−0.097) (0.060) (−0.220) (1.630) (−1.700) Unmarried 0.807 1.205 1.186 0.968 1.278 1.120 1.225 1.095 (−3.146) (1.609) (1.299) (−0.477) (2.327) (1.279) (1.508) (1.106) More than HS 0.882 0.599 1.347 0.924 1.359 1.104 1.441 0.881 (−1.151) (−2.091) (1.009) (−0.738) (1.461) (0.677) (1.563) (−1.016) HS or less 0.850 1.319 1.088 1.026 1.155 1.120 1.341 1.122 (−2.222) (2.160) (0.673) (0.334) (1.297) (1.100) (1.991) (1.195) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.853 1.091 1.073 0.992 1.220 1.108 1.355 1.019 (−2.644) (0.827) (0.632) (−0.125) (2.046) (1.251) (2.509) (0.258) White 0.931 1.086 0.824 1.008 1.459 1.216 1.232 0.767 (−0.442) (0.328) (−0.722) (0.052) (1.616) (1.152) (0.899) (−1.593) Black 0.706 1.321 1.175 0.933 1.149 1.276 1.480 0.955 (−3.138) (1.644) (0.772) (−0.558) (0.832) (1.338) (2.134) (−0.372) Hispanic 0.925 1.067 1.072 1.046 1.076 1.058 1.942 1.339 (−0.915) (0.359) (0.434) (0.495) (0.423) (0.455) (1.669) (2.170) Married 1.080 0.588 0.782 0.983 1.019 0.951 1.734 0.715 (0.547) (−1.622) (−1.030) (−0.097) (0.060) (−0.220) (1.630) (−1.700) Unmarried 0.807 1.205 1.186 0.968 1.278 1.120 1.225 1.095 (−3.146) (1.609) (1.299) (−0.477) (2.327) (1.279) (1.508) (1.106) More than HS 0.882 0.599 1.347 0.924 1.359 1.104 1.441 0.881 (−1.151) (−2.091) (1.009) (−0.738) (1.461) (0.677) (1.563) (−1.016) HS or less 0.850 1.319 1.088 1.026 1.155 1.120 1.341 1.122 (−2.222) (2.160) (0.673) (0.334) (1.297) (1.100) (1.991) (1.195) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 Notes Each coefficient comes from a separate regression. Logit‐FE models include year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A6 Logit‐FE Estimates of Effects of Current State of Residence UR in Using FF . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.853 1.091 1.073 0.992 1.220 1.108 1.355 1.019 (−2.644) (0.827) (0.632) (−0.125) (2.046) (1.251) (2.509) (0.258) White 0.931 1.086 0.824 1.008 1.459 1.216 1.232 0.767 (−0.442) (0.328) (−0.722) (0.052) (1.616) (1.152) (0.899) (−1.593) Black 0.706 1.321 1.175 0.933 1.149 1.276 1.480 0.955 (−3.138) (1.644) (0.772) (−0.558) (0.832) (1.338) (2.134) (−0.372) Hispanic 0.925 1.067 1.072 1.046 1.076 1.058 1.942 1.339 (−0.915) (0.359) (0.434) (0.495) (0.423) (0.455) (1.669) (2.170) Married 1.080 0.588 0.782 0.983 1.019 0.951 1.734 0.715 (0.547) (−1.622) (−1.030) (−0.097) (0.060) (−0.220) (1.630) (−1.700) Unmarried 0.807 1.205 1.186 0.968 1.278 1.120 1.225 1.095 (−3.146) (1.609) (1.299) (−0.477) (2.327) (1.279) (1.508) (1.106) More than HS 0.882 0.599 1.347 0.924 1.359 1.104 1.441 0.881 (−1.151) (−2.091) (1.009) (−0.738) (1.461) (0.677) (1.563) (−1.016) HS or less 0.850 1.319 1.088 1.026 1.155 1.120 1.341 1.122 (−2.222) (2.160) (0.673) (0.334) (1.297) (1.100) (1.991) (1.195) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . All 0.853 1.091 1.073 0.992 1.220 1.108 1.355 1.019 (−2.644) (0.827) (0.632) (−0.125) (2.046) (1.251) (2.509) (0.258) White 0.931 1.086 0.824 1.008 1.459 1.216 1.232 0.767 (−0.442) (0.328) (−0.722) (0.052) (1.616) (1.152) (0.899) (−1.593) Black 0.706 1.321 1.175 0.933 1.149 1.276 1.480 0.955 (−3.138) (1.644) (0.772) (−0.558) (0.832) (1.338) (2.134) (−0.372) Hispanic 0.925 1.067 1.072 1.046 1.076 1.058 1.942 1.339 (−0.915) (0.359) (0.434) (0.495) (0.423) (0.455) (1.669) (2.170) Married 1.080 0.588 0.782 0.983 1.019 0.951 1.734 0.715 (0.547) (−1.622) (−1.030) (−0.097) (0.060) (−0.220) (1.630) (−1.700) Unmarried 0.807 1.205 1.186 0.968 1.278 1.120 1.225 1.095 (−3.146) (1.609) (1.299) (−0.477) (2.327) (1.279) (1.508) (1.106) More than HS 0.882 0.599 1.347 0.924 1.359 1.104 1.441 0.881 (−1.151) (−2.091) (1.009) (−0.738) (1.461) (0.677) (1.563) (−1.016) HS or less 0.850 1.319 1.088 1.026 1.155 1.120 1.341 1.122 (−2.222) (2.160) (0.673) (0.334) (1.297) (1.100) (1.991) (1.195) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 Notes Each coefficient comes from a separate regression. Logit‐FE models include year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab 5.7. Selective Attrition Another potential source of selection bias in this study is the presence of selective attrition from year 5 to year 9. Selective attrition may bias our estimates of UR on health outcomes if for instance, mothers who are interviewed in year 5 and not in year 9, are missing from the data perhaps due to experiencing material hardship in year 9 (e.g. telephone service disconnected), which could be correlated with an increase in the probability of experiencing poor health. The attrition rate from year 5 to year 9 of FF is 19%.23 To analyse whether the effect of UR on the probability of attrition was different for different groups, we perform a simple test in which we construct a dummy variable equal to one if a mother left the sample from year 5 to year 9,24 and we regress this indicator on the UR she experienced in year 5, her observable characteristics interacted by the UR in year 5 and all other covariates as described in (1).25 In the presence of selective attrition, the coefficients on the interaction between the UR and a woman’s characteristics should be statistically significant. We also examine selective attrition in terms of health outcomes (physical and mental health and health behaviour) by replicating the previous analysis on selective attrition based on women’s observable characteristics but this time we interact a woman’s health outcomes in year 5 with the UR in year 5. Appendix Tables A7 and A8 show estimates of selective attrition in terms of women’s observable characteristics and in terms of women’s health outcomes. We find little evidence of selective attrition in terms of mother characteristics. In fact, the only group that is less likely to attrition in year 9 is women with a college degree who faced high UR in year 5. In terms of health status in year 5 we also find little evidence of selective attrition. We do see, however, that women who suffer from obesity in year 5 are significantly more likely to leave the sample in year 9 after experiencing high unemployment. These findings suggest that selective attrition is not a big issue in our analysis. To the extent that there is selective attrition, women in better health (i.e. more educated, less likely to be obese and less likely to consume drugs) are more likely to be interviewed in year 9, which may lead to an underestimation of the effect of the UR on women’s health. Table A8 The Propensity to Attrite in Year 9 Explained by UR and Mother’s Health in Year 5 . (1) . (2) . UR 1.727 1.747 (1.754) (1.765) UR × health is excellent or very good 0.989 (−0.122) UR × health problem limits work 0.749 (−1.605) UR × obesity 1.321 (4.201) UR × any health insurance 0.882 (−1.920) UR × smokes 1.088 (1.036) UR × 4 ≥ drinks in 1 occasion 0.916 (−0.740) UR × uses drugs 1.207 (1.777) UR × depressed 1.016 (0.114) N 3,472 3,472 . (1) . (2) . UR 1.727 1.747 (1.754) (1.765) UR × health is excellent or very good 0.989 (−0.122) UR × health problem limits work 0.749 (−1.605) UR × obesity 1.321 (4.201) UR × any health insurance 0.882 (−1.920) UR × smokes 1.088 (1.036) UR × 4 ≥ drinks in 1 occasion 0.916 (−0.740) UR × uses drugs 1.207 (1.777) UR × depressed 1.016 (0.114) N 3,472 3,472 Notes Each column is a separate regression. The state UR and all health variables (health status, health problem that limits work, obesity, etc.) are measured in year 5. In addition to the listed covariates, both regressions include main effects for mother’s age, race/ethnicity, education, income‐to‐needs ratio and marital status as well as baseline state and year fixed‐effects; errors are clustered at the baseline state level. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A8 The Propensity to Attrite in Year 9 Explained by UR and Mother’s Health in Year 5 . (1) . (2) . UR 1.727 1.747 (1.754) (1.765) UR × health is excellent or very good 0.989 (−0.122) UR × health problem limits work 0.749 (−1.605) UR × obesity 1.321 (4.201) UR × any health insurance 0.882 (−1.920) UR × smokes 1.088 (1.036) UR × 4 ≥ drinks in 1 occasion 0.916 (−0.740) UR × uses drugs 1.207 (1.777) UR × depressed 1.016 (0.114) N 3,472 3,472 . (1) . (2) . UR 1.727 1.747 (1.754) (1.765) UR × health is excellent or very good 0.989 (−0.122) UR × health problem limits work 0.749 (−1.605) UR × obesity 1.321 (4.201) UR × any health insurance 0.882 (−1.920) UR × smokes 1.088 (1.036) UR × 4 ≥ drinks in 1 occasion 0.916 (−0.740) UR × uses drugs 1.207 (1.777) UR × depressed 1.016 (0.114) N 3,472 3,472 Notes Each column is a separate regression. The state UR and all health variables (health status, health problem that limits work, obesity, etc.) are measured in year 5. In addition to the listed covariates, both regressions include main effects for mother’s age, race/ethnicity, education, income‐to‐needs ratio and marital status as well as baseline state and year fixed‐effects; errors are clustered at the baseline state level. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A7 The Propensity to Attrition in Year 9 Explained by The UR in Year 5 and Women’s Characteristics . (1) . (2) . UR 1.711 5.291 (2.061) (1.001) UR × mother’s age <20 1.001 (0.006) UR × mother’s age 20–23 0.979 (−0.208) UR × mother’s age 24–27 0.991 (−0.118) UR × mother’s age 28–32 1.001 (0.021) UR × mother is black 0.821 (−1.187) UR × mother is hispanic 0.774 (−1.129) UR × mother is other race/ethn 0.787 (−1.693) UR × mother is immigrant 1.062 (0.338) UR × mother is single 0.814 (−1.015) UR × mother cohabitates 0.894 (−0.616) UR × mother’s education HS 0.905 (−0.992) UR × mother’s education some college 0.819 (−3.733) UR × mother’s education college 0.759 (−1.131) UR × mother’s income‐to‐needs ratio <100% 1.014 (0.150) UR × mother’s inc.‐to‐needs ratio: 100–199% 1.099 (0.718) UR × mother’s inc.‐to‐needs ratio: 200–399% 1.111 (0.662) UR × child’s age in months 0.988 (−0.510) N 3,797 3,797 . (1) . (2) . UR 1.711 5.291 (2.061) (1.001) UR × mother’s age <20 1.001 (0.006) UR × mother’s age 20–23 0.979 (−0.208) UR × mother’s age 24–27 0.991 (−0.118) UR × mother’s age 28–32 1.001 (0.021) UR × mother is black 0.821 (−1.187) UR × mother is hispanic 0.774 (−1.129) UR × mother is other race/ethn 0.787 (−1.693) UR × mother is immigrant 1.062 (0.338) UR × mother is single 0.814 (−1.015) UR × mother cohabitates 0.894 (−0.616) UR × mother’s education HS 0.905 (−0.992) UR × mother’s education some college 0.819 (−3.733) UR × mother’s education college 0.759 (−1.131) UR × mother’s income‐to‐needs ratio <100% 1.014 (0.150) UR × mother’s inc.‐to‐needs ratio: 100–199% 1.099 (0.718) UR × mother’s inc.‐to‐needs ratio: 200–399% 1.111 (0.662) UR × child’s age in months 0.988 (−0.510) N 3,797 3,797 Notes Each column is a separate regression. Sample includes year 9 data as a cross section. The state UR is measured in year 5. In addition to the listed covariates, both regressions include main effects for mother’s age, race/ethnicity, education, income‐to‐needs ratio and marital status as well as baseline state and year fixed‐effects; errors are clustered at the baseline state level. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A7 The Propensity to Attrition in Year 9 Explained by The UR in Year 5 and Women’s Characteristics . (1) . (2) . UR 1.711 5.291 (2.061) (1.001) UR × mother’s age <20 1.001 (0.006) UR × mother’s age 20–23 0.979 (−0.208) UR × mother’s age 24–27 0.991 (−0.118) UR × mother’s age 28–32 1.001 (0.021) UR × mother is black 0.821 (−1.187) UR × mother is hispanic 0.774 (−1.129) UR × mother is other race/ethn 0.787 (−1.693) UR × mother is immigrant 1.062 (0.338) UR × mother is single 0.814 (−1.015) UR × mother cohabitates 0.894 (−0.616) UR × mother’s education HS 0.905 (−0.992) UR × mother’s education some college 0.819 (−3.733) UR × mother’s education college 0.759 (−1.131) UR × mother’s income‐to‐needs ratio <100% 1.014 (0.150) UR × mother’s inc.‐to‐needs ratio: 100–199% 1.099 (0.718) UR × mother’s inc.‐to‐needs ratio: 200–399% 1.111 (0.662) UR × child’s age in months 0.988 (−0.510) N 3,797 3,797 . (1) . (2) . UR 1.711 5.291 (2.061) (1.001) UR × mother’s age <20 1.001 (0.006) UR × mother’s age 20–23 0.979 (−0.208) UR × mother’s age 24–27 0.991 (−0.118) UR × mother’s age 28–32 1.001 (0.021) UR × mother is black 0.821 (−1.187) UR × mother is hispanic 0.774 (−1.129) UR × mother is other race/ethn 0.787 (−1.693) UR × mother is immigrant 1.062 (0.338) UR × mother is single 0.814 (−1.015) UR × mother cohabitates 0.894 (−0.616) UR × mother’s education HS 0.905 (−0.992) UR × mother’s education some college 0.819 (−3.733) UR × mother’s education college 0.759 (−1.131) UR × mother’s income‐to‐needs ratio <100% 1.014 (0.150) UR × mother’s inc.‐to‐needs ratio: 100–199% 1.099 (0.718) UR × mother’s inc.‐to‐needs ratio: 200–399% 1.111 (0.662) UR × child’s age in months 0.988 (−0.510) N 3,797 3,797 Notes Each column is a separate regression. Sample includes year 9 data as a cross section. The state UR is measured in year 5. In addition to the listed covariates, both regressions include main effects for mother’s age, race/ethnicity, education, income‐to‐needs ratio and marital status as well as baseline state and year fixed‐effects; errors are clustered at the baseline state level. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab 6. Conclusions This study contributes to the ongoing discussion of the relationship between economic fluctuations and people’s health, by providing new evidence of the effects of the Great Recession on a growing group of vulnerable families, unmarried women with children. Our results imply that increases in unemployment over the Great Recession period of 2007–9, reduced the probability of having ‘excellent’ or ‘very good’ health and increased the probability of smoking and of using drugs. The effects are larger than those reported in the previous literature, for example Davalos and French (2011) found that a one percentage point increase in the unemployment rate increased the probability of fair or poor health by 0.9%, whereas we estimate an increase of 4.3%. These larger estimates are consistent with the fact that the Great Recession represented a massive and unprecedented economic shock for millions of families and so may have had larger effects than smaller previous recessions. We show that if we estimate models of the state UR on health outcomes without controlling for individual fixed‐effects, the coefficients are very similar in magnitude to those obtained when we do account for these time‐invariant characteristics, although they are less precisely estimated. Thus, in order to be able to identify more precise estimates of the UR, it is helpful to be able to follow individuals over time. Previous studies have come to very different conclusions about the impacts of economic downturns on health. Most of this research, however, predates the Great Recession, and only a few studies have focused on the recent crisis. Most importantly, no study has yet focused on the groups who were most likely to be impacted by high unemployment rate (i.e. disadvantaged families) and this is particularly relevant considering the growing body of research showing that inequality starts in early life and that children of more disadvantaged mothers are more likely to be disadvantaged themselves. We show that the Great Recession had heterogeneous effects on the health of women. While increases in unemployment worsened physical and mental health, and increased smoking and drug use among minorities, unmarried mothers and less‐educated mothers more advantaged women may have actually experienced better mental health and some improvements in their physical health. For example, we found that whites were less likely to be obese and more educated women were less likely to have health problems during the Recession. However, the picture was mixed as they were also more likely to smoke and binge drink as the UR increased. These results are consistent with recent findings suggesting that the employment effects of the crisis were disproportionately concentrated in some subpopulations. We faced several limitations. First, our sample is not generalisable to the population as a whole since FF is an urban birth cohort study; however, since the evidence in this area is limited, especially on women or disadvantaged groups, using FF contributes to the discussion. Second, all the measures that we have analysed are self‐reported and they have not been medically verified. Third, although we suggested potential pathways through which the recession could have affected women’s health, we did not directly test them. Research that further explores the effect of economic conditions on the health outcomes of more disadvantaged groups should explore potential mechanisms driving these impacts. Many studies have argued that unemployment could impact people’s health through changes in health behaviour or increasing stress due to income and wealth declines; however, whether the relative importance of these pathways differs across social groups and in particular for those experiencing a high economic burden remains an open question. Another useful extension of our work would be to investigate the impacts of the Recession on children’s health. The declines in mothers’ health, particularly among fragile families, could suggest important short and long‐term effects on young children that could contribute to inequality for years to come. Appendix A: Extensions and robustness checks Table A1 The Effect of The UR on Mothers’ Health for The Full Sample and for The Sample Interviewed After 2008 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Sample interviewed AFTER 2008 LOGIT 0.929 0.99 1.018 0.966 1.089 1.046 1.048 0.978 (−1.66) (−0.182) (0.712) (−0.701) (1.382) (0.912) (0.621) (−0.283) LOGIT‐FE 0.842 1.013 1.017 1.025 1.214 1.188 1.252 0.935 (−2.610) (0.123) (0.142) (0.371) (1.841) (1.921) (1.574) (−0.832) N 3,540 3,539 3,100 3,534 3,540 3,537 3,536 3,532 N changers 531 202 279 415 209 302 161 320 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Sample interviewed AFTER 2008 LOGIT 0.929 0.99 1.018 0.966 1.089 1.046 1.048 0.978 (−1.66) (−0.182) (0.712) (−0.701) (1.382) (0.912) (0.621) (−0.283) LOGIT‐FE 0.842 1.013 1.017 1.025 1.214 1.188 1.252 0.935 (−2.610) (0.123) (0.142) (0.371) (1.841) (1.921) (1.574) (−0.832) N 3,540 3,539 3,100 3,534 3,540 3,537 3,536 3,532 N changers 531 202 279 415 209 302 161 320 Notes Each coefficient comes from a separate regression. Logit models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and baseline state and year fixed‐effects; errors are clustered at the baseline state level (see (1)). Logit‐FE models control for year fixed‐effects (see (2)). The sample interviewed after 2008 includes years 2009 and 2010. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A1 The Effect of The UR on Mothers’ Health for The Full Sample and for The Sample Interviewed After 2008 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Sample interviewed AFTER 2008 LOGIT 0.929 0.99 1.018 0.966 1.089 1.046 1.048 0.978 (−1.66) (−0.182) (0.712) (−0.701) (1.382) (0.912) (0.621) (−0.283) LOGIT‐FE 0.842 1.013 1.017 1.025 1.214 1.188 1.252 0.935 (−2.610) (0.123) (0.142) (0.371) (1.841) (1.921) (1.574) (−0.832) N 3,540 3,539 3,100 3,534 3,540 3,537 3,536 3,532 N changers 531 202 279 415 209 302 161 320 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Sample interviewed AFTER 2008 LOGIT 0.929 0.99 1.018 0.966 1.089 1.046 1.048 0.978 (−1.66) (−0.182) (0.712) (−0.701) (1.382) (0.912) (0.621) (−0.283) LOGIT‐FE 0.842 1.013 1.017 1.025 1.214 1.188 1.252 0.935 (−2.610) (0.123) (0.142) (0.371) (1.841) (1.921) (1.574) (−0.832) N 3,540 3,539 3,100 3,534 3,540 3,537 3,536 3,532 N changers 531 202 279 415 209 302 161 320 Notes Each coefficient comes from a separate regression. Logit models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and baseline state and year fixed‐effects; errors are clustered at the baseline state level (see (1)). Logit‐FE models control for year fixed‐effects (see (2)). The sample interviewed after 2008 includes years 2009 and 2010. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A2 The Effect of The UR on Mothers’ Health for The Full sample and for Different Samples of States . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Excluding states with the highest population: CA and TX LOGIT 0.906 1.002 1.017 0.955 1.120 0.99 1.018 0.911 (−1.172) (0.029) (0.392) (−0.731) (1.372) (−0.089) (0.141) (−1.001) LOGIT‐FE 0.768 0.987 1.093 0.971 1.275 1.198 1.459 0.859 (−2.631) (−0.087) (0.512) (−0.284) (1.610) (1.299) (2.089) (−1.288) N 5,003 4,997 4,370 4,994 5,003 4,994 4,981 4,984 N changers 667 281 369 484 257 328 238 411 Excluding states with the highest avg. UR: MI and OH LOGIT 0.906 0.988 1.029 0.986 1.095 1.119 1.015 1.038 (−2.588) (−0.299) (1.413) (−0.339) (1.664) (2.569) (0.199) (0.656) LOGIT‐FE 0.832 1.043 1.023 1.01 1.189 1.163 1.198 0.962 (−2.819) (0.369) (0.189) (0.149) (1.639) (1.709) (1.277) (−0.483) N 6,375 6,367 5,567 6,360 6,375 6,365 6,346 6,363 N changers 859 315 447 696 324 441 279 523 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Excluding states with the highest population: CA and TX LOGIT 0.906 1.002 1.017 0.955 1.120 0.99 1.018 0.911 (−1.172) (0.029) (0.392) (−0.731) (1.372) (−0.089) (0.141) (−1.001) LOGIT‐FE 0.768 0.987 1.093 0.971 1.275 1.198 1.459 0.859 (−2.631) (−0.087) (0.512) (−0.284) (1.610) (1.299) (2.089) (−1.288) N 5,003 4,997 4,370 4,994 5,003 4,994 4,981 4,984 N changers 667 281 369 484 257 328 238 411 Excluding states with the highest avg. UR: MI and OH LOGIT 0.906 0.988 1.029 0.986 1.095 1.119 1.015 1.038 (−2.588) (−0.299) (1.413) (−0.339) (1.664) (2.569) (0.199) (0.656) LOGIT‐FE 0.832 1.043 1.023 1.01 1.189 1.163 1.198 0.962 (−2.819) (0.369) (0.189) (0.149) (1.639) (1.709) (1.277) (−0.483) N 6,375 6,367 5,567 6,360 6,375 6,365 6,346 6,363 N changers 859 315 447 696 324 441 279 523 Notes Each coefficient comes from a separate regression. Logit models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and baseline state and year fixed‐effects; errors are clustered at the baseline state level (see (1)). Logit‐FE models control for year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A2 The Effect of The UR on Mothers’ Health for The Full sample and for Different Samples of States . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Excluding states with the highest population: CA and TX LOGIT 0.906 1.002 1.017 0.955 1.120 0.99 1.018 0.911 (−1.172) (0.029) (0.392) (−0.731) (1.372) (−0.089) (0.141) (−1.001) LOGIT‐FE 0.768 0.987 1.093 0.971 1.275 1.198 1.459 0.859 (−2.631) (−0.087) (0.512) (−0.284) (1.610) (1.299) (2.089) (−1.288) N 5,003 4,997 4,370 4,994 5,003 4,994 4,981 4,984 N changers 667 281 369 484 257 328 238 411 Excluding states with the highest avg. UR: MI and OH LOGIT 0.906 0.988 1.029 0.986 1.095 1.119 1.015 1.038 (−2.588) (−0.299) (1.413) (−0.339) (1.664) (2.569) (0.199) (0.656) LOGIT‐FE 0.832 1.043 1.023 1.01 1.189 1.163 1.198 0.962 (−2.819) (0.369) (0.189) (0.149) (1.639) (1.709) (1.277) (−0.483) N 6,375 6,367 5,567 6,360 6,375 6,365 6,346 6,363 N changers 859 315 447 696 324 441 279 523 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Full sample LOGIT 0.933 0.989 1.024 0.987 1.09 1.091 1.029 0.998 (−1.755) (−0.284) (1.407) (−0.334) (1.810) (1.852) (0.471) (−0.033) LOGIT‐FE 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Excluding states with the highest population: CA and TX LOGIT 0.906 1.002 1.017 0.955 1.120 0.99 1.018 0.911 (−1.172) (0.029) (0.392) (−0.731) (1.372) (−0.089) (0.141) (−1.001) LOGIT‐FE 0.768 0.987 1.093 0.971 1.275 1.198 1.459 0.859 (−2.631) (−0.087) (0.512) (−0.284) (1.610) (1.299) (2.089) (−1.288) N 5,003 4,997 4,370 4,994 5,003 4,994 4,981 4,984 N changers 667 281 369 484 257 328 238 411 Excluding states with the highest avg. UR: MI and OH LOGIT 0.906 0.988 1.029 0.986 1.095 1.119 1.015 1.038 (−2.588) (−0.299) (1.413) (−0.339) (1.664) (2.569) (0.199) (0.656) LOGIT‐FE 0.832 1.043 1.023 1.01 1.189 1.163 1.198 0.962 (−2.819) (0.369) (0.189) (0.149) (1.639) (1.709) (1.277) (−0.483) N 6,375 6,367 5,567 6,360 6,375 6,365 6,346 6,363 N changers 859 315 447 696 324 441 279 523 Notes Each coefficient comes from a separate regression. Logit models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and baseline state and year fixed‐effects; errors are clustered at the baseline state level (see (1)). Logit‐FE models control for year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A3 The Effect of The State UR on Mothers’ Weight . Obesity . BMI . Logit . OLS . OLS . State UR Without individual FE 1.024 0.005 0.033 (1.407) (1.086) (0.252) With individual FE 1.087 0.009 0.056 (0.712) (1.164) (0.727) City UR Without individual FE 1.025 0.006 0.042 (1.237) (1.261) (0.341) With individual FE 1.038 0.008 0.050 (0.332) (1.042) (0.651) N 6,178 6,178 6,178 N changers 511 511 2,541 . Obesity . BMI . Logit . OLS . OLS . State UR Without individual FE 1.024 0.005 0.033 (1.407) (1.086) (0.252) With individual FE 1.087 0.009 0.056 (0.712) (1.164) (0.727) City UR Without individual FE 1.025 0.006 0.042 (1.237) (1.261) (0.341) With individual FE 1.038 0.008 0.050 (0.332) (1.042) (0.651) N 6,178 6,178 6,178 N changers 511 511 2,541 Notes Each coefficient comes from a separate regression. Logit/OLS models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and state (city) and year fixed‐effects; errors are clustered at the baseline state (city) level (see (1)). Logit‐FE/Linear models with individual fixed‐effects control for year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; bold font indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A3 The Effect of The State UR on Mothers’ Weight . Obesity . BMI . Logit . OLS . OLS . State UR Without individual FE 1.024 0.005 0.033 (1.407) (1.086) (0.252) With individual FE 1.087 0.009 0.056 (0.712) (1.164) (0.727) City UR Without individual FE 1.025 0.006 0.042 (1.237) (1.261) (0.341) With individual FE 1.038 0.008 0.050 (0.332) (1.042) (0.651) N 6,178 6,178 6,178 N changers 511 511 2,541 . Obesity . BMI . Logit . OLS . OLS . State UR Without individual FE 1.024 0.005 0.033 (1.407) (1.086) (0.252) With individual FE 1.087 0.009 0.056 (0.712) (1.164) (0.727) City UR Without individual FE 1.025 0.006 0.042 (1.237) (1.261) (0.341) With individual FE 1.038 0.008 0.050 (0.332) (1.042) (0.651) N 6,178 6,178 6,178 N changers 511 511 2,541 Notes Each coefficient comes from a separate regression. Logit/OLS models control for mother characteristics (age, race/ethnicity, education, income‐to‐needs ratio and marital status), and state (city) and year fixed‐effects; errors are clustered at the baseline state (city) level (see (1)). Logit‐FE/Linear models with individual fixed‐effects control for year fixed‐effects (see (2)). t‐statistics are shown in parenthesis; bold font indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A5 Logit‐FE Estimates of Effects of UR Controlling for a Mother’s Current State of Residence . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Without current state of residence controls 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) With current state of residence controls 0.839 1.086 1.112 1.022 1.320 1.135 1.427 0.967 (−2.770) (0.781) (0.884) (0.33) (2.672) (1.483) (2.603) (−0.43) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Without current state of residence controls 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) With current state of residence controls 0.839 1.086 1.112 1.022 1.320 1.135 1.427 0.967 (−2.770) (0.781) (0.884) (0.33) (2.672) (1.483) (2.603) (−0.43) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Notes Each coefficient comes from a separate regression. All models (Logit‐FE models) include year fixed‐effects (see (2)); in addition to year fixed‐effects, models in the third row (‘WITH current state of residence controls’) include current state fixed‐effects. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Table A5 Logit‐FE Estimates of Effects of UR Controlling for a Mother’s Current State of Residence . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Without current state of residence controls 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) With current state of residence controls 0.839 1.086 1.112 1.022 1.320 1.135 1.427 0.967 (−2.770) (0.781) (0.884) (0.33) (2.672) (1.483) (2.603) (−0.43) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 . Health status excellent or very good . Health problem limits work . Obesity . Any health insurance . Smokes . ≥4 drinks on 1 occasion . Drug use . Depressed . Without current state of residence controls 0.848 1.073 1.087 0.993 1.256 1.140 1.400 0.941 (−2.602) (0.661) (0.712) (−0.111) (2.231) (1.521) (2.499) (−0.791) With current state of residence controls 0.839 1.086 1.112 1.022 1.320 1.135 1.427 0.967 (−2.770) (0.781) (0.884) (0.33) (2.672) (1.483) (2.603) (−0.43) N 7,080 7,070 6,178 7,064 7,079 7,070 7,058 7,067 N changers 953 364 511 758 359 491 322 591 Notes Each coefficient comes from a separate regression. All models (Logit‐FE models) include year fixed‐effects (see (2)); in addition to year fixed‐effects, models in the third row (‘WITH current state of residence controls’) include current state fixed‐effects. t‐statistics are shown in parenthesis; italics indicates that the result is statistically significant at the 95% level of confidence. Open in new tab Footnotes 1 " In particular, he found significant associations for men between 20 and 44, and weak (null) results for those between 45 and 64 and for those over 65. 2 " The authors found that black women are less likely to give birth during recessions (which might be due either to foetal selection or to selection into pregnancy), which tends to raise mean birthweights. 3 " While Charles and DeCicca obtained their result from a sample of young men with high socio‐economic status, Deb et al. confirmed this finding on a sample of workers near retirement age. 4 " Two studies use longitudinal data for Iceland (Ásgeirsdóttir et al., 2012; McClure et al., 2013). 5 " For example, all the questions related to maternal anxiety were only available at years 1 and 3. 6 " The data files and programs used in this article are available online. In order to protect the confidentiality of survey respondents, personal and geographic (i.e. city) identifiers are not released in the data files we provide. 7 " These variables include both commonly used health measures and new outcomes that have not been examined in previous studies, for example the use of drugs or screener for depression. 8 " The complete list includes: illegal drugs (marihuana or hashish; cocaine, crack or free base; LSD or other hallucinogens; heroin), sedatives (including either barbiturates or sleeping pills such as Seconal, Halcion, Methaqualone), tranquilisers or ‘nerve pills’ (e.g. Librium, Valium, Ativan, Meprobamate, Xanax), amphetamines or other stimulants (e.g. methamphetamine, Preludin, Dexedrine, Ritalin, ‘Speed’), analgesics or other prescription painkillers (note: this does not include normal use of aspirin, Tylenol without codeine etc., but does include use of Tylenol with codeine and other Rx painkillers such as Demerol, Darvon, Percodan, Codeine, Morphine and Methadone), inhalants (e.g. Amylnitrate, Freon, Nitrous Oxide (‘whippets’), Petrol, Spray paint). 9 " A respondent is assessed as depressed if they had feelings of dysphoria (depression) or anhedonia (inability to enjoy what is usually pleasurable) in the past year that lasted for two weeks or more and, if she had symptoms (1. losing interest, 2. feeling tired, 3. change in weight, 4. trouble sleeping, 5. trouble concentrating, 6. feeling worthless and 7. thinking about death) that lasted at least about half of the day and occurred every day during the two‐week period. 10 " A mother’s risk for depression is based on her score from a short version of the CIDI‐SF, Section A (Kessler and Mroczek, 1994; Kessler et al., 1998) that is asked to the mother in a phone interview. The short form of the CIDI interview takes a portion of the full set of CIDI questions and uses the responses to generate the probability that the respondent would be a ‘case’ (i.e. a positively diagnosed respondent), if given a full CIDI interview. The CIDI questions are consistent with the Diagnostic and Statistical Manual of Mental Disorders – Fourth Edition (DSM‐IV; American Psychiatric Association, 1994). The CIDI is a standardised instrument for assessment of mental disorders intended for use in epidemiological, cross‐cultural and other research studies. 11 " Statistics on women’s physical health and health behaviours were obtained from the ‘Summary Health Statistics for US Adults: National Health Interview Survey, 2011’ of the Center for Disease Control and Prevention (http://www.cdc.gov/nchs/data/series/sr_10/sr10_256.pdf). 12 " Statistics on the prevalence of depression were obtained from the 2013 report on ‘Mental health among women of reproductive age’ of the Center for Disease Control and Prevention (http://www.cdc.gov/reproductivehealth/Depression/PDFs/Mental_Health_Women_Repo_Age.pdf.) 13 " No information was available on drug use at the national level. 14 " We use baseline city weights for FF. 15 " The state unemployment and employment‐to‐population ratio (used later in the article) are obtained from Table 3 in the files: ‘Regional and State Employment and Unemployment’ (in pdf format) that are available for each year/month from December 1993 to April 2012. The link to the BLS with these specific files is: http://www.bls.gov/schedule/archives/laus_nr.htm#2004. 16 " Figure 1 only includes information for the periods of interview. 17 " The income‐to‐needs ratio is based on the official US poverty thresholds established by the Census Bureau. 18 " During the recession, there was a sharp decline in the share of the population with employer‐sponsored health insurance due to the massive decline in employment, which could have been offset by a significant rise in Medicare enrolment (Cawley et al., 2011). 19 " In other analysis (not shown here), we estimate the effect of UR on the likelihood of being overweight (BMI ≥ 25) and we find no effect. 20 " In other analysis (not shown here), we also find that a rise in the UR is not associated with changes in the likelihood of being sad or blue for at least two weeks in the past year, which is a less extreme case of mental health condition, providing further evidence that there is little impact of the Recession on the aggregate sample of women. 21 " Weighted estimates using baseline city weights in FF. 22 " We have also estimated models simply including controls (dummy variables) for a mother’s current state of residence. These results are shown in Appendix Table A5. Controlling for a mother’s current location does not substantially change the estimated effect of the UR on health. 23 " In year 5, 3,808 mothers were interviewed and 3,069 were interviewed in year 9. These numbers differ slightly from those shown in Table 2 because they are conditional on being interviewed in year 5, hence excludes those mothers who were interviewed in year 9 and not in year 5. 24 " The dummy for attrition from year 5 to year 9 takes the value of 1 when the mother was interviewed in year 5 and not in year 9, and zero otherwise. 25 " We include a mother’s baseline characteristics, and state and year fixed‐effects. Errors are clustered at the state level. References Aalto‐Setälä , T. , Haarasilta , L., Marttunen , M., Tuulio‐Henriksson , A., Poikolainen , K., Aro , H. and Lönnqvist , J. 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( 2013 ). ‘ Health and health behaviors during the worst of times: evidence from the great recession ’, Working Paper, NBER, 19234. Theodossiou , I. ( 1997 ). ‘ The effects of low‐pay and unemployment on psychological well‐being: a logistic regression approach ’, Journal of Health Economics , vol. 17 ( 1 ), pp. 85 – 104 . OpenURL Placeholder Text WorldCat Verick , S. ( 2010 ). ‘Who is hit hardest during a financial crisis? The vulnerability of young men and women to unemployment in an economic downturn’, in ( I. Islam and S. Verick, eds.), From the Great Recession to Labour Market Recovery: Issues, Evidence and Policy Options . Basingstoke : Palgrave . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Xu , X. and Kaestner , R. ( 2010 ). ‘ The business cycle and health behaviors ’, Working Paper, NBER, 15737. Author notes " The project was supported by the Eunice Kennedy Shriver National Institute of Child Health & Human Development Award Numbers R01HD066054, R01HD036916 and R24HD058486 and by the National Institute on Aging Roybal grant P30AGO24928. The content is solely the responsibility of the authors and does not necessarily represent the official views of the Eunice Kennedy Shriver National Institute of Child Health & Human Development or the National Institutes of Health. The authors thank the participants at the Fragile Families Seminar at Columbia University – School of Social Work and at the Association of Public Policy and Management (APPAM) Conference 2013, and two reviewers for comments and suggestions. All errors are our own. © 2015 Royal Economic Society

Lavy,, Victor

doi: 10.1111/ecoj.12233pmid: N/A

Abstract The time that children spend in school varies across countries. Do these differences explain international gaps in pupils’ academic achievements? In this article I estimate the effects of instructional time on students’ achievement using PISA 2006 data, which include data samples from over 50 countries. I find that instructional time has a positive and significant effect on test scores, and that the effect is much lower in developing countries. Evidence also suggests that the productivity of instructional time is higher in countries which implemented school accountability measures or that gave schools autonomy in budgetary decisions and in hiring/firing teachers. The amount of time that students spend in public schools varies widely from one country to another. For example, among European countries such as Belgium, France and Greece, 15‐year‐old pupils receive an average of more than 1,000 hours per year of total compulsory classroom instruction, while in England, Luxembourg and Sweden the average is only 750 hours per year.1 Also, children from the ages 7–8 in England, Greece, France and Portugal receive an average instructional time of more than 800 hours per year, while in Finland and Norway they receive less than 600 hours. Similar differences among countries exist in the number of classroom lessons per week in different subjects as evident from data from the 2006 Programme for International Student Assessment (PISA), a unique international education survey of 15‐year‐old students conducted by the Organisation for Economic Co‐operation and Development (OECD) and designed to allow for cross‐country comparisons. For instance, these data show that 15‐year‐old pupils in Denmark receive four hours of instruction per week in mathematics and 4.7 hours in language, while pupils of the same age in Austria receive only 2.7 hours of weekly classroom lessons in mathematics and 2.4 hours in language. Overall, total weekly hours of instruction in mathematics, language and science is 55% higher in Denmark (11.5 hours) than in Austria (7.4 hours). Similar magnitudes of disparities in instructional time appear among the Eastern European and developing countries that are included in the PISA 2006. Do these large differences in instructional time explain some of the differences across countries in pupils’ achievements in different subjects? While research in recent years provides convincing evidence about the effect of several inputs in the education production function,2 there is limited evidence on the effect of classroom instructional time. This evidence ought to be important for policy makers in many countries since increasing instructional time is a relatively simple option to implement (provided that resources are available) and, moreover, such an increase would be feasible in many countries. For example, US President Barack Obama has argued in recent years that American children should go to school longer – either staying later in the day or attending later into the summer or both. He has spoken of this goal, of extending the school week and year, as a central element in his proposed education reform.3 In this article, I use the results of the PISA 2006. PISA is a triennial survey of the knowledge and skills of 15‐year olds. It is the product of collaboration between participating countries through the OECD and draws on leading international expertise to develop valid comparisons across countries and cultures. More than 400,000 students from 57 countries constituting close to 90% of the world economy took part in PISA 2006. The study focused on science but the assessment also included language and mathematics. In addition, it collected data on student, family and institutional factors, including information about the amount of instructional time per week in each of the subjects tested. I exploit these features of the data to identify the effect of instructional time on academic achievement. First, having test scores in multiple subjects for each student and relatively large variation in instructional time across subjects allows me to use within‐student estimation of the effect of instructional time. At the same time, I am able to control for individual time‐invariant characteristics that equally affect performance across subjects, such as the individual’s underlying ability, parental and family background, lagged achievements and lagged and current school resources and characteristics. Second, the considerable within‐student variation in instructional time allows for additional analysis. I use this significant variation to test whether the effect of instructional time is non‐linear and whether it differs among developed and developing countries. The disadvantage of this identification approach is that I assume that the effect of instructional time is the same for all three subjects, an assumption that is common in many studies that pool cross‐sectional data across subjects. However, in this study I can assess how restrictive it is by comparing estimates obtained based on pooling only subgroups or all three subjects together. This article hopes to overcome some of the problems and limitations found in the numerous studies which have evaluated the effect of time spent in school on student achievement and earnings. For example, Grogger (1996) and Eide and Showalter (1998) estimated the effect of the length of the school year in the US and found insignificant effects, perhaps due to limited variation in the length of the school year there or the omission of other variables. Card and Krueger (1992) and Betts and Johnson (1998) used state‐level data in the US to examine the same effect and found a positive significant effect on earnings, perhaps because they studied earlier periods when length of the school year varied more widely and because state‐level data may be of sufficient size to contend with the potential effect of unobserved heterogeneity. Card and Krueger (1992) also presented results controlling for state effects, showing that the positive effect of a longer school year length vanishes within states and conditional on other school quality variables. Lee and Barro (2001) examined the effect of the amount of time spent in school during the year on student performance across countries while controlling for a variety of measures for school resources. They found no effects of the length of the school year on internationally comparable test scores. However, while this study attempted to identify the effect of instructional time on test scores by controlling for many characteristics and resources in each school and country, this method cannot rule out biases (due to school and country unobserved heterogeneity) that are correlated with instructional time and test scores. A more recent study, Pischke (2007), overcame potential selection and endogeneity problems by using a West German short school year in 1966–67 which reduced those school years by about two‐thirds for some students. This change increased grade repetition in primary school and lowered enrolment in higher secondary school tracks but it had no adverse effect on earnings and employment later in life. Hansen (2008) reported that more instructional time due to fewer snow‐related school day cancelations and delayed testing increased student performance in Colorado and Maryland. Marcotte and Hemelt (2008) reported that substantial snowfall (leading to fewer days spent at school) is associated with lower pupils’ performance in Maryland. Allensworth and Takako (2009) evaluate the efficacy of a double‐period algebra policy initiated in the Chicago Public Schools in 2003 and targeted to ninth grade students with test scores below the national median. The authors suggest that support courses improved algebra test scores for the target population, mainly for students close to the national median. Dobbie and Fryer (2011) find that charter schools in New York City that add 25% or more instructional time have an annual gain of 0.059 of a standard deviation in mathematics. However, the authors emphasise that their estimates of the relationship between instructional time and school effectiveness are unlikely to be causal given the lack of experimental variation in instructional time school inputs. However, Fryer (2012) reports similar size effects of instructional time in Houston’s public schools. The results I present in this article show that instructional time has a positive and significant effect on the academic achievements of pupils. However, the estimates are much lower than the ‘naïve’ OLS estimates which overstate the extent to which countries like the US might ‘catch up’ to other developed nations by increasing instructional time. The size of the estimated effects is modest to large. On average, a one‐hour increase per week in mathematics, science or language instruction raises the test score in these subjects by 0.06 of a standard deviation of the distribution of test scores. I also find that the results were heterogeneous across groups, and that the effect of instructional time is larger for girls, immigrants and pupils from low socio‐economic status families. In addition, while estimates based on the sample of the former Soviet Eastern European countries are very similar to the average effect obtained from the sample of OECD developed countries, the evidence based on a sample of developing countries suggests a much lower effect of additional instructional time on test scores. I find that on average, one additional instructional hour in developing countries improves test scores by 0.025 SD of the test score distribution. Overall, the main results presented in this article are very robust to a variety of robustness checks with respect to the identification assumptions and to threats to their validity. In addition, this evidence is almost identical to related results I obtained with data from Israel using two different identification strategies (Lavy, 2012). In that paper, the first method was identical to the one used in this article, and the second stemmed from a natural experiment that provided an opportunity to exploit a sharp change in the method of funding schools in Israel. Remarkably, the results from the research in Israel and the results presented in this research in an international context are almost identical. Moreover, the estimate of the effect of instructional time obtained from the PISA is also very close to the estimate presented in Dobbie and Fryer (2011) and Fryer (2012). This various estimates suggest an apparent ‘empirical regularity’ in the relationship between instructional time and test scores. However, it should be noted that the pupil fixed effect framework used in this paper relies on some assumptions that reduce the strength of the identification of causal relationships relative to a research design based on a randomised control trial, a regression discontinuity model or a valid instrumental variable. In the latter part of the article, I investigate whether the estimated effect of instructional time varies by certain characteristics of the labour market for teachers and of the school environment. I use information from PISA 2006 about school accountability measures and the degree of school autonomy, such as the role of schools in hiring and firing teachers and in determining wages of teachers. The main effects of these characteristics, which vary by school, are absorbed in the estimation by the school fixed effects. However, I am able to estimate the effect of their interactions with instructional time in each subject. The evidence suggests that the productivity of instructional time is higher in schools that operate under well‐defined accountability measures, and in schools that enjoy extensive autonomy in budgetary decisions and in hiring and firing teachers. These findings emphasise the importance of quality and quantity of instructional time in bridging the gaps in student achievement across countries. The rest of the article is organised as follows: Section 1 describes the identification strategy. Section 2 presents the data, the construction of the analysis samples and the various pieces of evidence that assess the validity of the identification strategy. Section 3 reports the pupil fixed effects estimates of the effect of instructional time in each subject using the three international samples of countries. The Section also shows results about the correlations of the average productivity of instructional time with schools’ and teachers’ labour market characteristics. Section 4 presents conclusions. 1. Empirical Strategy The effects of unobserved correlated factors usually confound the effect of instructional time on students’ outcomes. Such correlations could result if self‐selection and sorting of students across schools are affected by school resources, or if there is a correlation between school instructional time and other characteristics of the school that may affect students’ outcomes. One possible method to account for both sources of confounding factors in the estimation of instructional time is to rely on within‐student variations in instructional time across various subjects of study.4 Based on this approach, I examine whether differences in students between subjects are systematically associated with differences between subjects in instructional time. The basic idea for identification is that the student characteristics, ability and the school environment are the same for all three subjects except for the fact that some subjects receive more instructional time than others. Of course, it could be that at the school level such variation is not purely random. However, the cause of such selection across schools is constant for students in each school and therefore does not vary within each student. Based on this approach, I present within‐student estimates of the effect of instructional time on individual test scores using the following panel data specification, Aijk=μi+λHkj+betaXij+deltaSj+(ϵj+ηk)+uijk,(1) Where Aijk is the achievement of the ith student, in the jth school, in the kth subject, Hkj is instructional time in the kth subject in the jth school, X is a vector of characteristics of the ith student in the jth school and Sj is a vector of characteristics of the jth school. εj and ηk represent the unobserved characteristics of the school and the subject, respectively, and uijk is the remaining unobserved error term. The student fixed effects μi captures the individual’s family background, underlying ability, motivation and other constant non‐cognitive skills. Note that controlling for this individual fixed effect, in combination with within‐student variation across subjects’ test scores, controls for school fixed effects εj. In other words, exploiting within‐student variation allows me to control for a number of sources of potential biases related to unobserved characteristics of the school, the student or their interaction. In some situations, students might be placed or be sorted according to their ability across schools that provide more (or less) instructional time in some subjects. For instance, if more talented students attend better schools that provide more instructional hours overall in each subject, it would cause γ to be biased downward unless one were to account for student and school fixed effects. The bias would have an opposite sign if the less talented students were exposed to more instructional time. However, identification of the effect of instructional time based on a comparison of the performance of the same student in different subjects is immune to these potential biases. Several additional remarks about this identification strategy merit additional comment. First, the necessary assumption for this identification strategy is that the effect of instructional time is the same for all subjects, implying that γ cannot vary by subject. This assumption can be violated if the production function for knowledge differs by subjects at different ages. For example, reading literacy might yield high returns per hour of instruction when children are young while the return to mathematics instruction might be higher at later age. Although the restriction of equal productivity of instruction time across subjects is plausible when children are at age 15, in this article I provide some evidence to support this conjecture. Second, the effect of instructional time is ‘net’ of instructional time spillovers across subjects (e.g. instruction time in language might influence pupils’ test scores in mathematics). Third, the pupil fixed effect framework does not preclude the possibility that pupils select or are sorted across schools partly based on subject‐specific instructional time. For example, pupils who have high ability in mathematics may select or be placed in a school that specialises in mathematics, and they may receive more instructional time in mathematics as a result. This might be the case in a charter school that focuses on mathematics, and therefore attracts students with a particular gap between their mathematics and language skills. Such school might also have a particularly strong mathematics faculty and therefore may choose to have more mathematics instruction time for students. However, this latter issue may be less of a concern in the PISA sample for several reasons. First, since such tracking is largely conducted within schools, and I measure instructional time in each subject by the school‐level means and not by the class means or even the within school programme level means. Second, the pupils in the sample are 15‐years old and most are still in ninth grade. In most countries, ninth grade is part of middle school or lower secondary school, while schools that specialise in a given subject are mostly upper secondary schools, from 10th grade on. Third, I am able to stratify the sample according to good proxies of whether the school sorts and selects students based on subject‐specific considerations. For example, I observe in the PISA data information about whether admission to a school takes into account the student’s academic record, or the student’s need or desire for a special programme. I also note whether a school uses tracking in forming classes and whether it is a public or a private school. I assume that a school that does not use academic ability as an admission criterion, or does not take into account student’s desire for a particular programme, will most likely not select students on subject‐specific considerations. Such selection is also less likely to take place in schools that do not use any form of tracking by ability, or in public schools. Indeed, the results that I present below are very similar across the various stratified samples based on schools’ admission and tracking policies, and whether the schools are private or public, suggesting that this issue is not a source of bias. In the next Section, I describe in more detail the data that I use for the analysis. 2. Data The Programme for International Student Assessment, known by its acronym PISA, provides regular data on the OECD country education systems and the knowledge and skills of their students. The first survey was in 2000, the second in 2003 and the third in 2006. More than 50 countries have taken part in PISA so far, and it is the only international education survey to measure the knowledge and skills of 15‐year olds, an age at which students in most countries are nearing the end of their compulsory time in school. PISA does not examine students’ mastery of specific school curricula. Instead, it evaluates students’ ability to apply knowledge and skills in key subject areas and their ability to analyse reason and communicate effectively as they examine, interpret and solve problems. PISA measures student performance in language, mathematics and science literacy and asks students about their motivations, beliefs about themselves and learning strategies. All OECD member countries participated in the first three PISA surveys along with certain partner countries. In total, 43 countries took part in PISA 2000, 41 in PISA 2003 and 58 in PISA 2006.5 Each participating OECD country has a PISA Governing Board representative who is appointed by the country’s education ministry. Guided by the OECD’s education objectives the Board determines the policy priorities for PISA and makes sure that these are respected during the PISA surveys. For each survey, an international contractor (usually a testing and assessment agency) is responsible for the survey design and implementation. Working with the OECD Secretariat, the PISA Governing Board and the international contractor, the PISA National Project Managers oversee the implementation in each participating country. PISA has Subject Matter Expert Groups for its three key areas of testing – language, mathematics and science literacy – as well as for other subjects when appropriate.6 These groups include world experts in each area and together they design the theoretical framework for each PISA survey. The international contractor randomly selects schools in each country. The tests are administered to students who are between 15 years three months and 16 years two months of age at the time of the test, rather than to students in a specific year of school. This average age of 15 was chosen since at this age young people in most OECD countries are nearing the end of compulsory education. The selection of schools aims to be representative of the respective country’s population of schools and students. The tests are made up of both multiple‐choice questions and questions requiring students to construct their own responses. All PISA countries are invited to submit questions to the international contractor; in addition, the international contractor also writes some questions. The international contractor and participating countries review the questions and carefully check them for cultural bias. PISA uses only those questions that have been approved unanimously. The material is organised around texts and sometimes includes pictures, graphs or tables setting out real‐life situations. Each PISA survey includes about seven hours of test material and each student takes a two‐hour test, with the actual combination of test materials different for every student. Students also answer a 20 to 30‐minute background questionnaire, providing information about themselves, their homes and their attitudes to learning. In addition, school principals are given a 20‐minute questionnaire about their schools. Each country has its own group of test markers, overseen by the country’s National Project Manager. They mark the PISA tests using a guide developed by the international contractor and the PISA subject experts (with input from all participating countries). Other experts crosscheck the corrections. The results are then sent to the international contractor, who in turn transmits the final data to the OECD Secretariat. The average score among OECD countries is 500 points, and the standard deviation is 100 points. The results from PISA can be compared across the surveys, as can some of the background questionnaire items. Table 1 reports the distribution of instructional time in each of the three international samples of countries in the 2006 PISA based on the pupil‐level data. Each pupil replied to the following question: ‘How much time do you typically spend per week studying the following subjects in regular lessons at school?’7 The student could choose from the following options: no time, less than two hours a week, two or more but less than four hours a week, four or more but less than six hours a week, or more than six hours a week. I merged the first two options into one joint category as ‘less than two hours a week’ and used the other categories as set out. I computed the school average in each subject using the mid values of each range. Since the PISA data allow for overall instruction time per week in all subjects to be combined, I have aggregated and averaged this information at the country annual level for all OECD countries. A high correlation emerges between these country means and the administrative data on total annual hours of instruction in secondary schooling as reported in the OECD report, ‘Education at Glance’. Table 1 Means and Standard Deviations of Instructional Time in OECD, Eastern European and Developing Countries . . . Proportion of pupils by weekly instruction time . Subject . Mean value . SD . <2 hours . 2–3 hours . 4–5 hours . 6 hours+ . Panel (a): 22 OECD countries All subjects 3.38 1.48 13.16 40.43 36.45 9.97 Mathematics 3.53 1.38 8.72 39.54 43.14 8.60 Science 3.06 1.57 21.14 42.72 25.53 10.61 Reading 3.54 1.44 9.61 39.02 40.66 10.71 Panel (b): 14 Eastern European countries All subjects 3.05 1.56 22.51 39.59 29.29 8.61 Mathematics 3.30 1.48 15.36 38.97 37.59 8.08 Science 2.77 1.68 33.38 37.21 17.53 11.88 Reading 3.08 1.45 18.79 42.59 32.75 5.86 Panel (c): 13 Developing countries All subjects 3.23 1.71 22.86 34.72 27.51 14.90 Mathematics 3.48 1.69 18.72 30.73 34.06 16.50 Science 2.97 1.74 29.03 37.17 18.53 15.27 Reading 3.24 1.65 20.85 36.27 29.94 12.95 . . . Proportion of pupils by weekly instruction time . Subject . Mean value . SD . <2 hours . 2–3 hours . 4–5 hours . 6 hours+ . Panel (a): 22 OECD countries All subjects 3.38 1.48 13.16 40.43 36.45 9.97 Mathematics 3.53 1.38 8.72 39.54 43.14 8.60 Science 3.06 1.57 21.14 42.72 25.53 10.61 Reading 3.54 1.44 9.61 39.02 40.66 10.71 Panel (b): 14 Eastern European countries All subjects 3.05 1.56 22.51 39.59 29.29 8.61 Mathematics 3.30 1.48 15.36 38.97 37.59 8.08 Science 2.77 1.68 33.38 37.21 17.53 11.88 Reading 3.08 1.45 18.79 42.59 32.75 5.86 Panel (c): 13 Developing countries All subjects 3.23 1.71 22.86 34.72 27.51 14.90 Mathematics 3.48 1.69 18.72 30.73 34.06 16.50 Science 2.97 1.74 29.03 37.17 18.53 15.27 Reading 3.24 1.65 20.85 36.27 29.94 12.95 Notes The first column shows the mean of instruction time per week and the second column presents the respective standard deviations. The third to sixth columns present the proportion of pupils by the amount of weekly hours of instruction time. The sample in panel (a) includes 22 OECD developed countries: Australia, Austria, Belgium, Canada, Germany, Denmark, Spain, Finland, France, Greece, Ireland, Iceland, Italy, Japan, Luxembourg, Netherlands, Norway, New Zealand, Portugal, Sweden, Switzerland, UK. Panel (b) includes 14 countries of Eastern Europe: Bulgaria, Croatia, Czech Republic, Estonia, Hungary, Latvia, Lithuania, Montenegro, Poland, Romania, Russian Federation, Serbia, Slovak Republic, Slovenia. Panel (c) includes 13 developing countries: Argentina, Azerbaijan, Brazil, Chile, Colombia, Indonesia, Jordan, Kyrgyzstan, Mexico, Thailand, Tunisia, Turkey, Uruguay. Open in new tab Table 1 Means and Standard Deviations of Instructional Time in OECD, Eastern European and Developing Countries . . . Proportion of pupils by weekly instruction time . Subject . Mean value . SD . <2 hours . 2–3 hours . 4–5 hours . 6 hours+ . Panel (a): 22 OECD countries All subjects 3.38 1.48 13.16 40.43 36.45 9.97 Mathematics 3.53 1.38 8.72 39.54 43.14 8.60 Science 3.06 1.57 21.14 42.72 25.53 10.61 Reading 3.54 1.44 9.61 39.02 40.66 10.71 Panel (b): 14 Eastern European countries All subjects 3.05 1.56 22.51 39.59 29.29 8.61 Mathematics 3.30 1.48 15.36 38.97 37.59 8.08 Science 2.77 1.68 33.38 37.21 17.53 11.88 Reading 3.08 1.45 18.79 42.59 32.75 5.86 Panel (c): 13 Developing countries All subjects 3.23 1.71 22.86 34.72 27.51 14.90 Mathematics 3.48 1.69 18.72 30.73 34.06 16.50 Science 2.97 1.74 29.03 37.17 18.53 15.27 Reading 3.24 1.65 20.85 36.27 29.94 12.95 . . . Proportion of pupils by weekly instruction time . Subject . Mean value . SD . <2 hours . 2–3 hours . 4–5 hours . 6 hours+ . Panel (a): 22 OECD countries All subjects 3.38 1.48 13.16 40.43 36.45 9.97 Mathematics 3.53 1.38 8.72 39.54 43.14 8.60 Science 3.06 1.57 21.14 42.72 25.53 10.61 Reading 3.54 1.44 9.61 39.02 40.66 10.71 Panel (b): 14 Eastern European countries All subjects 3.05 1.56 22.51 39.59 29.29 8.61 Mathematics 3.30 1.48 15.36 38.97 37.59 8.08 Science 2.77 1.68 33.38 37.21 17.53 11.88 Reading 3.08 1.45 18.79 42.59 32.75 5.86 Panel (c): 13 Developing countries All subjects 3.23 1.71 22.86 34.72 27.51 14.90 Mathematics 3.48 1.69 18.72 30.73 34.06 16.50 Science 2.97 1.74 29.03 37.17 18.53 15.27 Reading 3.24 1.65 20.85 36.27 29.94 12.95 Notes The first column shows the mean of instruction time per week and the second column presents the respective standard deviations. The third to sixth columns present the proportion of pupils by the amount of weekly hours of instruction time. The sample in panel (a) includes 22 OECD developed countries: Australia, Austria, Belgium, Canada, Germany, Denmark, Spain, Finland, France, Greece, Ireland, Iceland, Italy, Japan, Luxembourg, Netherlands, Norway, New Zealand, Portugal, Sweden, Switzerland, UK. Panel (b) includes 14 countries of Eastern Europe: Bulgaria, Croatia, Czech Republic, Estonia, Hungary, Latvia, Lithuania, Montenegro, Poland, Romania, Russian Federation, Serbia, Slovak Republic, Slovenia. Panel (c) includes 13 developing countries: Argentina, Azerbaijan, Brazil, Chile, Colombia, Indonesia, Jordan, Kyrgyzstan, Mexico, Thailand, Tunisia, Turkey, Uruguay. Open in new tab According to Table 1, the means of instructional time in the developed OECD countries in mathematics, science and language are 3.53, 3.06 and 3.54 hours per week respectively. In the Eastern European sample, mean instructional time is lower than in the OECD countries in all subjects (3.30 for mathematics, 2.77 for science and 3.08 in language). These Eastern European figures are similar to the mean instructional time in the developing countries’ sample (3.48 for mathematics, 2.97 for science and 3.24 for language). Tables A1–A3 in Appendix A present the mean instructional time in each of the subjects for each of the countries included in the three samples of the 2006 PISA. As seen from these tables, large variation in instructional time exists on many levels. Variation emerges among the countries that make up the three broad multi‐country groups and also within individual countries among the different schools and various subjects. The PISA data – which include instruction time per week for the three subjects studied here, all other subjects and for the overall school week – explain some of the reasons behind the variations. For instance, the data show that a large part of the variation across subjects in instruction time is explained by variation across schools in total instruction time per week. Of course, the variation in total weekly instruction time across schools is caused by several obvious factors. For instance, governments may allocate resources to schools in a differential manner that is dependent on their socio‐economic background, and schools may receive different amounts of contributions from parents, the community or local school authority. Many of these factors vary at the school or country level and our identification strategy that uses the within school and pupil estimation strategies will account for them. When the variation in instructional time across subjects is related to the overall length of the school week, then the benefit of additional classes in mathematics, science or English is at the expense of time not being in school. However, the counterfactual of increasing instruction time in one of the three subjects could also be a reduction in instruction time of the other two subjects and in all other subject as well. Indeed the PISA data reveal that schools with the highest level of instruction time (observed in the data) in a given subject are more likely to have less than the maximum instruction time in each of the other two subjects and also of all other subjects. Similar evidence is reported in Rivkin and Schiman (2013) based on the PISA 2009 data. Certain additional issues regarding the data and methodology bear mention. Different countries vary in the length of the school year (number of weeks of study) but this factor is not a limitation in this case since the within school and pupil estimation strategies control for the length of the school year. Regarding instruction time, the measurements reflect the average in the school and not the hours reported by each student. It is also worth noting that the variation in subject instruction hours across students in the same school is not due to an endogenous decision of the students since the PISA sample in each country includes students in ninth and 10th grades; levels at which the curriculum of study in most or all countries is completely compulsory. Students may choose some courses only in the latter part of high school, perhaps at 11th and 12th grades. Variation in subject instruction hours could stem from tracking practices in schools, however, and I address this issue by directly examining the sensitivity of my results to differences in tracking practices across schools. Finally, Table A4 in Appendix A presents the means of the PISA test scores and the instruction time variables for all three samples of countries. The average test score in the developed OECD countries is 513.4 and the standard deviation in test scores between pupils is 84.4. The within‐student standard deviation in test scores is almost half as large, 38.8. Thus, there is considerable variation in test scores of the same pupil to explain. The average weekly instructional time per subject in the OECD sample is 3.38 hours and the within‐pupil standard deviation in instructional time is 1.02 – comparable in magnitude to the standard deviation in instructional time between students, 1.08. The Table also indicates that there are no dramatic differences between the OECD sample and the Eastern European or developing countries’ samples in the within‐ and between‐pupil standard deviations. 3. Results 3.1. Estimates of The Effects of Instructional Time in OECD Countries Table 2 reports the estimated coefficients of instructional time from subject‐specific test score regressions based on the sample of the OECD countries. For each subject, I report estimates from three specifications: Table 2 OLS Regressions of Standardised Test Scores on Instructional Time, OECD Sample . Mathematics . Science . Reading . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . I. Continuous hours Hours 0.217 0.280 0.244 0.262 0.384 0.339 0.046 0.154 0.125 (0.010) (0.012) (0.011) (0.008) (0.009) (0.008) (0.010) (0.013) (0.012) II. Categorical hours 2–3 hours 0.409 0.480 0.430 0.447 0.537 0.485 0.493 0.507 0.422 (0.082) (0.073) (0.067) (0.026) (0.028) (0.025) (0.104) (0.085) (0.077) 4 hours+ 0.637 0.701 0.619 0.771 0.905 0.804 0.557 0.649 0.534 (0.082) (0.074) (0.068) (0.030) (0.032) (0.030) (0.104) (0.087) (0.078) Country dummies ✓ ✓ ✓ ✓ ✓ ✓ Individual characteristics ✓ ✓ ✓ . Mathematics . Science . Reading . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . I. Continuous hours Hours 0.217 0.280 0.244 0.262 0.384 0.339 0.046 0.154 0.125 (0.010) (0.012) (0.011) (0.008) (0.009) (0.008) (0.010) (0.013) (0.012) II. Categorical hours 2–3 hours 0.409 0.480 0.430 0.447 0.537 0.485 0.493 0.507 0.422 (0.082) (0.073) (0.067) (0.026) (0.028) (0.025) (0.104) (0.085) (0.077) 4 hours+ 0.637 0.701 0.619 0.771 0.905 0.804 0.557 0.649 0.534 (0.082) (0.074) (0.068) (0.030) (0.032) (0.030) (0.104) (0.087) (0.078) Country dummies ✓ ✓ ✓ ✓ ✓ ✓ Individual characteristics ✓ ✓ ✓ Notes The Table shows OLS regression estimates of student test z‐scores on hours of school instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. In the first regression hours of instruction is a continuous variable. In the second regression hours enters the regression as binary variables for a particular number of hours learned per subject per week. The base (omitted) category is 1 hour. Controls on individual characteristics include binary variables for gender, fathers’ and mothers’ education and immigrant status. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Each regression contains 137,083 observations. Open in new tab Table 2 OLS Regressions of Standardised Test Scores on Instructional Time, OECD Sample . Mathematics . Science . Reading . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . I. Continuous hours Hours 0.217 0.280 0.244 0.262 0.384 0.339 0.046 0.154 0.125 (0.010) (0.012) (0.011) (0.008) (0.009) (0.008) (0.010) (0.013) (0.012) II. Categorical hours 2–3 hours 0.409 0.480 0.430 0.447 0.537 0.485 0.493 0.507 0.422 (0.082) (0.073) (0.067) (0.026) (0.028) (0.025) (0.104) (0.085) (0.077) 4 hours+ 0.637 0.701 0.619 0.771 0.905 0.804 0.557 0.649 0.534 (0.082) (0.074) (0.068) (0.030) (0.032) (0.030) (0.104) (0.087) (0.078) Country dummies ✓ ✓ ✓ ✓ ✓ ✓ Individual characteristics ✓ ✓ ✓ . Mathematics . Science . Reading . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . I. Continuous hours Hours 0.217 0.280 0.244 0.262 0.384 0.339 0.046 0.154 0.125 (0.010) (0.012) (0.011) (0.008) (0.009) (0.008) (0.010) (0.013) (0.012) II. Categorical hours 2–3 hours 0.409 0.480 0.430 0.447 0.537 0.485 0.493 0.507 0.422 (0.082) (0.073) (0.067) (0.026) (0.028) (0.025) (0.104) (0.085) (0.077) 4 hours+ 0.637 0.701 0.619 0.771 0.905 0.804 0.557 0.649 0.534 (0.082) (0.074) (0.068) (0.030) (0.032) (0.030) (0.104) (0.087) (0.078) Country dummies ✓ ✓ ✓ ✓ ✓ ✓ Individual characteristics ✓ ✓ ✓ Notes The Table shows OLS regression estimates of student test z‐scores on hours of school instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. In the first regression hours of instruction is a continuous variable. In the second regression hours enters the regression as binary variables for a particular number of hours learned per subject per week. The base (omitted) category is 1 hour. Controls on individual characteristics include binary variables for gender, fathers’ and mothers’ education and immigrant status. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Each regression contains 137,083 observations. Open in new tab (i) without any controls; (ii) with country fixed effects; and (iii) with country fixed effects and pupil characteristics. Panel (a) presents the OLS estimates when instructional time is measured in hours per week. Panel (b) presents estimates for measures of instructional time by category: less than two hours per week, 2–3 hours per week and 4+ hours. Note that the first category indicator (less than two hours per week) is the omitted group in the regression. The dependent variable is the standardised scores, computed by subtracting the mean of 500 from each score and dividing it by standard deviation of 100. Therefore, the estimated coefficients of interest are in terms of standard deviation of the test score distribution. Table 2 indicates that the estimated effects of instructional time on PISA test scores are all positive, very large, always significantly different from zero and not dramatically sensitive to the addition of controls to the regression. For example, the estimate for total instructional time in mathematics is 0.217 with no controls, 0.280 with country fixed effects and 0.244 with the addition of student’s controls. In science, the respective estimates are about 25–30% higher than in mathematics. Interestingly, the language estimates are much lower than in mathematics and science. However, since the OLS estimates do not include student fixed effects, we will show below that the results are highly biased upward. Panel (b) indicates that the largest marginal effect of one additional hour of instruction is when classroom hours are increased from less than two hours to two to three hours. For example, this change in instructional hours for mathematics is associated with an increase in test scores of nearly half of the standard deviation of between pupils test score distribution. In Table 3, column 1 presents estimates from regressions based on a pooled sample of all three subjects (with subject fixed effects included as controls) while column 2 presents estimates when student fixed effects are included. The OLS estimates in column 1 are very similar to the estimates presented in Table 2. The within‐student estimates in column 2 are all positive and much smaller than the OLS estimates in column 1 but they are still very precisely measured. Assuming a constant linear effect of instructional time, the effect of one additional hour of classroom instruction in the within‐student regression is associated with an increase of 0.058 SD on the PISA test. Table 3 Estimated Effect of Instructional Time on Standardised Test Scores, OECD Sample . Whole sample . Sample divided by school admission policy . . . . Academic record is irrelevant . Academic record taken in to account . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . I. Continuous hours Hours of instructional time 0.196 0.058 0.170 0.060 0.211 0.062 (0.007) (0.004) (0.009) (0.005) (0.017) (0.009) II. Categorical hours 2–3 hours 0.469 0.063 0.432 0.075 0.558 0.065 (0.027) (0.011) (0.038) (0.016) (0.057) (0.024) 4 hours+ 0.679 0.124 0.627 0.141 0.737 0.131 (0.029) (0.013) (0.040) (0.018) (0.060) (0.028) Number of observations 460,734 266,769 86,370 (b) Mathematics + science I. Continuous hours Hours of instructional time 0.255 0.071 0.218 0.086 0.276 0.076 (0.007) (0.006) (0.009) (0.008) (0.018) (0.013) II. Categorical hours 2–3 hours 0.457 0.094 0.401 0.108 0.552 0.122 (0.026) (0.015) (0.035) (0.026) (0.051) (0.034) 4 hours+ 0.739 0.170 0.657 0.207 0.805 0.187 (0.028) (0.018) (0.037) (0.028) (0.056) (0.041) Number of observations 307,156 177,846 57,580 . Whole sample . Sample divided by school admission policy . . . . Academic record is irrelevant . Academic record taken in to account . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . I. Continuous hours Hours of instructional time 0.196 0.058 0.170 0.060 0.211 0.062 (0.007) (0.004) (0.009) (0.005) (0.017) (0.009) II. Categorical hours 2–3 hours 0.469 0.063 0.432 0.075 0.558 0.065 (0.027) (0.011) (0.038) (0.016) (0.057) (0.024) 4 hours+ 0.679 0.124 0.627 0.141 0.737 0.131 (0.029) (0.013) (0.040) (0.018) (0.060) (0.028) Number of observations 460,734 266,769 86,370 (b) Mathematics + science I. Continuous hours Hours of instructional time 0.255 0.071 0.218 0.086 0.276 0.076 (0.007) (0.006) (0.009) (0.008) (0.018) (0.013) II. Categorical hours 2–3 hours 0.457 0.094 0.401 0.108 0.552 0.122 (0.026) (0.015) (0.035) (0.026) (0.051) (0.034) 4 hours+ 0.739 0.170 0.657 0.207 0.805 0.187 (0.028) (0.018) (0.037) (0.028) (0.056) (0.041) Number of observations 307,156 177,846 57,580 Notes The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. In the first regression hours of instruction is measured a continuous variable. In the second regression hours enters the regression as binary variables for a particular number of hours learned per subject per week. The base (omitted) category is 1 hour. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab Table 3 Estimated Effect of Instructional Time on Standardised Test Scores, OECD Sample . Whole sample . Sample divided by school admission policy . . . . Academic record is irrelevant . Academic record taken in to account . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . I. Continuous hours Hours of instructional time 0.196 0.058 0.170 0.060 0.211 0.062 (0.007) (0.004) (0.009) (0.005) (0.017) (0.009) II. Categorical hours 2–3 hours 0.469 0.063 0.432 0.075 0.558 0.065 (0.027) (0.011) (0.038) (0.016) (0.057) (0.024) 4 hours+ 0.679 0.124 0.627 0.141 0.737 0.131 (0.029) (0.013) (0.040) (0.018) (0.060) (0.028) Number of observations 460,734 266,769 86,370 (b) Mathematics + science I. Continuous hours Hours of instructional time 0.255 0.071 0.218 0.086 0.276 0.076 (0.007) (0.006) (0.009) (0.008) (0.018) (0.013) II. Categorical hours 2–3 hours 0.457 0.094 0.401 0.108 0.552 0.122 (0.026) (0.015) (0.035) (0.026) (0.051) (0.034) 4 hours+ 0.739 0.170 0.657 0.207 0.805 0.187 (0.028) (0.018) (0.037) (0.028) (0.056) (0.041) Number of observations 307,156 177,846 57,580 . Whole sample . Sample divided by school admission policy . . . . Academic record is irrelevant . Academic record taken in to account . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . I. Continuous hours Hours of instructional time 0.196 0.058 0.170 0.060 0.211 0.062 (0.007) (0.004) (0.009) (0.005) (0.017) (0.009) II. Categorical hours 2–3 hours 0.469 0.063 0.432 0.075 0.558 0.065 (0.027) (0.011) (0.038) (0.016) (0.057) (0.024) 4 hours+ 0.679 0.124 0.627 0.141 0.737 0.131 (0.029) (0.013) (0.040) (0.018) (0.060) (0.028) Number of observations 460,734 266,769 86,370 (b) Mathematics + science I. Continuous hours Hours of instructional time 0.255 0.071 0.218 0.086 0.276 0.076 (0.007) (0.006) (0.009) (0.008) (0.018) (0.013) II. Categorical hours 2–3 hours 0.457 0.094 0.401 0.108 0.552 0.122 (0.026) (0.015) (0.035) (0.026) (0.051) (0.034) 4 hours+ 0.739 0.170 0.657 0.207 0.805 0.187 (0.028) (0.018) (0.037) (0.028) (0.056) (0.041) Number of observations 307,156 177,846 57,580 Notes The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. In the first regression hours of instruction is measured a continuous variable. In the second regression hours enters the regression as binary variables for a particular number of hours learned per subject per week. The base (omitted) category is 1 hour. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab The other estimates presented in panel (a) suggest some non‐linearity in the effect of instructional time, with a larger effect in the range of 1–2 hours than at higher levels. The difference between the estimated effect of two to three hours of instruction versus the effect of up to two instruction hours is 0.0252 [= (0.063 points/2.5 hours)]. Similarly, the difference between the estimated effect of four or more hours of instruction versus the effect of up to two instruction hours is 0.0248 [= (0.124 points/5 hours)], both of which are lower than the average effect of 0.058. This suggests that the first two hours of instruction have the lowest effect. Interestingly, the results in Table 3 on the effects of instructional time are very similar to the results in Lavy (2012). In that paper, I report results based on the same method I use in this article and also based on an alternative identification strategy that relies on a natural experiment that exploit a sharp change in the funding method of schools in Israel. Remarkably, both of these two methods lead to identical point estimates for the effect of instructional time on core subjects test scores, and these two sets of estimates from the previous paper are almost identical to the results presented in this article.8 These similar findings strengthen the overall credibility of the results I present in this article and also their causal interpretation. The productivity of classroom hours might be different for different subjects. In order to check for such variation I estimate models based on the three possible samples that include only two of three subjects. The second panel of Table 3 presents estimates based on the sample that pools the mathematics and science test scores. The estimated effects of classroom hours obtained from this sample is higher, 0.071, about 22% higher than the respective estimate obtained from pooling all three subjects together. However, pooling mathematics and language test scores yields an estimate of 0.074 and pooling science and language yields an estimate of 0.043 (results available from the author upon request). The pattern that emerges from the OECD country group does not permit me to conclude whether the average productivity of instructional time is lower for any of the three subjects. However, the average (0.063) of the three estimates obtained from three samples that include only two of the three subjects is very close to the estimate (0.058) obtained by pooling all three subjects. It is also important to note that in Lavy (2012) I was able to estimate separately the effect for each subject and these estimates are very similar to each other and as noted above their mean is very close to the estimate we present here in Table 3. 3.2. Robustness of Main Results and Checks for Threats of Identification In this Section, I present a set of robustness checks and alternative specifications that support the causal interpretation of the findings reported in column 2 of Table 3. Since the variation in hours of instruction is at the school level, the first robustness check is based on a sample of schools instead of pupils. I present these results in Appendix Table A5. I obtain the variables at the school level by collapsing the pupil‐level data to the respective school‐level means. The pattern in this Table is very similar to Table 3. The OLS estimates in the two Tables are practically identical while the school fixed effect estimates based on the school‐level sample are slightly lower than the estimates based on student micro data. The estimate based on all three subjects is lower by 17% than the respective estimate in Table 3; the estimate based on mathematics and science only is lower by 9% than the respective estimate in Table 3.9 The second robustness check concerns whether the evidence in column 2 of Table 3 reflects some subject‐specific selection and sorting in some schools. It is based on the data available from the PISA school questionnaire about how much consideration is given in the admission decisions to student’s academic record and whether placements tests are used in this process.10 I expect that the validity of the identification strategy will be underscored here since my prior is that the sample of schools that do not pay any attention to applicants’ previous academic records and do not use any admission examinations should not be sensitive to endogenous sorting and selection. In columns 3–4 of Table 3, I report results from a sample of schools that do not consider a student’s prior academic record and in columns 5–6 I report estimates based on a sample of schools that consider student’s academic record for admission. Note that the sample of students in schools in which past academic achievements are irrelevant for admission is larger and accounts for about two‐thirds of the whole sample. The Table indicates that the estimates from this sample are only marginally different from those obtained from full sample: the OLS estimate is lower, 0.170 versus 0.196, and pupil fixed effect estimate is higher, 0.060 versus 0.058. Also, the OLS and the pupil fixed effect estimates in columns 5–6 are also only marginally different than the estimates obtained from the full. Overall, these results suggest that the type of admission process does not lead to differences that are statistically significant. This suggests that our results in column 2 are not biased by school‐sorting processes.11 Another potential source of selection bias is tracking pupils into classes within schools according to their ability. One can expect that schools practising such tracking will also tend to select and admit pupils based on subject‐specific strengths. If the strengths or specialisations of schools are correlated with hours of instruction in different subjects, a bias in the estimated effect of hours of instruction will occur. In Table 4, I present results for three different samples distinguished by schools’ tracking policies. Columns 1–2 show the estimates for a sample of schools that practise tracking at the class level where students in classes are grouped according to their ability. Columns 3–4 show the results based on a sample of schools that sort pupils into different ability study groups within classes. Columns 5–6 show the results based on a sample of schools that do not practise any form of pupil tracking. The OLS and the pupil fixed effect estimates in the first row in columns 1–2 are quite similar to the respective estimates presented in columns 3–4. This indicates that the two forms of tracking leads to similar results. However, the results of column 1–2 are 15% higher than the respective estimates in Table 3, and the results of columns 3–4 are about 7% higher than the estimates in Table 3. However, in both cases, these estimates are not significantly different from the point estimates obtained from the full sample. Finally, the effect of instruction hours on test scores in schools that practise no tracking at all is 0.052 which is not significantly different from the estimate from the full sample 0.058. However, these results are significantly lower than the estimates obtained for schools which practise tracking between classes. Table 4 Estimated Effect of Instructional Time on Standardised Test Scores by Tracking Status . Tracking by class . Track in class . No tracking . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . Hours of instructional time 0.199 0.066 0.190 0.062 0.200 0.052 (0.011) (0.005) (0.010) (0.006) (0.014) (0.007) Number of observations 212,169 201,138 160,188 . Tracking by class . Track in class . No tracking . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . Hours of instructional time 0.199 0.066 0.190 0.062 0.200 0.052 (0.011) (0.005) (0.010) (0.006) (0.014) (0.007) Number of observations 212,169 201,138 160,188 Notes Table 4 replicates Table 3 in samples defined by tracking status – whether the school tracks students by classes, within classes or not at all. The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of learning is a continuous variable. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab Table 4 Estimated Effect of Instructional Time on Standardised Test Scores by Tracking Status . Tracking by class . Track in class . No tracking . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . Hours of instructional time 0.199 0.066 0.190 0.062 0.200 0.052 (0.011) (0.005) (0.010) (0.006) (0.014) (0.007) Number of observations 212,169 201,138 160,188 . Tracking by class . Track in class . No tracking . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . Hours of instructional time 0.199 0.066 0.190 0.062 0.200 0.052 (0.011) (0.005) (0.010) (0.006) (0.014) (0.007) Number of observations 212,169 201,138 160,188 Notes Table 4 replicates Table 3 in samples defined by tracking status – whether the school tracks students by classes, within classes or not at all. The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of learning is a continuous variable. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab Another potential source of bias can originate from the inclusion of private schools in the PISA sample. For example, 18% of the schools in the OECD sample are classified as private. This could be of concern since private schools are more likely to base admission on previous academic record and on additional examinations, and to track pupils by ability. To address these concerns, I therefore estimated the effect of instruction hours based on a sample that included only the public schools in the PISA sample. The estimated effect of instruction school hours based on pooling together the mathematics, science and language test scores is 0.061, just barely higher than the estimate from a sample that included also the private schools (results available from the author upon request). Overall, the lack of any large, discernible differences in the effect of hours of instruction by admission or tracking policies of schools suggests that my estimates are not biased by unobservables correlated with sorting or selection of pupils based on subject‐specific hours of instruction. This is an important result since schools that admit pupils based on academic record or that track students by ability also tend to select and admit pupils based on subject‐specific strengths. If the strength or specialisation of schools is also correlated with hours of instruction in different subjects, it might bias the estimates of the effect of hours of instruction. For example, certain schools may come to be known as ‘mathematics‐oriented’ or ‘literature‐oriented’. The more effective teachers in each of these areas may gravitate to the schools that emphasise these subjects – perhaps because they like teaching students motivated in their subjects, or because they believe being the mathematics teacher in the mathematics‐oriented school confers higher prestige than being the mathematics teacher in a the literature‐oriented school. If these schools add more hours of instructions to their favourite subject of specialisation, then teachers’ quality will confound the effect of instruction time. Such specialised‐focus schools almost always select their students based on subject‐specific ability and motivation and often also use tracking. As a result, the robustness of the evidence presented above regarding patterns of admission and student selection criteria is reassuring that the effect of instruction time that I estimate is not capturing other effects such as teacher quality. Table 5 provides further evidence to support this conclusion. First, I add to the regressions control variables that are indicators of whether the school offers a special study programme in science or mathematics which may attract students with special interest and ability in those subjects. The set of controls is based on questions 20 and 22 in the PISA school questionnaire. These questions consist of indicators for school activities that promote student engagement with science (such as science clubs, science fairs, science competitions, extracurricular science projects, excursions and field trips). The motivation for including these control variables is that they most likely will eliminate a potential bias in the estimated effect of hours of instruction due to selection or sorting of students to schools based on special abilities and interest in science and mathematics. These results are presented in columns 1 and 2 of Table 5. Note that the OLS (column 1) and fixed effects (column 2) estimates, are almost identical to the respective estimates presented in columns 1–2 of Table 3. This suggests that the many schools that offer special programmes and activities in science and mathematics are not source of concern for bias. Table 5 Estimated Effects of Instruction Time on Standardised Test Scores, with Controls Included in the Regressions for Special Science Activities in School and for Scarcity of Teachers in Each Subject . Control added for . . Special science school activities . Scarcity of teachers in each subject . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.184 0.056 0.196 0.058 (0.007) (0.004) (0.007) (0.004) Number of observations 460,734 224,508 . Control added for . . Special science school activities . Scarcity of teachers in each subject . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.184 0.056 0.196 0.058 (0.007) (0.004) (0.007) (0.004) Number of observations 460,734 224,508 Notes The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of instruction is a continuous variable. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab Table 5 Estimated Effects of Instruction Time on Standardised Test Scores, with Controls Included in the Regressions for Special Science Activities in School and for Scarcity of Teachers in Each Subject . Control added for . . Special science school activities . Scarcity of teachers in each subject . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.184 0.056 0.196 0.058 (0.007) (0.004) (0.007) (0.004) Number of observations 460,734 224,508 . Control added for . . Special science school activities . Scarcity of teachers in each subject . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.184 0.056 0.196 0.058 (0.007) (0.004) (0.007) (0.004) Number of observations 460,734 224,508 Notes The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of instruction is a continuous variable. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab Another robustness check of our evidence is based on the data available in PISA (school questionnaire question 14) about lack of qualified teachers for each of the following subjects: science, mathematics, language and other subjects. I have added a control variable for whether the school’s capacity to provide instruction in a given subject is hindered by a lack of qualified teachers in that subject. The rationale for adding this control is that specialised schools with a particular strength in a given subject are less likely to struggle to find and hire qualified teachers. The OLS and pupil fixed effect estimates are presented in columns 3 and 4 in Table 5. They are almost identical to those presented in columns 1–2 of Table 3.12 These results suggest that a school’s ability to find qualified teachers is not a potential source of bias regarding our core results. 3.3. Heterogeneous Treatment Effects To gain further insights into the effect of instructional time, I explore heterogeneous effects of classroom hours for different subgroups. In Table 6, I report separate estimates for boys and for girls. The estimates show a positive impact of instructional time for both genders. In my preferred fixed effects specification, the effect is marginally higher (by 13%) for girls than for boys, but this difference is not significantly different from zero. This suggests that the benefits of additional instructional time are similar for both genders. Table 6 Estimated Effect of Instructional Time on Standardised Test Scores, by Gender, OECD Sample . Boys . Girls . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.202 0.050 0.186 0.056 (0.009) (0.004) (0.008) (0.004) Number of observations 224,508 236,226 . Boys . Girls . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.202 0.050 0.186 0.056 (0.009) (0.004) (0.008) (0.004) Number of observations 224,508 236,226 Notes The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of instruction is a continuous variable. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab Table 6 Estimated Effect of Instructional Time on Standardised Test Scores, by Gender, OECD Sample . Boys . Girls . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.202 0.050 0.186 0.056 (0.009) (0.004) (0.008) (0.004) Number of observations 224,508 236,226 . Boys . Girls . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . Hours of instructional time 0.202 0.050 0.186 0.056 (0.009) (0.004) (0.008) (0.004) Number of observations 224,508 236,226 Notes The Table shows OLS and FE regressions of student z‐scores on hours of instruction in a particular subject. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of instruction is a continuous variable. The sample includes 22 OECD developed countries (see notes to Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab In Table 7, I report results for two sub‐samples stratified by certain family characteristics: the average years of schooling of both parents and by immigrant status. In my preferred fixed effects specification, the productivity of instructional time is clearly higher (35%) for pupils from low‐education families. Also, the effect of additional instructional time for immigrants reveals a striking pattern. As compared to children of native parents, the benefits of additional instruction time are marginally higher (12%) for children of first‐generation immigrants, but they are much higher (30%) for second‐generation immigrants. This suggests that there are some heterogeneous effects of instructional time. Table 7 Heterogeneity in Estimated Effect of Instructional Time on Standardised Test Scores, OECD Sample . High parental education . Low parental education . Immigrants – first generation . Immigrants – second generation . OLS . Student FE . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Hours of instructional time 0.196 0.048 0.178 0.065 0.399 0.064 0.376 0.076 (0.009) (0.004) (0.007) (0.004) (0.020) (0.009) (0.020) (0.009) Number of observations 235,539 225,195 23,103 22,092 . High parental education . Low parental education . Immigrants – first generation . Immigrants – second generation . OLS . Student FE . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Hours of instructional time 0.196 0.048 0.178 0.065 0.399 0.064 0.376 0.076 (0.009) (0.004) (0.007) (0.004) (0.020) (0.009) (0.020) (0.009) Number of observations 235,539 225,195 23,103 22,092 Notes The Table reports estimates of the effect of instruction time on test z‐scores for the following sub‐samples: pupils from high education families, pupils from low‐education families, first‐generation immigrants and second‐generation immigrants. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of instruction is a continuous variable. The sample includes 22 OECD developed countries (see notes in Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab Table 7 Heterogeneity in Estimated Effect of Instructional Time on Standardised Test Scores, OECD Sample . High parental education . Low parental education . Immigrants – first generation . Immigrants – second generation . OLS . Student FE . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Hours of instructional time 0.196 0.048 0.178 0.065 0.399 0.064 0.376 0.076 (0.009) (0.004) (0.007) (0.004) (0.020) (0.009) (0.020) (0.009) Number of observations 235,539 225,195 23,103 22,092 . High parental education . Low parental education . Immigrants – first generation . Immigrants – second generation . OLS . Student FE . OLS . Student FE . OLS . Student FE . OLS . Student FE . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Hours of instructional time 0.196 0.048 0.178 0.065 0.399 0.064 0.376 0.076 (0.009) (0.004) (0.007) (0.004) (0.020) (0.009) (0.020) (0.009) Number of observations 235,539 225,195 23,103 22,092 Notes The Table reports estimates of the effect of instruction time on test z‐scores for the following sub‐samples: pupils from high education families, pupils from low‐education families, first‐generation immigrants and second‐generation immigrants. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Each regression also includes subject fixed effects. Hours of instruction is a continuous variable. The sample includes 22 OECD developed countries (see notes in Table 1). Standard errors in parentheses are clustered at the school level. Open in new tab 3.4. Evidence From Middle‐ and Low‐Income Countries In this sub‐section, I explore whether the effects of instructional time differ by country income. The first panel in Table 8 presents evidence that is based on a sample of 14 middle‐income countries from the former Soviet Bloc: Bulgaria, Czech Republic, Estonia, Croatia, Hungary, Lithuania, Latvia, Montenegro, Poland, Romania, Russian Federation, Serbia, Slovak Republic and Slovenia. The mean test scores of the three subjects in this sample are all lower than the respective means of the OECD countries. The mean test scores for this sample are: 472.4 for mathematics, 480.4 for science and 458.3 for language (see Table A2 in the online Appendix). The standard deviations in the pupil‐level distribution of test scores are 97.8 in mathematics, 97.9 in science and 105.0 in language – similar to those in the OECD sample. Table 8 Estimates of Effect of Instructional Time on Standardised Test Scores, Samples of Eastern European and Developing and Countries . All . Boys . Girls . High parental education . Low parental education . Immigrant 1st Gen. . Immigrant 2nd Gen. . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . Eastern European Countries OLS 0.382 0.389 0.372 0.412 0.334 0.263 0.357 (0.013) (0.014) (0.014) (0.016) (0.013) (0.033) (0.027) Fixed effects 0.061 0.051 0.065 0.050 0.067 0.055 0.073 (0.006) (0.006) (0.006) (0.007) (0.006) (0.021) (0.019) Number of observations 177,015 84,612 92,403 78,006 99,009 3,525 5,604 Developing countries OLS 0.366 0.382 0.352 0.433 0.296 0.581 0.515 (0.012) (0.014) (0.012) (0.014) (0.012) (0.053) (0.042) Fixed effects 0.030 0.024 0.033 0.034 0.026 0.186 0.111 (0.008) (0.009) (0.009) (0.009) (0.009) (0.047) (0.039) Number of observations 238,938 108,927 130,011 76,970 82,322 1,642 2,210 . All . Boys . Girls . High parental education . Low parental education . Immigrant 1st Gen. . Immigrant 2nd Gen. . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . Eastern European Countries OLS 0.382 0.389 0.372 0.412 0.334 0.263 0.357 (0.013) (0.014) (0.014) (0.016) (0.013) (0.033) (0.027) Fixed effects 0.061 0.051 0.065 0.050 0.067 0.055 0.073 (0.006) (0.006) (0.006) (0.007) (0.006) (0.021) (0.019) Number of observations 177,015 84,612 92,403 78,006 99,009 3,525 5,604 Developing countries OLS 0.366 0.382 0.352 0.433 0.296 0.581 0.515 (0.012) (0.014) (0.012) (0.014) (0.012) (0.053) (0.042) Fixed effects 0.030 0.024 0.033 0.034 0.026 0.186 0.111 (0.008) (0.009) (0.009) (0.009) (0.009) (0.047) (0.039) Number of observations 238,938 108,927 130,011 76,970 82,322 1,642 2,210 Notes The Table shows OLS and fixed effect regressions of z‐scores on hours of instructional time (continuous measure) for two samples. The first sample includes the following 14 Eastern European countries: Bulgaria, Croatia, Czech Republic, Estonia, Hungary, Latvia, Lithuania, Montenegro, Poland, Romania, Russian Federation, Serbia, Slovak Republic, Slovenia. The second sample includes the following 13 developing countries: Argentina, Azerbaijan, Brazil, Chile, Colombia, Indonesia, Jordan, Kyrgyzstan, Mexico, Thailand, Tunisia, Turkey, Uruguay. Scores are standardised using a mean of 500 and a standard deviation of 100. Open in new tab Table 8 Estimates of Effect of Instructional Time on Standardised Test Scores, Samples of Eastern European and Developing and Countries . All . Boys . Girls . High parental education . Low parental education . Immigrant 1st Gen. . Immigrant 2nd Gen. . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . Eastern European Countries OLS 0.382 0.389 0.372 0.412 0.334 0.263 0.357 (0.013) (0.014) (0.014) (0.016) (0.013) (0.033) (0.027) Fixed effects 0.061 0.051 0.065 0.050 0.067 0.055 0.073 (0.006) (0.006) (0.006) (0.007) (0.006) (0.021) (0.019) Number of observations 177,015 84,612 92,403 78,006 99,009 3,525 5,604 Developing countries OLS 0.366 0.382 0.352 0.433 0.296 0.581 0.515 (0.012) (0.014) (0.012) (0.014) (0.012) (0.053) (0.042) Fixed effects 0.030 0.024 0.033 0.034 0.026 0.186 0.111 (0.008) (0.009) (0.009) (0.009) (0.009) (0.047) (0.039) Number of observations 238,938 108,927 130,011 76,970 82,322 1,642 2,210 . All . Boys . Girls . High parental education . Low parental education . Immigrant 1st Gen. . Immigrant 2nd Gen. . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . Eastern European Countries OLS 0.382 0.389 0.372 0.412 0.334 0.263 0.357 (0.013) (0.014) (0.014) (0.016) (0.013) (0.033) (0.027) Fixed effects 0.061 0.051 0.065 0.050 0.067 0.055 0.073 (0.006) (0.006) (0.006) (0.007) (0.006) (0.021) (0.019) Number of observations 177,015 84,612 92,403 78,006 99,009 3,525 5,604 Developing countries OLS 0.366 0.382 0.352 0.433 0.296 0.581 0.515 (0.012) (0.014) (0.012) (0.014) (0.012) (0.053) (0.042) Fixed effects 0.030 0.024 0.033 0.034 0.026 0.186 0.111 (0.008) (0.009) (0.009) (0.009) (0.009) (0.047) (0.039) Number of observations 238,938 108,927 130,011 76,970 82,322 1,642 2,210 Notes The Table shows OLS and fixed effect regressions of z‐scores on hours of instructional time (continuous measure) for two samples. The first sample includes the following 14 Eastern European countries: Bulgaria, Croatia, Czech Republic, Estonia, Hungary, Latvia, Lithuania, Montenegro, Poland, Romania, Russian Federation, Serbia, Slovak Republic, Slovenia. The second sample includes the following 13 developing countries: Argentina, Azerbaijan, Brazil, Chile, Colombia, Indonesia, Jordan, Kyrgyzstan, Mexico, Thailand, Tunisia, Turkey, Uruguay. Scores are standardised using a mean of 500 and a standard deviation of 100. Open in new tab The Table indicates that the OLS estimates of the effect of instructional time are much higher in this sample relative to the results for the OECD developed countries. For example, the OLS estimate for the continuous hours of instruction variable is 0.38.2, versus 0.196 in the OECD sample. However, the within‐pupil estimate is 0.061 which is almost identical to the respective OECD estimate. This suggests that the selection or endogeneity in school resources in the Eastern European countries is much more important. In terms of heterogeneity, in my preferred fixed‐effect specification the estimate for girls is again higher (26%) than for boys, and it is much higher (33%) for pupils from low‐education families. Also, the greater effect of hours of instruction on second‐generation immigrants is again evident as in the OECD sample. The second panel in Table 8 presents estimates based on a sample of 13 developing countries: Argentina, Azerbaijan, Brazil, Chile, Colombia, Indonesia, Jordan, Kyrgyzstan, Mexico, Thailand, Tunisia, Turkey and Uruguay.13 The mean test scores for this sample of developing countries are: 398.5 in mathematics, 403.4 in science and 397.1 in language. This implies that their mean test scores are 21% lower than in the OECD countries. The standard deviation in the pupil‐level distribution of test scores is around 100 in the three subjects. The panel (b) estimates show much lower instructional time productivity than the estimates of the OECD or the middle‐income Eastern European countries. The effect of a change of one classroom hour is only 0.029 points in our fixed effects specification. This effect size is about half the effect size estimated for the OECD developed economies and for the Eastern European sample.14 In terms of heterogeneity, instructional time in the sample of the developing countries is much more effective in improving test scores of girls (38% higher than for boys) and of first‐generation immigrants (67% higher than second‐generation immigrants). However, in this sample the effect of additional instructional time is 26% lower for pupils from low‐education families than for pupils from highly educated families. Our Table 8 results can be used to compute what proportion of the gap in knowledge and test scores between the developed and developing countries can be explained or eliminated by bridging the gap in instructional time and in its productivity in the different subjects. According to Table 1, the mean instructional times in mathematics, science and language in the OECD countries are 3.5, 3.1 and 3.5 hours per week; in the poor countries they are 3.5, 3.0 and 3.2 hours per week respectively. A comparison shows that the gaps in instructional time are relatively small. The two distinct groups of countries spend almost the same amount of time on mathematics and science, and the wealthy OECD countries spend only marginally more time on language (9%). At the same time, the mean test scores in the developing countries sample are about 100 points lower: 398.5 versus 506.5 in mathematics, 403.4 versus 508.6 in science and 397.1 versus 497.7 in language (see Tables A1 and A3). Therefore, the gap in mean test scores between the developing and the OECD developed countries is very large (more than 20%) and its size is about one standard deviation in each of the subjects. Obviously, equalising the instructional time in the poor countries to the level in rich countries will not significantly eliminate the test score gap between these two parts of the world. However, the poor countries can reduce this gap by raising the marginal productivity of instructional time to the level in rich countries. The average instructional time in the three subjects in the developing countries sample is 0.032. Converging to the productivity of instructional time in the OECD countries will therefore raise achievements in each of the three subjects by 0.10 of a standard deviation. In the next Section, I explore the potential impact of changing structural features of the education system in developing countries as these changes may lead to a convergence of the productivity of instructional time to the level in the OECD countries. 3.5. Correlates of Productivity Differences of Instructional Time Across Countries The productivity of instructional time is endogenous and it can be affected by a wide variety of factors – for example, the quantity and quality of other school inputs, teachers’ education and training, class size, computers, science laboratories and other similar factors. All of these inputs might interact with learning hours and shape the productivity of instructional time in school. Similarly, various structural features of the education system may affect teachers’ and school principals’ effort and efficiency, which should influence the productivity of instructional time. These structural features include accountability measures that publish school league tables based on national tests, or policies that use pupils’ performance measures to determine school staff compensation. Another relevant structural characteristic of the education system is the degree of autonomy that schools have in hiring and dismissing teachers. We can presume that more flexibility in staffing decision might lead to a better match between teachers and schools and create an environment that induces more effort and responsibility among school staff. Many aspects and characteristics of this dimension of the educational landscape were surveyed as part of the 2006 PISA, through a survey of school head masters and the gathering of data on various indicators in a comparable manner for all the participating countries. For instance, PISA includes three binary indicators of school accountability measures: whether achievements data are posted publicly; whether achievements data are used in evaluation of school principal performance; and whether achievements data are used in evaluation of teachers’ performance. Another index ranks the school’s quality of educational resources that is based on teachers’ qualifications, class size and the quality of other school inputs. Two additional indices measure the degree of school autonomy. The first measures the school’s autonomy in resource allocation: hiring and firing teachers, determining teachers’ starting salaries and potential raises and determining and allocating the budget. The second index measures the school’s responsibility for curriculum and assessment including school independence in deciding the courses offered and their content, the textbooks used and the method of assessing pupil performance. Table 9 presents the estimated coefficients from these regressions. I focus on the OECD sample since it is the largest in terms of number of countries and schools in the sample and due to the relatively large variation in structure and characteristics of schools. The first column presents the means for the school measures. The Table indicates that accountability is not widespread among OECD countries as only 33.5% of the schools post their mean achievement publicly and even fewer schools use them to evaluate school principals (22%) or teachers (29%). The relative size for the means of the other indices is harder to interpret. Table 9 Estimated Effects of School Characteristics Interacted with Instructional Hours, OECD Countries . . Separate specification . Joint specification . Index . Index’s mean . Hours main effect . Hours interacted with index . Hours interacted with index . Hours interacted with index . . (1) . (2) . (3) . (4) . (5) . Achievement data are posted publicly (e.g. in the media). (binary variable) 0.335 0.050 0.027 0.020 0.025 (0.472) (0.004) (0.008) (0.009) (0.009) Achievement data are used in evaluation of the principal’s performance (binary variable) 0.216 0.052 0.021 0.022 0.023 (0.411) (0.004) (0.009) (0.011) (0.011) Achievement data are used in evaluation of teachers’ performance (binary variable) 0.294 0.055 0.003 −0.012 −0.009 (0.456) (0.005) (0.008) (0.010) (0.010) Quality of educational resources: index, (range −3.45 to 2.1) 0.150 0.058 0.001 0.004 0.004 (0.989) (0.004) (0.004) (0.004) (0.004) School responsibility for resource allocation: Index, (range −1.1 to 2.0) −0.058 0.059 0.012 0.008 0.009 (0.946) (0.004) (0.004) (0.004) (0.004) School responsibility for curriculum and assessment: index (range −1.4 to 1.3) 0.052 0.058 −0.002 −0.005 −0.006 (0.964) (0.004) (0.004) (0.004) (0.004) School governing board influences staffing (binary variable) 0.363 0.050 0.026 0.012 (0.481) (0.005) (0.008) (0.009) School governing board influences budget (binary variable) 0.706 0.038 0.030 0.018 (0.455) (0.007) (0.008) (0.009) School governing board influences instructional content (binary variable) 0.162 0.060 −0.006 −0.002 (0.368) (0.004) (0.010) (0.011) School governing board influences assessment (binary variable) 0.219 0.060 −0.008 −0.008 (0.413) (0.005) (0.008) (0.009) Hours main effect 0.047 0.033 (0.007) (0.010) . . Separate specification . Joint specification . Index . Index’s mean . Hours main effect . Hours interacted with index . Hours interacted with index . Hours interacted with index . . (1) . (2) . (3) . (4) . (5) . Achievement data are posted publicly (e.g. in the media). (binary variable) 0.335 0.050 0.027 0.020 0.025 (0.472) (0.004) (0.008) (0.009) (0.009) Achievement data are used in evaluation of the principal’s performance (binary variable) 0.216 0.052 0.021 0.022 0.023 (0.411) (0.004) (0.009) (0.011) (0.011) Achievement data are used in evaluation of teachers’ performance (binary variable) 0.294 0.055 0.003 −0.012 −0.009 (0.456) (0.005) (0.008) (0.010) (0.010) Quality of educational resources: index, (range −3.45 to 2.1) 0.150 0.058 0.001 0.004 0.004 (0.989) (0.004) (0.004) (0.004) (0.004) School responsibility for resource allocation: Index, (range −1.1 to 2.0) −0.058 0.059 0.012 0.008 0.009 (0.946) (0.004) (0.004) (0.004) (0.004) School responsibility for curriculum and assessment: index (range −1.4 to 1.3) 0.052 0.058 −0.002 −0.005 −0.006 (0.964) (0.004) (0.004) (0.004) (0.004) School governing board influences staffing (binary variable) 0.363 0.050 0.026 0.012 (0.481) (0.005) (0.008) (0.009) School governing board influences budget (binary variable) 0.706 0.038 0.030 0.018 (0.455) (0.007) (0.008) (0.009) School governing board influences instructional content (binary variable) 0.162 0.060 −0.006 −0.002 (0.368) (0.004) (0.010) (0.011) School governing board influences assessment (binary variable) 0.219 0.060 −0.008 −0.008 (0.413) (0.005) (0.008) (0.009) Hours main effect 0.047 0.033 (0.007) (0.010) Notes This Table presents the continuous effect of hours of instruction when it is interacted with various school characteristics (means of hours characteristics are shown in column 1). The estimates presented in columns 2 and 3 are based on regressions when each characteristic enters the regression separately. In columns 4 and 5, all characteristics are jointly included. Regressions include hours of instruction, interaction between hours and the school characteristic, subject dummies, subject dummies interacted with school characteristics, and pupil fixed effects. The dependent variable is standardised test scores. The scores are standardised using a mean of 500 and a standard deviation of 100. The sample includes 22 OECD developed countries that are listed in the notes of Table 3. Open in new tab Table 9 Estimated Effects of School Characteristics Interacted with Instructional Hours, OECD Countries . . Separate specification . Joint specification . Index . Index’s mean . Hours main effect . Hours interacted with index . Hours interacted with index . Hours interacted with index . . (1) . (2) . (3) . (4) . (5) . Achievement data are posted publicly (e.g. in the media). (binary variable) 0.335 0.050 0.027 0.020 0.025 (0.472) (0.004) (0.008) (0.009) (0.009) Achievement data are used in evaluation of the principal’s performance (binary variable) 0.216 0.052 0.021 0.022 0.023 (0.411) (0.004) (0.009) (0.011) (0.011) Achievement data are used in evaluation of teachers’ performance (binary variable) 0.294 0.055 0.003 −0.012 −0.009 (0.456) (0.005) (0.008) (0.010) (0.010) Quality of educational resources: index, (range −3.45 to 2.1) 0.150 0.058 0.001 0.004 0.004 (0.989) (0.004) (0.004) (0.004) (0.004) School responsibility for resource allocation: Index, (range −1.1 to 2.0) −0.058 0.059 0.012 0.008 0.009 (0.946) (0.004) (0.004) (0.004) (0.004) School responsibility for curriculum and assessment: index (range −1.4 to 1.3) 0.052 0.058 −0.002 −0.005 −0.006 (0.964) (0.004) (0.004) (0.004) (0.004) School governing board influences staffing (binary variable) 0.363 0.050 0.026 0.012 (0.481) (0.005) (0.008) (0.009) School governing board influences budget (binary variable) 0.706 0.038 0.030 0.018 (0.455) (0.007) (0.008) (0.009) School governing board influences instructional content (binary variable) 0.162 0.060 −0.006 −0.002 (0.368) (0.004) (0.010) (0.011) School governing board influences assessment (binary variable) 0.219 0.060 −0.008 −0.008 (0.413) (0.005) (0.008) (0.009) Hours main effect 0.047 0.033 (0.007) (0.010) . . Separate specification . Joint specification . Index . Index’s mean . Hours main effect . Hours interacted with index . Hours interacted with index . Hours interacted with index . . (1) . (2) . (3) . (4) . (5) . Achievement data are posted publicly (e.g. in the media). (binary variable) 0.335 0.050 0.027 0.020 0.025 (0.472) (0.004) (0.008) (0.009) (0.009) Achievement data are used in evaluation of the principal’s performance (binary variable) 0.216 0.052 0.021 0.022 0.023 (0.411) (0.004) (0.009) (0.011) (0.011) Achievement data are used in evaluation of teachers’ performance (binary variable) 0.294 0.055 0.003 −0.012 −0.009 (0.456) (0.005) (0.008) (0.010) (0.010) Quality of educational resources: index, (range −3.45 to 2.1) 0.150 0.058 0.001 0.004 0.004 (0.989) (0.004) (0.004) (0.004) (0.004) School responsibility for resource allocation: Index, (range −1.1 to 2.0) −0.058 0.059 0.012 0.008 0.009 (0.946) (0.004) (0.004) (0.004) (0.004) School responsibility for curriculum and assessment: index (range −1.4 to 1.3) 0.052 0.058 −0.002 −0.005 −0.006 (0.964) (0.004) (0.004) (0.004) (0.004) School governing board influences staffing (binary variable) 0.363 0.050 0.026 0.012 (0.481) (0.005) (0.008) (0.009) School governing board influences budget (binary variable) 0.706 0.038 0.030 0.018 (0.455) (0.007) (0.008) (0.009) School governing board influences instructional content (binary variable) 0.162 0.060 −0.006 −0.002 (0.368) (0.004) (0.010) (0.011) School governing board influences assessment (binary variable) 0.219 0.060 −0.008 −0.008 (0.413) (0.005) (0.008) (0.009) Hours main effect 0.047 0.033 (0.007) (0.010) Notes This Table presents the continuous effect of hours of instruction when it is interacted with various school characteristics (means of hours characteristics are shown in column 1). The estimates presented in columns 2 and 3 are based on regressions when each characteristic enters the regression separately. In columns 4 and 5, all characteristics are jointly included. Regressions include hours of instruction, interaction between hours and the school characteristic, subject dummies, subject dummies interacted with school characteristics, and pupil fixed effects. The dependent variable is standardised test scores. The scores are standardised using a mean of 500 and a standard deviation of 100. The sample includes 22 OECD developed countries that are listed in the notes of Table 3. Open in new tab In columns 2 and 3 of Table 9, I present the estimates of the main effect of instructional hours and the estimates of the interaction of instructional hours and each of the school‐level indices. It should be noted that because these indices are the same in each school for all subjects, their main effect cannot be included as covariates in a regression that includes a school fixed effect. However, the interactions of these indices with instructional time can be included in the within‐pupil regression of achievement. Note that while the pupil fixed effect absorbs the school fixed effect it also controls for any school‐level factor that is correlated with or determines these indices. In other words, even if the distribution of these indices across schools is not random, the school fixed effect will control for such heterogeneity. Therefore, the identifying assumption for the effect of the interaction between the indices and the hours of instruction is that the heterogeneity in these indices across schools is not subject specific. In other words, the interaction of hours of instruction with, for example, accountability, can be interpreted as causal only if it is picking up observed and unobserved variation of a school characteristics that do not vary by subject. I include the interactions one at a time, so each pair of estimates comes from a different regression. The estimated main effect of instruction hours is always positive and significant and it does not vary much across the different regressions and from the estimate presented in Table 3. Several of the estimated effects for the interaction terms are significantly different from zero. For example, the effects of publishing achievement data and school responsibly for budget allocation are positive and significant. Furthermore, these results remain significantly different from zero and their point estimate does not change much when all the interactions simultaneously in the regression. These results, shown in column 4 of Table 9, suggest the multi‐collinearity among the various indices does not prevent the estimation of the unique effect of each index. Overall, the results suggest that the productivity of instructional time is higher in schools that implement school accountability measures and in schools that have a degree of independence in allocating their resources. The index of quality of educational resources has a positive coefficient but it is not precisely measured. In contrast, school flexibility in determining its curriculum and pupils’ assessment measures do not have a significant effect on the productivity of instruction hours. Note that this index has no significant effect even when regressed as the sole interaction with hours of instruction. However, I should emphasise that the main effect on pupils’ achievement of school pedagogical autonomy may still be positive even though it does not vary with hours of instruction across the three subjects measured in PISA. The main effect of instructional time in the regression when all indices are included simultaneously is 0.047. In schools that post the achievements of their students publicly, this estimate is 6.64, more than 40% higher. A similar large effect is evident in schools that evaluate school principals according to their students’ performance though no such effect is evident in schools that similarly evaluate their teachers. However, the 2006 PISA questionnaire data do not provide enough details to allow an understanding of how exactly such evaluations are done and whether they are used to reward school staff or affect their wages. As a result, we should be cautious in interpreting these results. Another interesting feature of the school structure in PISA 2006 is governance, in particular the role of the school governing board. Four questions assess the role of the governing board in influencing staffing, the budget and instructional content and assessment. Adding to the regression interactions terms between these four indicators and instructional hours did not change the point estimates of the already included interaction terms. Furthermore, the pattern of the estimates of these new interaction terms is interesting since the results are consistent with the evidence of the other interaction terms. First, the results indicate that having a board that influences staffing and the budget leads to a higher productivity of instructional time. Second, having a board that influences instructional content and assessment has no measurable effect on the productivity of instruction in school. This evidence (presented in column 5 of Table 9) strengthens the overall findings that school autonomy in budgetary issues is conducive to enhancing pupils’ learning and achievement. At the same time, there is no evidence that school pedagogic autonomy will lead to higher productivity. 4. Conclusions In this article, I measure the effects of instructional time on students’ academic achievement empirically. The evidence from a sample of 15‐year‐old students from over 50 countries consistently shows that additional instructional time has a positive and significant effect on test scores. The OLS results are highly biased upward but the within‐student estimates are very similar across groups of developed and middle‐income countries. Overall, the effects of instructional time are relatively large relative to other school‐level interventions for which there is reliable evidence. However, I should note that the identification strategy based on within‐pupil variation has some limitations which may qualify the strength of the causal statements that one can make relative to evidence from randomised experiments or quasi‐experimental settings such as a regression discontinuity model. From a policy perspective, any evaluation of the merits of adding instructional time should take into account its cost relative to other potentially beneficial inputs or interventions. Policy makers would be advised to consider that adding instructional time in a given subject may be associated with beneficial spillover effects by leading to more demanding and advanced coursework. For example, if high school students from a different country or school spend twice as much class time on mathematics than students from a different country or school, they are much more likely to cover algebra rather than just geometry. Such an increase in the level of challenge in coursework may have increased performance in PISA along with the effect realised solely through more time devoted to subjects. The PISA data do now allow me to disentangle these two channels of effect of change in instruction time.15 Also, our results also show that the estimated effect of additional instructional time is strikingly lower for the sample of developing countries and the gains in developing countries were only half the size of those in developed countries. The results are all the more worrying since the developing countries included in the PISA sample (such as Chile, Argentina and Thailand) are much more developed than the ‘typical’ developing country. Possible explanations for the low productivity of instruction time in the PISA developing countries sample can be drawn from the findings reported in the previous section as school accountability measures, large degree of schools’ independence in allocating resources and in hiring/firing teachers and strong influence of school governing boards are much less prevalent among schools from these countries in comparison to the PISA developed countries sample. Given the recent evidence from India, Kenya and other very poor developing countries about the high rate of absenteeism of teachers, we can expect that the productivity of instructional time in the poorest developing counties in Africa and in South East Asia is even lower than in our PISA sample. The significant association between instructional time productivity and the structure and working environments of educational systems in OECD countries points towards a path for improvements in all nations. For developing countries in particular, one avenue for enhanced educational and economic progress clearly lies in closing this gap in productivity of instructional time. Appendix A: Additional Tables Table A1 Average Hours of Instructional Time and PISA Scores, for OECD Countries . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of Students . 1 Australia AUS 3.5 2.8 3.5 9.8 516.2 523.0 508.3 515.8 14,170 2 Austria AUT 2.8 2.2 2.4 7.4 509.3 513.8 494.0 505.7 4,927 3 Belgium BEL 3.2 2.3 3.1 8.6 526.9 516.2 506.9 516.6 8,857 4 Canada CAN 3.9 3.5 3.9 11.3 517.4 522.5 512.4 517.5 22,646 5 Switzerland CHE 3.5 2.0 3.4 8.9 527.8 507.6 496.2 510.5 12,192 6 Germany DEU 3.4 2.7 3.2 9.3 503.7 516.0 496.2 505.3 4,891 7 Denmark DNK 3.9 2.8 4.8 11.5 512.4 495.1 494.1 500.5 4,532 8 Spain ESP 3.1 2.8 3.2 9.1 501.4 504.4 479.7 495.2 19,604 9 Finland FIN 3.0 2.7 2.7 8.4 549.9 563.7 547.2 553.6 4,714 10 France FRA 3.4 2.5 3.6 9.5 497.0 496.1 488.6 493.9 4,716 11 UK GBR 3.4 3.7 3.4 10.5 497.5 514.3 496.0 502.6 13,152 12 Greece GRC 3.0 2.8 2.8 8.6 461.9 476.8 462.1 466.9 4,873 13 Ireland IRL 3.2 2.2 3.1 8.5 502.2 509.4 518.8 510.1 4,585 14 Iceland ISL 4.2 2.6 4.0 10.7 505.2 490.8 484.3 493.4 3,789 15 Italy ITA 3.2 2.5 3.9 9.6 473.8 487.2 477.4 479.4 21,773 16 Japan JPN 3.7 2.3 3.3 9.4 525.8 534.1 500.1 520.0 5,952 17 Luxembourg LUX 3.4 2.1 3.1 8.5 490.5 487.0 480.5 486.0 4,567 18 Netherlands NLD 2.5 2.0 2.5 7.1 537.2 530.4 513.8 527.1 4,871 19 Norway NOR 2.9 2.3 3.1 8.4 489.9 486.4 484.5 486.9 4,692 20 New Zealand NZL 3.9 3.6 3.9 11.4 523.0 532.3 523.3 526.2 4,823 21 Portugal PRT 3.2 2.9 2.8 8.9 470.2 478.7 476.6 475.2 5,109 22 Sweden SWE 2.6 2.4 2.7 7.7 503.3 504.3 508.5 505.4 4,443 Average 3.3 2.6 3.3 9.2 506.5 508.6 497.7 504.3 8358.1 SD 0.4 0.5 0.6 1.3 21.5 21.1 19.0 19.6 6089.3 Total 183,878 . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of Students . 1 Australia AUS 3.5 2.8 3.5 9.8 516.2 523.0 508.3 515.8 14,170 2 Austria AUT 2.8 2.2 2.4 7.4 509.3 513.8 494.0 505.7 4,927 3 Belgium BEL 3.2 2.3 3.1 8.6 526.9 516.2 506.9 516.6 8,857 4 Canada CAN 3.9 3.5 3.9 11.3 517.4 522.5 512.4 517.5 22,646 5 Switzerland CHE 3.5 2.0 3.4 8.9 527.8 507.6 496.2 510.5 12,192 6 Germany DEU 3.4 2.7 3.2 9.3 503.7 516.0 496.2 505.3 4,891 7 Denmark DNK 3.9 2.8 4.8 11.5 512.4 495.1 494.1 500.5 4,532 8 Spain ESP 3.1 2.8 3.2 9.1 501.4 504.4 479.7 495.2 19,604 9 Finland FIN 3.0 2.7 2.7 8.4 549.9 563.7 547.2 553.6 4,714 10 France FRA 3.4 2.5 3.6 9.5 497.0 496.1 488.6 493.9 4,716 11 UK GBR 3.4 3.7 3.4 10.5 497.5 514.3 496.0 502.6 13,152 12 Greece GRC 3.0 2.8 2.8 8.6 461.9 476.8 462.1 466.9 4,873 13 Ireland IRL 3.2 2.2 3.1 8.5 502.2 509.4 518.8 510.1 4,585 14 Iceland ISL 4.2 2.6 4.0 10.7 505.2 490.8 484.3 493.4 3,789 15 Italy ITA 3.2 2.5 3.9 9.6 473.8 487.2 477.4 479.4 21,773 16 Japan JPN 3.7 2.3 3.3 9.4 525.8 534.1 500.1 520.0 5,952 17 Luxembourg LUX 3.4 2.1 3.1 8.5 490.5 487.0 480.5 486.0 4,567 18 Netherlands NLD 2.5 2.0 2.5 7.1 537.2 530.4 513.8 527.1 4,871 19 Norway NOR 2.9 2.3 3.1 8.4 489.9 486.4 484.5 486.9 4,692 20 New Zealand NZL 3.9 3.6 3.9 11.4 523.0 532.3 523.3 526.2 4,823 21 Portugal PRT 3.2 2.9 2.8 8.9 470.2 478.7 476.6 475.2 5,109 22 Sweden SWE 2.6 2.4 2.7 7.7 503.3 504.3 508.5 505.4 4,443 Average 3.3 2.6 3.3 9.2 506.5 508.6 497.7 504.3 8358.1 SD 0.4 0.5 0.6 1.3 21.5 21.1 19.0 19.6 6089.3 Total 183,878 Notes The Table shows, for each OECD country, average hours of instruction per week, for Mathematics, Science and Reading, and the total for all three subjects. Average Scores are also shown for these categories. Open in new tab Table A1 Average Hours of Instructional Time and PISA Scores, for OECD Countries . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of Students . 1 Australia AUS 3.5 2.8 3.5 9.8 516.2 523.0 508.3 515.8 14,170 2 Austria AUT 2.8 2.2 2.4 7.4 509.3 513.8 494.0 505.7 4,927 3 Belgium BEL 3.2 2.3 3.1 8.6 526.9 516.2 506.9 516.6 8,857 4 Canada CAN 3.9 3.5 3.9 11.3 517.4 522.5 512.4 517.5 22,646 5 Switzerland CHE 3.5 2.0 3.4 8.9 527.8 507.6 496.2 510.5 12,192 6 Germany DEU 3.4 2.7 3.2 9.3 503.7 516.0 496.2 505.3 4,891 7 Denmark DNK 3.9 2.8 4.8 11.5 512.4 495.1 494.1 500.5 4,532 8 Spain ESP 3.1 2.8 3.2 9.1 501.4 504.4 479.7 495.2 19,604 9 Finland FIN 3.0 2.7 2.7 8.4 549.9 563.7 547.2 553.6 4,714 10 France FRA 3.4 2.5 3.6 9.5 497.0 496.1 488.6 493.9 4,716 11 UK GBR 3.4 3.7 3.4 10.5 497.5 514.3 496.0 502.6 13,152 12 Greece GRC 3.0 2.8 2.8 8.6 461.9 476.8 462.1 466.9 4,873 13 Ireland IRL 3.2 2.2 3.1 8.5 502.2 509.4 518.8 510.1 4,585 14 Iceland ISL 4.2 2.6 4.0 10.7 505.2 490.8 484.3 493.4 3,789 15 Italy ITA 3.2 2.5 3.9 9.6 473.8 487.2 477.4 479.4 21,773 16 Japan JPN 3.7 2.3 3.3 9.4 525.8 534.1 500.1 520.0 5,952 17 Luxembourg LUX 3.4 2.1 3.1 8.5 490.5 487.0 480.5 486.0 4,567 18 Netherlands NLD 2.5 2.0 2.5 7.1 537.2 530.4 513.8 527.1 4,871 19 Norway NOR 2.9 2.3 3.1 8.4 489.9 486.4 484.5 486.9 4,692 20 New Zealand NZL 3.9 3.6 3.9 11.4 523.0 532.3 523.3 526.2 4,823 21 Portugal PRT 3.2 2.9 2.8 8.9 470.2 478.7 476.6 475.2 5,109 22 Sweden SWE 2.6 2.4 2.7 7.7 503.3 504.3 508.5 505.4 4,443 Average 3.3 2.6 3.3 9.2 506.5 508.6 497.7 504.3 8358.1 SD 0.4 0.5 0.6 1.3 21.5 21.1 19.0 19.6 6089.3 Total 183,878 . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of Students . 1 Australia AUS 3.5 2.8 3.5 9.8 516.2 523.0 508.3 515.8 14,170 2 Austria AUT 2.8 2.2 2.4 7.4 509.3 513.8 494.0 505.7 4,927 3 Belgium BEL 3.2 2.3 3.1 8.6 526.9 516.2 506.9 516.6 8,857 4 Canada CAN 3.9 3.5 3.9 11.3 517.4 522.5 512.4 517.5 22,646 5 Switzerland CHE 3.5 2.0 3.4 8.9 527.8 507.6 496.2 510.5 12,192 6 Germany DEU 3.4 2.7 3.2 9.3 503.7 516.0 496.2 505.3 4,891 7 Denmark DNK 3.9 2.8 4.8 11.5 512.4 495.1 494.1 500.5 4,532 8 Spain ESP 3.1 2.8 3.2 9.1 501.4 504.4 479.7 495.2 19,604 9 Finland FIN 3.0 2.7 2.7 8.4 549.9 563.7 547.2 553.6 4,714 10 France FRA 3.4 2.5 3.6 9.5 497.0 496.1 488.6 493.9 4,716 11 UK GBR 3.4 3.7 3.4 10.5 497.5 514.3 496.0 502.6 13,152 12 Greece GRC 3.0 2.8 2.8 8.6 461.9 476.8 462.1 466.9 4,873 13 Ireland IRL 3.2 2.2 3.1 8.5 502.2 509.4 518.8 510.1 4,585 14 Iceland ISL 4.2 2.6 4.0 10.7 505.2 490.8 484.3 493.4 3,789 15 Italy ITA 3.2 2.5 3.9 9.6 473.8 487.2 477.4 479.4 21,773 16 Japan JPN 3.7 2.3 3.3 9.4 525.8 534.1 500.1 520.0 5,952 17 Luxembourg LUX 3.4 2.1 3.1 8.5 490.5 487.0 480.5 486.0 4,567 18 Netherlands NLD 2.5 2.0 2.5 7.1 537.2 530.4 513.8 527.1 4,871 19 Norway NOR 2.9 2.3 3.1 8.4 489.9 486.4 484.5 486.9 4,692 20 New Zealand NZL 3.9 3.6 3.9 11.4 523.0 532.3 523.3 526.2 4,823 21 Portugal PRT 3.2 2.9 2.8 8.9 470.2 478.7 476.6 475.2 5,109 22 Sweden SWE 2.6 2.4 2.7 7.7 503.3 504.3 508.5 505.4 4,443 Average 3.3 2.6 3.3 9.2 506.5 508.6 497.7 504.3 8358.1 SD 0.4 0.5 0.6 1.3 21.5 21.1 19.0 19.6 6089.3 Total 183,878 Notes The Table shows, for each OECD country, average hours of instruction per week, for Mathematics, Science and Reading, and the total for all three subjects. Average Scores are also shown for these categories. Open in new tab Table A2 Average Hours of Instructional Time and PISA Scores, for Eastern European Countries . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Bulgaria BGR 2.6 2.3 2.6 7.5 417.2 439.4 407.2 421.3 4,498 2 Czech Republic CZE 3.5 3.0 3.2 9.7 536.0 537.7 510.0 527.9 5,932 3 Estonia EST 3.7 2.9 3.1 9.7 517.2 534.5 502.9 518.2 4,865 4 Croatia HRV 2.7 1.8 2.9 7.3 467.3 493.3 477.1 479.2 5,213 5 Hungary HUN 2.9 2.2 2.8 7.9 496.7 508.9 488.4 498.0 4,490 6 Lithuania LTU 3.1 2.4 3.2 8.7 485.3 486.5 468.7 480.1 4,744 7 Latvia LVA 3.9 2.5 3.2 9.7 491.1 493.7 484.6 489.8 4,719 8 Montenegro MNE 2.7 2.5 2.6 7.8 395.2 408.8 387.8 397.3 4,455 9 Poland POL 3.9 2.4 4.1 10.4 500.3 503.0 512.7 505.3 5,547 10 Romania ROU 2.5 1.9 2.8 7.3 415.0 416.3 392.0 407.7 5,118 11 Russian Federation RUS 3.2 3.3 1.8 8.3 478.6 481.4 442.3 467.4 5,799 12 Serbia SRB 2.8 2.5 2.8 8.1 436.1 436.8 403.0 425.3 4,798 13 Slovak Republic SVK 2.9 2.2 2.7 7.8 494.7 491.1 470.2 485.3 4,731 14 Slovenia SVN 2.8 2.2 2.7 7.7 482.3 494.3 468.9 481.8 6,595 Average 3.1 2.4 2.9 8.4 472.4 480.4 458.3 470.3 5107.4 SD 0.5 0.4 0.5 1.0 41.3 40.2 44.0 41.3 640.5 Total 71,504 . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Bulgaria BGR 2.6 2.3 2.6 7.5 417.2 439.4 407.2 421.3 4,498 2 Czech Republic CZE 3.5 3.0 3.2 9.7 536.0 537.7 510.0 527.9 5,932 3 Estonia EST 3.7 2.9 3.1 9.7 517.2 534.5 502.9 518.2 4,865 4 Croatia HRV 2.7 1.8 2.9 7.3 467.3 493.3 477.1 479.2 5,213 5 Hungary HUN 2.9 2.2 2.8 7.9 496.7 508.9 488.4 498.0 4,490 6 Lithuania LTU 3.1 2.4 3.2 8.7 485.3 486.5 468.7 480.1 4,744 7 Latvia LVA 3.9 2.5 3.2 9.7 491.1 493.7 484.6 489.8 4,719 8 Montenegro MNE 2.7 2.5 2.6 7.8 395.2 408.8 387.8 397.3 4,455 9 Poland POL 3.9 2.4 4.1 10.4 500.3 503.0 512.7 505.3 5,547 10 Romania ROU 2.5 1.9 2.8 7.3 415.0 416.3 392.0 407.7 5,118 11 Russian Federation RUS 3.2 3.3 1.8 8.3 478.6 481.4 442.3 467.4 5,799 12 Serbia SRB 2.8 2.5 2.8 8.1 436.1 436.8 403.0 425.3 4,798 13 Slovak Republic SVK 2.9 2.2 2.7 7.8 494.7 491.1 470.2 485.3 4,731 14 Slovenia SVN 2.8 2.2 2.7 7.7 482.3 494.3 468.9 481.8 6,595 Average 3.1 2.4 2.9 8.4 472.4 480.4 458.3 470.3 5107.4 SD 0.5 0.4 0.5 1.0 41.3 40.2 44.0 41.3 640.5 Total 71,504 Notes The Table shows, for 14 Eastern European countries, average hours of instruction per week, for Mathematics, Science and Reading, and the total for all three subjects. Average Scores are also shown for these categories. The sample includes 14 countries of Eastern Europe: Bulgaria, Croatia, Czech Republic, Estonia, Hungary, Latvia, Lithuania, Montenegro, Poland, Romania, Russian Federation, Serbia, Slovak Republic, Slovenia. Open in new tab Table A2 Average Hours of Instructional Time and PISA Scores, for Eastern European Countries . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Bulgaria BGR 2.6 2.3 2.6 7.5 417.2 439.4 407.2 421.3 4,498 2 Czech Republic CZE 3.5 3.0 3.2 9.7 536.0 537.7 510.0 527.9 5,932 3 Estonia EST 3.7 2.9 3.1 9.7 517.2 534.5 502.9 518.2 4,865 4 Croatia HRV 2.7 1.8 2.9 7.3 467.3 493.3 477.1 479.2 5,213 5 Hungary HUN 2.9 2.2 2.8 7.9 496.7 508.9 488.4 498.0 4,490 6 Lithuania LTU 3.1 2.4 3.2 8.7 485.3 486.5 468.7 480.1 4,744 7 Latvia LVA 3.9 2.5 3.2 9.7 491.1 493.7 484.6 489.8 4,719 8 Montenegro MNE 2.7 2.5 2.6 7.8 395.2 408.8 387.8 397.3 4,455 9 Poland POL 3.9 2.4 4.1 10.4 500.3 503.0 512.7 505.3 5,547 10 Romania ROU 2.5 1.9 2.8 7.3 415.0 416.3 392.0 407.7 5,118 11 Russian Federation RUS 3.2 3.3 1.8 8.3 478.6 481.4 442.3 467.4 5,799 12 Serbia SRB 2.8 2.5 2.8 8.1 436.1 436.8 403.0 425.3 4,798 13 Slovak Republic SVK 2.9 2.2 2.7 7.8 494.7 491.1 470.2 485.3 4,731 14 Slovenia SVN 2.8 2.2 2.7 7.7 482.3 494.3 468.9 481.8 6,595 Average 3.1 2.4 2.9 8.4 472.4 480.4 458.3 470.3 5107.4 SD 0.5 0.4 0.5 1.0 41.3 40.2 44.0 41.3 640.5 Total 71,504 . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Bulgaria BGR 2.6 2.3 2.6 7.5 417.2 439.4 407.2 421.3 4,498 2 Czech Republic CZE 3.5 3.0 3.2 9.7 536.0 537.7 510.0 527.9 5,932 3 Estonia EST 3.7 2.9 3.1 9.7 517.2 534.5 502.9 518.2 4,865 4 Croatia HRV 2.7 1.8 2.9 7.3 467.3 493.3 477.1 479.2 5,213 5 Hungary HUN 2.9 2.2 2.8 7.9 496.7 508.9 488.4 498.0 4,490 6 Lithuania LTU 3.1 2.4 3.2 8.7 485.3 486.5 468.7 480.1 4,744 7 Latvia LVA 3.9 2.5 3.2 9.7 491.1 493.7 484.6 489.8 4,719 8 Montenegro MNE 2.7 2.5 2.6 7.8 395.2 408.8 387.8 397.3 4,455 9 Poland POL 3.9 2.4 4.1 10.4 500.3 503.0 512.7 505.3 5,547 10 Romania ROU 2.5 1.9 2.8 7.3 415.0 416.3 392.0 407.7 5,118 11 Russian Federation RUS 3.2 3.3 1.8 8.3 478.6 481.4 442.3 467.4 5,799 12 Serbia SRB 2.8 2.5 2.8 8.1 436.1 436.8 403.0 425.3 4,798 13 Slovak Republic SVK 2.9 2.2 2.7 7.8 494.7 491.1 470.2 485.3 4,731 14 Slovenia SVN 2.8 2.2 2.7 7.7 482.3 494.3 468.9 481.8 6,595 Average 3.1 2.4 2.9 8.4 472.4 480.4 458.3 470.3 5107.4 SD 0.5 0.4 0.5 1.0 41.3 40.2 44.0 41.3 640.5 Total 71,504 Notes The Table shows, for 14 Eastern European countries, average hours of instruction per week, for Mathematics, Science and Reading, and the total for all three subjects. Average Scores are also shown for these categories. The sample includes 14 countries of Eastern Europe: Bulgaria, Croatia, Czech Republic, Estonia, Hungary, Latvia, Lithuania, Montenegro, Poland, Romania, Russian Federation, Serbia, Slovak Republic, Slovenia. Open in new tab Table A3 Average Hours of Instructional Time and PISA Scores, for Developing Countries . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Argentina ARG 2.6 2.0 2.1 6.8 388.3 398.9 384.4 390.5 4,339 2 Azerbaijan AZE 3.3 2.5 3.2 9.0 476.6 385.3 355.2 405.7 5,184 3 Brazil BRA 2.7 2.0 2.6 7.3 365.8 385.5 389.9 380.4 9,295 4 Chile CHL 3.1 2.1 3.1 8.3 417.5 442.6 447.8 435.9 5,233 5 Columbia COL 3.7 3.0 3.4 10.2 373.5 391.5 390.9 385.3 4,478 6 Indonesia IDN 3.5 2.7 3.2 9.5 380.7 384.8 383.6 383.0 10,647 7 Jordan JOR 3.1 2.9 3.2 9.2 388.9 427.0 409.4 408.4 6,509 8 Kyrgyzstan KGZ 2.6 1.9 2.5 7.0 316.0 326.4 290.9 311.1 5,904 9 Mexico MEX 3.5 2.7 3.3 9.5 420.8 422.5 427.6 423.6 30,971 10 Thailand THA 3.4 3.4 2.7 9.5 425.2 430.0 425.3 426.8 6,192 11 Tunisia TUN 3.0 2.3 2.8 8.0 363.5 384.3 378.5 375.4 4,640 12 Turkey TUR 3.4 2.6 3.5 9.5 428.0 427.9 453.4 436.5 4,942 13 Uruguay URY 3.0 2.2 2.4 7.6 435.2 438.1 425.0 432.8 4,839 Average 3.1 2.5 2.9 8.6 398.5 403.4 397.1 399.7 7936.4 SD 0.4 0.5 0.4 1.1 41.0 32.2 43.0 34.8 7177.6 Total 103,173 . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Argentina ARG 2.6 2.0 2.1 6.8 388.3 398.9 384.4 390.5 4,339 2 Azerbaijan AZE 3.3 2.5 3.2 9.0 476.6 385.3 355.2 405.7 5,184 3 Brazil BRA 2.7 2.0 2.6 7.3 365.8 385.5 389.9 380.4 9,295 4 Chile CHL 3.1 2.1 3.1 8.3 417.5 442.6 447.8 435.9 5,233 5 Columbia COL 3.7 3.0 3.4 10.2 373.5 391.5 390.9 385.3 4,478 6 Indonesia IDN 3.5 2.7 3.2 9.5 380.7 384.8 383.6 383.0 10,647 7 Jordan JOR 3.1 2.9 3.2 9.2 388.9 427.0 409.4 408.4 6,509 8 Kyrgyzstan KGZ 2.6 1.9 2.5 7.0 316.0 326.4 290.9 311.1 5,904 9 Mexico MEX 3.5 2.7 3.3 9.5 420.8 422.5 427.6 423.6 30,971 10 Thailand THA 3.4 3.4 2.7 9.5 425.2 430.0 425.3 426.8 6,192 11 Tunisia TUN 3.0 2.3 2.8 8.0 363.5 384.3 378.5 375.4 4,640 12 Turkey TUR 3.4 2.6 3.5 9.5 428.0 427.9 453.4 436.5 4,942 13 Uruguay URY 3.0 2.2 2.4 7.6 435.2 438.1 425.0 432.8 4,839 Average 3.1 2.5 2.9 8.6 398.5 403.4 397.1 399.7 7936.4 SD 0.4 0.5 0.4 1.1 41.0 32.2 43.0 34.8 7177.6 Total 103,173 Notes The Table shows, for 13 Developing Countries, average hours of instruction per week, for Mathematics, Science and Reading, and the total for all three subjects. Average Scores are also shown for these categories. The sample includes 13 developing countries: Argentina, Azerbaijan, Brazil, Chile, Colombia, Indonesia, Jordan, Kyrgyzstan, Mexico, Thailand, Tunisia, Turkey, Uruguay. Open in new tab Table A3 Average Hours of Instructional Time and PISA Scores, for Developing Countries . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Argentina ARG 2.6 2.0 2.1 6.8 388.3 398.9 384.4 390.5 4,339 2 Azerbaijan AZE 3.3 2.5 3.2 9.0 476.6 385.3 355.2 405.7 5,184 3 Brazil BRA 2.7 2.0 2.6 7.3 365.8 385.5 389.9 380.4 9,295 4 Chile CHL 3.1 2.1 3.1 8.3 417.5 442.6 447.8 435.9 5,233 5 Columbia COL 3.7 3.0 3.4 10.2 373.5 391.5 390.9 385.3 4,478 6 Indonesia IDN 3.5 2.7 3.2 9.5 380.7 384.8 383.6 383.0 10,647 7 Jordan JOR 3.1 2.9 3.2 9.2 388.9 427.0 409.4 408.4 6,509 8 Kyrgyzstan KGZ 2.6 1.9 2.5 7.0 316.0 326.4 290.9 311.1 5,904 9 Mexico MEX 3.5 2.7 3.3 9.5 420.8 422.5 427.6 423.6 30,971 10 Thailand THA 3.4 3.4 2.7 9.5 425.2 430.0 425.3 426.8 6,192 11 Tunisia TUN 3.0 2.3 2.8 8.0 363.5 384.3 378.5 375.4 4,640 12 Turkey TUR 3.4 2.6 3.5 9.5 428.0 427.9 453.4 436.5 4,942 13 Uruguay URY 3.0 2.2 2.4 7.6 435.2 438.1 425.0 432.8 4,839 Average 3.1 2.5 2.9 8.6 398.5 403.4 397.1 399.7 7936.4 SD 0.4 0.5 0.4 1.1 41.0 32.2 43.0 34.8 7177.6 Total 103,173 . . . Hours of instruction per week . Pisa score . . No. . Country . Code . Mathematics . Science . Reading . All (sum) . Mathematics . Science . Reading . All (average) . Number of students . 1 Argentina ARG 2.6 2.0 2.1 6.8 388.3 398.9 384.4 390.5 4,339 2 Azerbaijan AZE 3.3 2.5 3.2 9.0 476.6 385.3 355.2 405.7 5,184 3 Brazil BRA 2.7 2.0 2.6 7.3 365.8 385.5 389.9 380.4 9,295 4 Chile CHL 3.1 2.1 3.1 8.3 417.5 442.6 447.8 435.9 5,233 5 Columbia COL 3.7 3.0 3.4 10.2 373.5 391.5 390.9 385.3 4,478 6 Indonesia IDN 3.5 2.7 3.2 9.5 380.7 384.8 383.6 383.0 10,647 7 Jordan JOR 3.1 2.9 3.2 9.2 388.9 427.0 409.4 408.4 6,509 8 Kyrgyzstan KGZ 2.6 1.9 2.5 7.0 316.0 326.4 290.9 311.1 5,904 9 Mexico MEX 3.5 2.7 3.3 9.5 420.8 422.5 427.6 423.6 30,971 10 Thailand THA 3.4 3.4 2.7 9.5 425.2 430.0 425.3 426.8 6,192 11 Tunisia TUN 3.0 2.3 2.8 8.0 363.5 384.3 378.5 375.4 4,640 12 Turkey TUR 3.4 2.6 3.5 9.5 428.0 427.9 453.4 436.5 4,942 13 Uruguay URY 3.0 2.2 2.4 7.6 435.2 438.1 425.0 432.8 4,839 Average 3.1 2.5 2.9 8.6 398.5 403.4 397.1 399.7 7936.4 SD 0.4 0.5 0.4 1.1 41.0 32.2 43.0 34.8 7177.6 Total 103,173 Notes The Table shows, for 13 Developing Countries, average hours of instruction per week, for Mathematics, Science and Reading, and the total for all three subjects. Average Scores are also shown for these categories. The sample includes 13 developing countries: Argentina, Azerbaijan, Brazil, Chile, Colombia, Indonesia, Jordan, Kyrgyzstan, Mexico, Thailand, Tunisia, Turkey, Uruguay. Open in new tab Table A4 Descriptive Statistics – Test Score and Instructional Time . Test scores . Instructional time . . OECD developed . Eastern Europe . Developing countries . OECD developed . Eastern Europe . Developing countries . Mean 513.4 485.6 413.5 3.38 3.05 3.23 SD between pupils 84.4 86.9 75.1 1.02 0.88 1.22 SD within pupils 38.8 40.9 46.7 1.08 1.28 1.19 . Test scores . Instructional time . . OECD developed . Eastern Europe . Developing countries . OECD developed . Eastern Europe . Developing countries . Mean 513.4 485.6 413.5 3.38 3.05 3.23 SD between pupils 84.4 86.9 75.1 1.02 0.88 1.22 SD within pupils 38.8 40.9 46.7 1.08 1.28 1.19 Notes The Table contains means, and the standard deviation within and between pupils, for 3 different samples: OECD countries, Eastern Europe and Developing Countries. Open in new tab Table A4 Descriptive Statistics – Test Score and Instructional Time . Test scores . Instructional time . . OECD developed . Eastern Europe . Developing countries . OECD developed . Eastern Europe . Developing countries . Mean 513.4 485.6 413.5 3.38 3.05 3.23 SD between pupils 84.4 86.9 75.1 1.02 0.88 1.22 SD within pupils 38.8 40.9 46.7 1.08 1.28 1.19 . Test scores . Instructional time . . OECD developed . Eastern Europe . Developing countries . OECD developed . Eastern Europe . Developing countries . Mean 513.4 485.6 413.5 3.38 3.05 3.23 SD between pupils 84.4 86.9 75.1 1.02 0.88 1.22 SD within pupils 38.8 40.9 46.7 1.08 1.28 1.19 Notes The Table contains means, and the standard deviation within and between pupils, for 3 different samples: OECD countries, Eastern Europe and Developing Countries. Open in new tab Table A5 Regressions of Test Standardised Scores on Instructional Time using School‐Level Means . Whole sample . Boys . Girls . OLS . School FE . OLS . School FE . OLS . School FE . (1) . (2) . (3) . (4) . (5) . (6) . A. Mathematics + science + reading I. Continuous regression Hours 0.203 0.048 0.195 0.042 0.201 0.051 (0.008) (0.005) (0.009) (0.005) (0.008) (0.005) Number of observations 19,731 18,894 18,792 B. Mathematics + science I. Continuous regression Hours 0.259 0.065 0.254 0.062 0.261 0.071 (0.008) (0.006) (0.009) (0.007) (0.008) (0.006) Number of observations 13,154 12,596 12,528 . Whole sample . Boys . Girls . OLS . School FE . OLS . School FE . OLS . School FE . (1) . (2) . (3) . (4) . (5) . (6) . A. Mathematics + science + reading I. Continuous regression Hours 0.203 0.048 0.195 0.042 0.201 0.051 (0.008) (0.005) (0.009) (0.005) (0.008) (0.005) Number of observations 19,731 18,894 18,792 B. Mathematics + science I. Continuous regression Hours 0.259 0.065 0.254 0.062 0.261 0.071 (0.008) (0.006) (0.009) (0.007) (0.008) (0.006) Number of observations 13,154 12,596 12,528 Notes These regressions are run using collapsed school‐level data. For example, hours refers to the mean of continuous hours of learning, averaged to the school level. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Hours of learning is a continuous variable. The sample includes 22 OECD developed countries: Australia, Austria, Belgium, Canada, Germany, Denmark, Spain, Finland, France, Greece, Ireland, Iceland, Italy, Japan, Luxembourg, Netherlands, Norway, New Zealand, Portugal, Sweden, Switzerland, UK. Each regression includes subject dummies, and school fixed effects. Standard errors in parentheses are clustered at the school level. Open in new tab Table A5 Regressions of Test Standardised Scores on Instructional Time using School‐Level Means . Whole sample . Boys . Girls . OLS . School FE . OLS . School FE . OLS . School FE . (1) . (2) . (3) . (4) . (5) . (6) . A. Mathematics + science + reading I. Continuous regression Hours 0.203 0.048 0.195 0.042 0.201 0.051 (0.008) (0.005) (0.009) (0.005) (0.008) (0.005) Number of observations 19,731 18,894 18,792 B. Mathematics + science I. Continuous regression Hours 0.259 0.065 0.254 0.062 0.261 0.071 (0.008) (0.006) (0.009) (0.007) (0.008) (0.006) Number of observations 13,154 12,596 12,528 . Whole sample . Boys . Girls . OLS . School FE . OLS . School FE . OLS . School FE . (1) . (2) . (3) . (4) . (5) . (6) . A. Mathematics + science + reading I. Continuous regression Hours 0.203 0.048 0.195 0.042 0.201 0.051 (0.008) (0.005) (0.009) (0.005) (0.008) (0.005) Number of observations 19,731 18,894 18,792 B. Mathematics + science I. Continuous regression Hours 0.259 0.065 0.254 0.062 0.261 0.071 (0.008) (0.006) (0.009) (0.007) (0.008) (0.006) Number of observations 13,154 12,596 12,528 Notes These regressions are run using collapsed school‐level data. For example, hours refers to the mean of continuous hours of learning, averaged to the school level. Scores are standardised using a mean of 500 and a standard deviation of 100. Fixed effects are at the student level. Hours of learning is a continuous variable. The sample includes 22 OECD developed countries: Australia, Austria, Belgium, Canada, Germany, Denmark, Spain, Finland, France, Greece, Ireland, Iceland, Italy, Japan, Luxembourg, Netherlands, Norway, New Zealand, Portugal, Sweden, Switzerland, UK. Each regression includes subject dummies, and school fixed effects. Standard errors in parentheses are clustered at the school level. Open in new tab Footnotes 1 " Source: OECD Education at Glance, 2006: http://www.oecd.org/dataoecd/6/47/37344903.xls. 2 " For example, see studies on class size (Angrist and Lavy, 1999; Krueger, 1999), teachers’ training and certification (Angrist and Lavy, 2001; Kane et al., 2007), remedial education (Jacob and Lefgren, 2004; Lavy and Schlosser, 2005), teacher effect (Lavy, 2002, 2009; Rockoff, 2004; Rivkin et al., 2005) and computer‐aided instruction (Angrist and Lavy, 2002; Barrow et al., 2009). 3 " President Barack Obama said on 10 March 2009, at a speech to the US Hispanic Chamber of Commerce, that American children should go to school longer – either stay later in the day or into the summer – to have a chance to compete for jobs and pay cheques against foreign children. He urged administrators to ‘rethink the school day’ by adding more class time, and proposed longer class hours as part of a broader effort to improve US schools that he said are falling behind foreign competitors. Also, these ideas have been recently implemented as part of Mayor Rahm Emanuel’s longer school day initiative, as students in 40 schools across Chicago will have an extra 90 minutes of instruction every day. (See http://www.suntimes.com/news/education/7757540-418/chicago-public-schools-system-launches-longer-school-day-website.html.) 4 " Dee (2005) used also the cross subject variation within student in his work on teacher effects with the Tennessee STAR experiment. 5 " Countries that are interested in participating in PISA contact the OECD Secretariat. The PISA Governing Board then approves membership according to certain criteria. Participating countries must have the technical expertise necessary to administer an international assessment and must be able to meet the full costs of participation. To take part in a cycle of PISA, countries must also join two years before the survey takes place. 6 " For example, the PISA 2003 has a section on problem solving. 7 " See the online Appendix for the exact format of this question in the PISA 2006 student questionnaire. 8 " It is also important to emphasise that the natural experiment method that I used in the Israeli context allowed me to test some of the central assumptions I make while using the pupil fixed effect identification method. These tests support the assumption that the effect of additional hours of instruction on each of the subjects is very similar and that there are no cross‐subjects spillover effects. 9 " I also examined how sensitive the treatment estimates are by including interactions between the subject dummies and pupil characteristics. The estimates from this more flexible specification approach are very similar to those presented in Table 3, though overall they are about 10% lower (results are available from the author upon request). 10 " The exact wording is based on question 19 and is available in the online Appendix. 11 " I also estimated the effect of hours of instruction based on a sample of schools that do not use a student’s desire for a particular programme as a criterion for admission. This information is also based on the PISA school questionnaire, question 19. The results based on this sample are very similar those obtained from the full sample (results are available from the author upon request). 12 " I also estimate the potential effect of teachers in other ways, through various samples stratified by the extent of lack of qualified teachers. For example, I compared a sample of schools that reported a lack of qualified teachers in at least two subjects to a sample that included only schools without a lack of qualified teachers in any subject. The results obtained from these samples are practically identical (results are available from the author upon request). 13 " It should be noted that I do not include in this sample the newly industrialised countries of Korea, Honk Kong, Macau and Chinese Taipei since their per capita income is much higher than the developing countries. In addition, PISA does not classify these countries as developing countries. These countries are also among the best‐performing countries among all participants in PISA 2006 and their mean instructional time in all three subjects is also among the highest in the overall sample. 14 " The gap is even larger based on a comparison of the estimates derived from pooling only mathematics and science test scores. Also, the largest difference in terms of the non‐linear specification of instructional hours between the two groups of countries is in the effect of changing from less than two hours to 2–3 hours of instruction per week. These results are available from the author upon request. 15 " See Goodman (2009) for a discussion of the literature on the effects of coursework on achievement and earnings. References Allensworth , E. and Takako , N. ( 2009 ). ‘ Double‐dose algebra as an alternative strategy to remediation: effects on students’ academic outcomes ’, Journal of Research on Educational Effectiveness , vol. 2 ( 2 ), pp. 111 – 48 . Google Scholar Crossref Search ADS WorldCat Angrist , J. and Lavy , V. ( 1999 ). ‘ Using Maimonides’ rule to estimate the effect of class size on children’s academic achievement ’, Quarterly Journal of Economics , vol. 114 ( 2 ), pp. 533 – 575 . Google Scholar Crossref Search ADS WorldCat Angrist , J. and Lavy , V. 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( 1999 ). ‘ Experimental estimates of education production functions ’, Quarterly Journal of Economics , vol. 114 ( 2 ), pp. 497 – 532 . Google Scholar Crossref Search ADS WorldCat Lavy , V . ( 2002 ). ‘ Evaluating the effect of teachers’ group performance incentives on pupils’ achievements ’, Journal of Political Economy , vol. 110 ( 6 ), pp. 1286 – 317 . Google Scholar Crossref Search ADS WorldCat Lavy , V . ( 2009 ). ‘ Performance pay and teachers’ effort, productivity and grading ethics ’, American Economic Review , vol. 99 ( 5 ), pp. 1979 – 2011 . Google Scholar Crossref Search ADS WorldCat Lavy , V . ( 2012 ). ‘ Expanding school resources and increasing time on task: effects of a policy experiment in Israel on student academic achievement and Behavior ’, NBER Working Paper 18369. Lavy , V. and Schlosser , A. ( 2005 ). ‘ Targeted remedial education for under‐performing teenagers: costs and benefits ’, Journal of Labor Economics , vol. 23 ( 4 ), pp. 839 – 74 . Google Scholar Crossref Search ADS WorldCat Lee , J.W. and Barro , R. ( 2001 ). ‘ School quality in a cross‐section of countries ’, Economica , vol. 68 ( 3 ), pp. 465 – 88 . Google Scholar Crossref Search ADS WorldCat Marcotte , D.E. and Hemelt , S.. ( 2008 ). ‘ Unscheduled closings and student performance ’, Education Finance and Policy , vol. 3 ( 3 ), pp. 316 – 38 . Google Scholar Crossref Search ADS WorldCat Pischke , J.‐S. . ( 2007 ). ‘ The impact of length of the school year on student performance and earnings: evidence from the German short school years ’, Economic Journal , vol. 117 ( 4 ), pp. 1216 – 42 . Google Scholar Crossref Search ADS WorldCat Rivkin , S.G. and Schiman , J.C. ( 2013 ). ‘ Instruction time, classroom quality, and academic achievement ’, NBER Working Paper 19464. Rivkin , S.G. , Hanushek , E.A. and Kain , J.F. ( 2005 ). ‘ Teachers, schools, and academic achievement ’, Econometrica , vol. 73 ( 1 ), pp. 417 – 59 . Google Scholar Crossref Search ADS WorldCat Rockoff , J.E. ( 2004 ). ‘ The impact of individual teachers on student achievement: evidence from panel data ’, American Economic Review , vol. 94 ( 2 ), pp. 247 – 52 . Google Scholar Crossref Search ADS WorldCat Author notes " This article is a revised version of NBER Working Paper 16227 (July 2010). Special thanks go to Katherine Eyal, Michael Friedman, Amit Meir and Oren Epshtain for their outstanding research assistance. I benefited from comments at seminars at the LSE, Rome Tor Vergata, LACEA conference in Buenos Aires, Itau Bank conference in Rio, Hebrew University, Spain Ministry of Education, Paris School of Economics, Oxford University and comments of Economic Journal referees and editor. I thank the Israeli Science Foundation and the Falk Research Institute for research support. © 2015 Royal Economic Society

Smith, James, P.

doi: 10.1111/ecoj.12280pmid: N/A

This Feature focuses on contributions to a new emerging economic literature – early life health and economic shocks to children and parents. Or to put it more succinctly – labour economists discovered kids. The impacts of economic and health shocks tend to not only be larger when they take place during the childhood years, their impacts appear to be longer lasting and, perhaps, more malleable While there were initially limitations on the data available for this topic that constrained scientific advances by economists, that has changed a great deal as new data sets emerged and existing ones were tweaked to address the central questions. In contrast, the theoretical and statistical toolkits of economists offered immediate insights on how to address these questions that went beyond the existing literature and the scientific disciplines that provided most of the best early work. The three articles in the Feature illustrate another important theme of this literature – important early life effects on central economic outcomes are not limited by geographic boundaries. The articles here cover China, Germany and the US, countries that differ significantly in levels of economic development, human capital, health and culture. The economic shocks studied are themselves quite diverse – a health shock to one of a pair of twins in rural China, childhood exposure to a severe hunger episode associated with the Second World War in Germany and the initial short‐run impact of the recent Great Recession, especially on behaviours of unmarried mothers in the US, and through those behaviours on a mother’s physical and mental health. 1. Getting the Data One upfront difficulty in doing this type of research, which amounted in many ways to a new topic in economics, was that available data which focused on contemporaneous labour market outcomes were limited and not ideal. Panel data that followed individuals through their childhood years well into their adult years while capturing along the way the main economic, psychological, cognitive and social outcomes of interest alongside the major external events and shocks that have altered life trajectories were very rare indeed. The glaring exception of course were the subset of British cohort studies made easily and readily available to the research community (the 1958 National Child Development Study (NCDS), the 1970 British Cohort Study (BCS) and the 2000–1 Millennium Cohort Study (MCS)) that followed a group of babies typically born in a single week and for the 1958 and 1970 cohorts now well into their adult years. For these cohorts of British children, we have prospectively collected information on childhood physical, cognitive and psychological health collected in medical examinations and self‐reports, as well as conditions of parental households as kids. During the adult years, information is collected on adult earnings, family income, work, relationship stability and adult physical and mental health. The British cohort studies are one of Britain’s unique contributions in economics and the social sciences and the rest of the world is playing catch up. Such prospective data at a population level did not exist in the US and other countries so there had to be another way. The way was to include retrospective histories into the best economic panels. This was first done in the PSID (Smith, 2009); then ELSA in England and SHARE in continental Europe created complete retrospective life histories into adult years with content way beyond childhood health (family, jobs, salient life events, etc.). These retrospective histories were collected not only about individual respondents in the surveys but also about the communities and time periods in which they lived. This is important since these community‐time period histories contain salient information about external events that significantly impacted people in their lives. These external events are not only part of the retrospective accounts but are supplemented by objective data at the time measuring them contemporaneously. The evidence so far indicates good correspondence between the self‐reports and the actual events (Smith, 2009; Kesternich et al., 2014). The SHARE data used by Kesternich et al. (2015) used a combination of retrospective self‐reports of hunger during and immediately after WWII in Germany. Following a procedure that is becoming increasing common in this new literature, these self‐reports on hunger are combined with contemporaneous information on levels of caloric restrictions that were imposed in the four occupation zones in Germany, particularly in the years immediately after the end of WWII. Another excellent illustration of bringing the tool kit of economics into data appropriate for the analysis of early childhood effects is illustrated in Yi et al. (2015). They use a population‐based sample of 1,694 twins between the ages of 6 and 18‐years‐old originally living in Kunming, a rural region in Yunnan Province China in 2002. The data have a rich array of relevant attributes of the twins (birth weight, height, weight, cognitive scores, education, emotional difficulties, age, gender) and the mothers (investments in health and schooling, education, labour supply and consumption of both parents). The twin sample has the traditional advantage of being able to control for a wide array of unobserved traits including biological and genetic ones, an advantage that is exploited to the hilt in the article. The third data set used in the articles in this Feature illustrates the opportunistic approach in the recent economic literature on this topic. Currie et al. (2015) use what started as a non‐economic survey – the Fragile Families and Child Wellbeing Study (FF) – a sample of about 5,000 births between 1998 and 2000 in 20 large American cities. Like the British cohort studies, mothers and fathers were initially surveyed soon after the birth with four follow‐up interviews up to age 9. Since the focus of the Currie et al. (2015) study is on the short‐run impact of the Great Recession, they concentrate on comparisons between age 5 (years 2003–5) and age 9 (years 2007–10) samples. A unique aspect of FF is that it provides special samples of disadvantaged households (especially initially unmarried households) who may well be more vulnerable to economic shocks. Like Kesternich et al. (2015), Currie et al. (2015) also match the survey to key objective variables that can measure the shock‐unemployment rates at the state and local area. Similarly like the other two articles, survey content is expansive moving well beyond the traditional education, employment and income of economic surveys – health status, obesity, cigarette, drug and alcohol use and depression. 2. The Long Shadow of David Barker – Biology and Behaviour One of the most brilliant and influential minds working on early childhood effects is reflected in the seminal work of David Barker (1997). Barker is justifiably known for emphasising the biological pathway through which adverse events – in particular under‐nutrition in in utero programmes the foetus to have certain metabolic characteristics which then impact health in later life. A well‐established biological channel explains these effects, at least in part: hunger has long‐run effects if under‐nutrition occurs in certain sensitive periods of growth or fat storage required for later growth (Barker, 1997; Almond and Currie, 2011). The Barker hypothesis puts the focus very much on very early life events and a biological pathway. But one unfortunate consequence of an exclusive focus on the Barker hypothesis is that there exist other important pathways which are not primarily biological but rather behavioural and will not likely be at their maximum in the very earliest stages of human life. One example of this is contained in the article by Kesternich et al. (2015) who show that periods of severe hunger in early life affect not only health outcomes of older individuals (higher body weight and higher rates of obesity) but also food consumption patterns at older ages. The authors argue that fear of future episodes of hunger change preferences in favour of more food consumption than is normal for low adult income levels. These behavioural effects are not limited to in utero or very early years of childhood but are present at all childhood ages and largest amongst those in their teenage years, consistent with a later life behavioural pathway. This theme of biological and behavioural pathways is taken up explicitly both theoretically and empirically by Yi et al. (2015). Building on Heckman’s prior path breaking work (Cunha and Heckman, 2007), one of their most useful contributions is that they develop a theoretical and statistical framework in which the initial biological response (no differential reactions and expenditures on the affected and non‐affected twin) and the behavioural response which includes such reactions and expenditures. They find substantial evidence of both biological and behavioural responses in their analysis. Yi et al. (2015) report that compared to a twin who did not suffer an early age (0–3) negative physical health shock, the twin who did suffer the early health shock received more parental money in health investments, presumably to mitigate the effects of the health shock. However, the health shock did appear to reduce parental investments in human capital (education) of the affected child so that the affected child had lower levels of academic achievement and schooling. According to Yi et al. (2015), compensatory investments in health by parents reduced the adverse effects of health shocks by 50% but exacerbated the adverse impacts of the health shocks by 30%. On net they report that behavioural responses by the family act as a net equaliser between the twins in terms of their responses to the initial bad health shock. Yi et al. (2015) document other important behavioural responses. They find two key types of responses. First, in families with a child affected by an early health shock fathers end up spending less on their own consumption, and second, mothers are more likely to work. According to Yi et al. (2015), the strict dichotomy between biological and behavioural pathways is misleading since not only can they co‐exist but there are linkages between the two whereby behavioural reactions can either mitigate or reinforce the initial impact of the biological health shock. Behavioural responses are also a central theme of the article by Currie et al. (2015) who investigate the impact of the Great Recession, a severe and sudden economic contraction, on mothers (Currie et al., 2015). For example, they report that the crisis lead to increases in the smoking and drug use of mothers. 3. Heterogeneous Effects A natural first step is to initially focus and document strong main effects of economic shocks. Current research on early life effects has certainly not been an exception. However, all three articles in this Feature examine and estimate not only main effects of economic shocks but heterogonous effects as well. The three articles report considerable evidence of heterogeneous impacts of these economic shocks in their respective samples. To illustrate, Currie et al. (2015) explicitly analyse heterogonous effects in reactions to the Financial Crisis. They find the more severe negative effects on both mental and physical health took place amongst Black, Hispanic and less‐educated unmarried women thereby accentuating health inequalities. As the unemployment rate rose, African‐American mothers reported a reduction in excellent or very good health and increased their drug use while white mothers were more likely to increase drinking, obesity and to be depressed. Similarly, Yi et al. (2015) find that reductions in education investments due to a child health shock are larger in the urban sample where education was a more viable option in the first place and that the compensating health investments and decreasing education investments due to a child health shock are more significant for higher educated mothers. Finally, they report that the compensating health investments lower education investments for the female twin sample. Another aspect of heterogeneity is illustrated in Kesternich et al. (2015). Their results suggest that, among those with exposure to severe hunger as a child, those with lower income as adults were much more likely to have a high food share presumably because they were at greater risk of adult hunger. 4. Physical and Mental Health Effects Another legacy of the initial dominance of Barker hypothesis is its emphasis on physical health consequences with little mention of mental health effects. The recent economic literature suggests that the long‐term economic effects of early life mental health shocks are much more pronounced than physical health shocks (Smith and Delaney, 2010; Smith and Smith, 2010). Mental effects are also explored in the articles in this Feature. Yi et al. (2015) provide estimates on child health shocks on their emotional skills (feeling lonely, feeling easily distracted, feeling easily frightened, being emotionally unstable). They report that the twin with the negative health shock does worse on all emotional outcomes. While Currie et al. (2015) find no main effect of the unemployment rate on depression, Hispanic mothers showed a significant increase in the probability of being depressed. Similarly, in an earlier paper Kesternich et al. (2014) showed exposure to the events of WWII was consistently significantly associated with being more depressed as an adult, higher levels of adult diabetes, and reporting one’s subjective health as worse. 5. Conclusions The articles in the Feature each make useful contributions to the expanding literature on early childhood effects. While this topic is now an established part of economics, there is still much to be learned about what matters and why. In particular, the topic of what are the effective pathways to remediation so that young lives are not spent trapped by the past should go high on that list. References Almond , D. and Currie , J. ( 2011 ). ‘ Killing me softly: the fetal origins hypothesis ’, Journal of Economic Perspectives , vol. 25 ( 3 ), pp. 153 – 72 . Google Scholar Crossref Search ADS PubMed WorldCat Barker , D.J.P. ( 1997 ). ‘ Maternal nutrition, fetal nutrition and diseases in later life ’, Nutrition , vol. 13 , pp. 807 – 13 . Google Scholar Crossref Search ADS PubMed WorldCat Cunha , F. and Heckman , J.J. ( 2007 ). ‘ The technology of skill formation ’, American Economic Review , vol. 97 ( 2 ), pp. 31 – 47 . Google Scholar Crossref Search ADS WorldCat Currie , J. , Duque , V. and Garfinkel , I. ( 2015 ). ‘ The great recession and mother’s health ’, Economic Journal , vol. 125 ( 588 ), pp. F311 – 46 . Google Scholar Crossref Search ADS WorldCat Kesternich , I. , Siflinger , B., Smith , J.P. and Winter , J. ( 2015 ). ‘ Individual behaviour as a pathway between early‐life shocks and adult health: evidence from hunger episodes in post‐war Germany ’, Economic Journal , vol. 125 ( 588 ), pp. F372 – 93 . Google Scholar Crossref Search ADS WorldCat Kesternich , I. , Siflinger , B., Smith , J.P. and Winter , J. ( 2014 ). ‘ The effects of World War II on economic and health outcomes across Europe ’, The Review of Economics and Statistics , vol. 96 ( 1 ), pp. 103 – 18 . Google Scholar Crossref Search ADS PubMed WorldCat National Child Development Study and the 1970 British Cohort Study . ( 2004 ). http://www.cls.ioe.ac.uk (last accessed: 20 August 2014). Smith , J.P. ( 2009a). ‘ The impact of childhood health on adult labor market outcomes ’, Review of Economics and Statistics , vol. 91 ( 3 ), pp. 478 – 89 . Google Scholar Crossref Search ADS PubMed WorldCat Smith , J.P. ( 2009b). ‘ Re‐constructing childhood health histories ’, Demography , vol. 46 ( 2 ), pp. 387 – 403 . Google Scholar Crossref Search ADS PubMed WorldCat Smith , J.P. and Delaney , L. ( 2010 ). ‘ Childhood health – trends and consequences over the life course ’, Future of Children , vol. 22 ( 1 ), pp. 43 – 63 . OpenURL Placeholder Text WorldCat Smith , J.P. and Smith , G.C. ( 2010 ). ‘ Long‐term economic costs of psychological problems during childhood ’, Social Science and Medicine , vol. 71 ( 1 ), pp. 110 – 5 . Google Scholar Crossref Search ADS PubMed WorldCat Yi , J. , Heckman , J., Zhang , J. and Conti , G. ( 2015 ). ‘ Early life shocks, intra‐household resource allocation and child outcomes ’, Economic Journal , vol. 125 ( 588 ), pp. F347 – 71 . Google Scholar Crossref Search ADS WorldCat © 2015 Royal Economic Society

Rivkin, Steven, G.;Schiman, Jeffrey, C.

doi: 10.1111/ecoj.12315pmid: N/A

Abstract It seems likely the magnitude of any causal link between achievement and instruction time depends upon the quality of instruction, the classroom environment and the rate that students translate classroom time into added knowledge. In this article, we use panel data methods to investigate instruction time effects in the 2009 Programme for International Student Assessment data. The empirical analysis shows that achievement increases with instruction time and that the increase varies by both the amount of time and the classroom environment. The results indicate that school circumstances are important determinants of the benefits and desirability of increased instruction time. The belief that increased time on task raises output would go unchallenged in most settings, but public schooling is an exception. Arguments of extensive inefficiencies that dampen the return to additional time or spending are widespread. Nonetheless, many countries and American jurisdictions have recently embraced longer school days or more time devoted to core academic classes. The conceptual appeal is clear: additional time may ‘allow teachers to cover more material and examine topics in greater depth; build‐in more project‐based and hands‐on learning; individualize and differentiate instruction; and answer students’ questions’ (Why Time Matters, 2015).1 Many point to Knowledge is Power Program (KIPP) academy schools in the US for evidence of the benefits of extended time in class. Through a longer school day and Saturday school, instruction time averages around 1,700 hours per year in KIPP schools, roughly 60% more hours than the US average, and evidence suggests that KIPP students significantly outperform similar students in regular public schools (Farbman, 2011). Of course KIPP academy schools differ along other dimensions as well, so it is difficult to isolate the specific mechanisms that account for KIPP’s apparent success.2 Recent research generally supports the notion that additional instruction time raises achievement, though difficulties isolating an exogenous source of variation raise questions about the strength of much of the evidence.3 To illustrate the empirical difficulty consider the difference between academic and vocational secondary schooling. Academic schools typically spend more time in mathematics and language arts instruction and boast higher achievement than vocational schools but instruction time differences across sectors do not provide a valid source of identification because of positive selection into academic schools. Alternatively, instruction‐time variation resulting from the desire to supplement the education of lower achievers would tend to produce downward biased estimates. Thus it is not possible to determine a priori if the simple correlation between achievement and instruction time overstates or understates the causal relationship. Moreover, it seems likely that the magnitude of any causal link between achievement and instruction time depends upon the quality of instruction, the classroom environment, the rate at which students translate classroom time into added knowledge and the activities reduced in order to increase instruction time. For example, expanded instruction time in response to poor mathematics achievement may have little impact if an ineffective curriculum, inadequate teacher subject matter knowledge, or disruptive behaviour led to the low achievement in the first place. Furthermore, even if existing class time is effective, there may be decreasing marginal benefits to additional minutes if the quality of instruction, classroom environment, or student effort diminishes with time. Finally, the benefit of added instruction time for a particular subject is likely to depend on the source of that time. A reallocation of time from social studies to language arts might be expected to have a smaller benefit than a reallocation of time from vocational training to language arts. In this article, we focus on such potential heterogeneity and investigate the pattern of instruction time effects using the 2009 Programme for International Student Assessment (PISA) data. We are particularly interested in the mediating effects of the classroom environment and the character of any diminishing returns. In order to overcome biases introduced by the non‐random allocation of instruction time and unobserved differences in school quality, we build on the work of Lavy (2010) and use within‐school variation across subjects or grades to identify the effects. The appeal of within school variation across subjects is that students taking both mathematics and language arts (for example) bring the same general skills and experience the same school environment for each subject. Therefore, neither heterogeneity in general ability and work habits nor general school quality will contaminate estimates of instruction‐time effects identified from average instruction‐time differences between subjects. This leaves only subject‐specific factors related to instruction time as potential confounding influences. Within‐school variation, including differences across tracks is likely to be related to differences in such factors. Therefore, we aggregate instruction time to the school‐by‐subject level. The possibility remains that school quality or school average ability differences by subject could exist and either precipitate or result from instruction‐time differences. Therefore, we also consider differences across grades within a school and subject as an alternative source of variation. This comparison is complicated by the fact that 9th graders have one year fewer of schooling than 10th graders and that each grade contains a different cohort of students. Nonetheless, as we discuss below, as long as skill and instruction‐time differences across cohorts are not related, the within‐subject variation produces lower bound estimates. The empirical analysis shows that achievement increases with instruction time and that the increase varies by both amount of time and classroom environment. First, there is evidence of diminishing returns, though the rate of decrease appears to be quite gradual. Second, there is evidence that better classroom environments as measured by responses to questions about student behaviour and student–teacher interactions also appear to raise the benefit of additional instruction time. These results indicate that school circumstances are important determinants of the likely benefits and desirability of increased instruction time. 1. Data The data is from the 2009 PISA, a survey and assessment administered to 15‐year old students around the world. Each student is assessed in mathematics, science and language arts and then answers a set of questions about family background, school environment, home environment and study habits.4 The PISA test focuses on knowledge applications and is thought to be highly informative about the quality of preparation for higher education and the labour market. A representative from each school also provides information on staff, environment, pedagogical practices and human resource practices. We focus on mathematics and language arts because the quality of mathematics education is likely to affect performance in the science examination. Because our research design identifies instruction time effects on the basis of between subject differences in test scores and instruction time, this potential spillover is especially problematic. We expect there to be little mathematics and language arts spillover at the high school level. In the Appendix, we provide results based on all three subjects combined that are consistent with the presence of substantial spillovers. The PISA test was administered in 2000, 2003, 2006 and 2009. We use the 2009 wave because of the richness of information on instruction time and the availability of measures about classroom environment. In 2009, students were asked the number of mathematics, science and language arts classes attended per week and the length in minutes of an average class. This potentially permits us to identify the effects of additional classes per week and minutes per class separately but in reality there is little variation in average class length across subjects. To calculate average instruction time for each subject, grade and school, we multiply the average weekly number of classes by the length of an average class. The variability and range of responses to the instruction time questions raises concerns about data quality and measurement that may not be fully addressed by aggregation. Non‐trivial numbers of students report more than ten classes per week in a subject or class lengths of over two hours. In order to mitigate errors in variables bias, we exclude information on classes per week or average length of classes from the school average calculations if the reported number of classes exceeds ten or class length exceeds two hours.5 These restrictions set to missing approximately 3% of the sample. The regressions reported in the article come from samples restricted to students with non‐missing instruction time information which ultimately drops 11% of the sample. The addition of those with missing or excluded information on class time makes the estimates somewhat less precise though the results are qualitatively similar. By comparison, the 2006 data used in Lavy (2010) (at the time of his writing, 2009 data were not yet available) report instruction time categories only. In 2006, students responded to weekly time spent in each subject in five intervals: ‘no time; less than 2 hours a week; 2 or more but less than 4 hours a week; 4 or more but less than 6 hours a week; and 6 or more hours a week’. A clear disadvantage of this taxonomy is the absence of detailed information on numbers of classes and minutes. In addition, the taxonomy produces instruction time distributions that differ substantially from those for 2000 and 2009. While the majority of weekly instruction time would fall in the 2 to <4 hour category based on survey responses in 2000 and 2009, the distribution is more evenly split between 2 to <4 hour and the 4 to <6 hour categories in 2006 (not shown), raising concerns about the accuracy of student responses in that year. We use factor analysis to generate the index of classroom environment based on school administrator responses to a series of questions listed in Table 1 about the extent to which the learning of students is hindered by a number of phenomena. The list includes disruption, other aspects of student behaviour, student–teacher interactions and other aspects of teacher behaviour. Respondents could check ‘not at all, some of the time, most of the time, or all of the time’. Note that we transform the answers such that a higher value on our index of quality reflects a classroom environment that is more conducive to learning. Table 1 Distribution of Responses to Classroom Quality Measures . ‘In your school, to what extent is the learning of students hindered by the following phenomenon?’ . Not at all . Very little . To some extent . A lot . Total . Student absences 0.12 0.39 0.36 0.13 18,033 Student–teacher relations 0.33 0.52 0.12 0.03 18,006 Students disrupt classes 0.18 0.47 0.29 0.07 18,016 Students skip classes 0.20 0.45 0.26 0.08 18,005 Students lack respect for teachers 0.27 0.51 0.18 0.04 18,015 Student alcohol or drug use 0.56 0.34 0.06 0.03 17,931 Student bullying 0.35 0.51 0.11 0.02 17,997 . ‘In your school, to what extent is the learning of students hindered by the following phenomenon?’ . Not at all . Very little . To some extent . A lot . Total . Student absences 0.12 0.39 0.36 0.13 18,033 Student–teacher relations 0.33 0.52 0.12 0.03 18,006 Students disrupt classes 0.18 0.47 0.29 0.07 18,016 Students skip classes 0.20 0.45 0.26 0.08 18,005 Students lack respect for teachers 0.27 0.51 0.18 0.04 18,015 Student alcohol or drug use 0.56 0.34 0.06 0.03 17,931 Student bullying 0.35 0.51 0.11 0.02 17,997 Notes Each school representative responds to a series of questions about the school and classroom climate (Q17) in the 2009 School Questionnaire. We use these responses to construct the classroom quality scale. Note that we reorder the responses so that a higher values corresponds to less hindrance and a higher quality environment (i.e. 1 = a lot; 2 = to some extent; 3 = very little; and 4 = not at all). The first four columns report shares of schools in each cell, and the ‘Total’ column reports the number of schools. Open in new tab Table 1 Distribution of Responses to Classroom Quality Measures . ‘In your school, to what extent is the learning of students hindered by the following phenomenon?’ . Not at all . Very little . To some extent . A lot . Total . Student absences 0.12 0.39 0.36 0.13 18,033 Student–teacher relations 0.33 0.52 0.12 0.03 18,006 Students disrupt classes 0.18 0.47 0.29 0.07 18,016 Students skip classes 0.20 0.45 0.26 0.08 18,005 Students lack respect for teachers 0.27 0.51 0.18 0.04 18,015 Student alcohol or drug use 0.56 0.34 0.06 0.03 17,931 Student bullying 0.35 0.51 0.11 0.02 17,997 . ‘In your school, to what extent is the learning of students hindered by the following phenomenon?’ . Not at all . Very little . To some extent . A lot . Total . Student absences 0.12 0.39 0.36 0.13 18,033 Student–teacher relations 0.33 0.52 0.12 0.03 18,006 Students disrupt classes 0.18 0.47 0.29 0.07 18,016 Students skip classes 0.20 0.45 0.26 0.08 18,005 Students lack respect for teachers 0.27 0.51 0.18 0.04 18,015 Student alcohol or drug use 0.56 0.34 0.06 0.03 17,931 Student bullying 0.35 0.51 0.11 0.02 17,997 Notes Each school representative responds to a series of questions about the school and classroom climate (Q17) in the 2009 School Questionnaire. We use these responses to construct the classroom quality scale. Note that we reorder the responses so that a higher values corresponds to less hindrance and a higher quality environment (i.e. 1 = a lot; 2 = to some extent; 3 = very little; and 4 = not at all). The first four columns report shares of schools in each cell, and the ‘Total’ column reports the number of schools. Open in new tab Research finds substantial variation in teacher value added to achievement, making it a likely mediator of the benefit of additional instruction time. Unfortunately, the information about teachers included in the PISA, such as fraction certified, has been found to explain little of the variation in teacher effectiveness. Data limitations prevent us from estimating teacher value added so we are unable to investigate the mediating effect of teacher quality on the benefit of additional instruction time. Note, however, that the classroom environment variable does reflect teacher effects on student–teacher interactions, the degree of disruptions and other aspects of the learning environment that teachers influence. PISA test booklets are designed so that not every student takes both a mathematics and language arts component. Instead, each student is randomly assigned 1 of 21 test booklets, 14 of which contain both mathematics and language arts components.6 Those who do not take a mathematics or language arts component have their scores for these subjects imputed by the PISA test makers based on the available assessments.7 Because our research design relies on information across subjects, prior to aggregation we drop students who do not take both mathematics and language arts and students taking a one‐hour version of the test, given to special‐needs students. This restriction drops approximately 31% of the sample. We also limit the analysis sample to the same set of observations used in all regressions, which drops approximately 3% of the remaining sample. The main sample used in this analysis includes 507,798 observations for 253,899 9th and 10th grade students in 16,310 schools in 72 countries. We focus on these two grades in order to minimise complications introduced by grade retention. Some components of the analysis further restrict the sample to only schools with both 9th and 10th grades which leaves 253,286 observations, roughly half the sample in 7,374 schools. Table A1 reports descriptive statistics. 2. Empirical Model This Section describes the empirical framework we use to investigate the effects of instruction time on achievement. Here we address potential biases introduced by unobserved student and school factors and the possibility that the benefits of additional time vary by the quality of the classroom environment. The association between instruction time and both student and school factors results from the fact that instruction time is determined by family selection of schools, assignment of students to schools and courses of study, and systemic rules about school operations. Academically oriented students are much more likely to attend academic high schools that devote more class time to mathematics and language arts. Schools may assign higher achievers in a subject to courses that meet more often, or schools may assign struggling students to additional remedial sections. Governments concerned about poor performance in mathematics may mandate a minimum amount of instruction time, or governments with a strong commitment to mathematics may mandate more class time along with higher salaries and stronger teacher training. Finally, the analysis must consider possible endogenous family responses to realised school quality, as additional instruction time outside of school can substitute for lower or less productive instruction time during school (Todd and Wolpin, 2003). Two things quickly become clear: instruction time is likely to be related to a number of factors that may themselves be determinants of achievement; the direction of those relationships and, therefore, the direction of any bias from unobserved factors are ambiguous. By comparison, potential heterogeneity in returns to additional instruction time is likely to be more predictable along at least two important dimensions. First, diminishing returns to additional time are likely to set in at some point due to fatigue. Second, extending the instruction time in a classroom plagued by disruption or poor relations between students and teachers is likely to yield little if any benefit. We investigate these predictions in the empirical analysis. Importantly, the return to additional instruction time for a given subject depends crucially on the opportunity cost of that time. Schools may reallocate time away from other academic subjects, physical education, or non‐academic subjects. Alternatively, schools could extend the school day, in which case the time would come from non‐school activities. Note that the opportunity cost of time may in some cases include learning that contributes to achievement in the same subject, which could be the case if science instruction time was taken to expand math instruction time and science education contributed to the development of mathematics skills. Figure 1 reports country‐specific correlation between weekly hours of instruction in mathematics on the one hand and weekly hours in science, language arts, and all courses other than mathematics, science or language arts combined on the other in order to illustrate variation across countries in the allocation of class time among subjects. We focus on weekly hours instead of weekly class periods because schools with shorter class periods may offer more classes in total during the week. Although the magnitudes of the correlations between weekly hours of mathematics instruction and weekly hours in science and language arts vary substantially, the vast majority of countries exhibit positive correlations consistent with the view that the devotion of more time to one academic subject typically accompanies the devotion of more time to another. In contrast, approximately half the correlations between mathematics and other classes are negative which is consistent with the notion that vocational high schools devote less class time to academic subjects. Taken as a whole, Figure 1 suggests that additional mathematics instruction time tends to be found in schools with more total class time or schools that focus on academic subjects. Note that the average correlation between weekly instruction time in different subjects may differ markedly from tradeoffs at the margin that occur when a school decides to increase instruction time for a specific subject. Fig. 1. Open in new tabDownload slide Correlations Between Weekly Hours of Instruction in Mathematics and Other Subjects by Country Notes. There are 72 countries in our data. Students report the number of mathematics, language and science class periods attended each week. Students also report the total number of class periods attended each week. To calculate ‘Other’ class periods, we subtract the sum of mathematics, language and science class periods from total class periods. We multiply class periods by length of an average class to obtain weekly hours of instruction. We set total classes to missing if the reported total is >50 per week (approx. 1% of sample) and we set other classes to missing if it is <0 (approx. 5% of sample). Fig. 1. Open in new tabDownload slide Correlations Between Weekly Hours of Instruction in Mathematics and Other Subjects by Country Notes. There are 72 countries in our data. Students report the number of mathematics, language and science class periods attended each week. Students also report the total number of class periods attended each week. To calculate ‘Other’ class periods, we subtract the sum of mathematics, language and science class periods from total class periods. We multiply class periods by length of an average class to obtain weekly hours of instruction. We set total classes to missing if the reported total is >50 per week (approx. 1% of sample) and we set other classes to missing if it is <0 (approx. 5% of sample). 2.1. Baseline Empirical Model The identification of the effect of instruction time on achievement requires exogenous variation that is not related to unobserved differences in students and schools. Existing research shows that available variables explain little of the variation in the quality of instruction and student skill and, therefore, it is necessary to account for unobserved student and school factors. Fortunately, as Dee and Cohodes (2008) and Lavy (2010) point out, the testing of students in multiple subjects enables the use of panel data methods that account for differences in school and teacher quality, school climate and ability that span both subjects. The 2009 PISA data provides test results for mathematics, language arts and science; student fixed effects regressions use instruction‐time differences within students and across subjects to identify the estimates. Importantly, the student fixed effects account for differences in both schools and students in 2009 (essentially student‐by‐year and school‐by‐year effects) that span the included subjects. The fixed effects do not account for any association between skill in a subject and class time in that subject introduced by the purposeful placement of students into courses. For example, weaker mathematics students may be more likely to be placed in lower‐level mathematics courses that could meet less frequently and the data may not contain information that could be used to control for underlying mathematics skill. Therefore, following Lavy (2010), we aggregate instruction time and test scores for each student to the school‐by‐grade‐by‐subject level. Such aggregation eliminates the potential confounding influence of within‐school variation in the difference between mathematics and language arts skills. It does not, however, account for average differences between subjects in ability, teacher quality or other dimensions of school quality that are related to differences in class time. Therefore, we also estimate alternative models that use instruction‐time differences between grades rather than subjects to identify the estimates. In order to highlight the key assumptions underlying the various fixed effects specifications, we begin with a simple model that ignores heterogeneity in the return to class time. Equation (1) models achievement A in subject k in grade g in school s in country c as a function of minutes per week of instruction M and a series of error components that capture interactions among country, school, grade and subject. Note that the country is fully subsumed by the school and is included as an interaction with grade and subject to highlight the potential importance of national policies and practices regarding curriculum, accountability, funding and other factors: Akgsc=Mkgscλ+ηs+ϕg+σk+ζc+θkgc+τks+ωgs+vkgsc.(1) The school‐by‐grade fixed effect (ω) accounts for differences in average ability, level of disruption and school quality that are common across subjects for students in a particular cohort, grade, school and country. Therefore all subject invariant differences in academic skills and school quality at each grade level are removed. Only within school and grade instruction time differences among subjects remain for identification. Note, importantly, that the school‐by‐grade fixed effects fully account for a range of subject invariant influences, including national minimum school starting and leaving ages, school funding and governance structures and family background. The school‐by‐grade fixed effect does not account for differences among subjects in either instruction time or various other factors that could influence achievement. These include, but are not limited to, national curricula, the quality of instruction in one subject in relation to the other and subject‐specific student skills. The country‐by‐grade‐by‐subject fixed effect (θ) captures some such influences, including national curricula but it does not capture subject‐specific abilities or instructional quality specific to schools that are related to instruction time. Our estimate of instruction time effects would be biased upward if the difference between school‐by‐grade average mathematics and language arts instruction time is positively related to the difference in average abilities in mathematics and language arts, as would be the case if analytically skilled students attended schools that devoted more time to mathematics instruction. A similar upward bias would arise if the instruction difference was positively related to the difference in the quality of mathematics versus language arts instruction. Of course, a negative relationship between instruction time in a subject on the one hand and ability or instructional quality on the other would introduce a negative bias. It is not clear whether confounding subject‐specific factors introduce bias. Nonetheless, the availability of multiple grades per school enables an alternative approach that accounts directly for school‐by‐subject factors. Rather than identifying effects on the basis of within school‐by‐grade instruction‐time differences across subjects, effects can be identified on the basis of instruction‐time differences across grades for the same subjects. Essentially this amounts to including a school‐by‐subject fixed effect into (1) and excluding the school‐by‐grade fixed effect. If instruction time is significantly related to achievement, a larger instruction time difference in mathematics courses between 9th and 10th grade should be associated with a larger difference in test scores. As opposed to the school‐by‐grade fixed effect specifications, the school‐by‐subject specification accounts for subject‐specific differences among schools in both school quality and average student skill. However, this advantage is potentially offset by the fact that 9th and 10th grade mathematics and language arts scores are produced by different students who are not in the same cohort. Importantly, the strict exogeneity assumption does not require equality in average ability or the quality of instruction across grades but only that any differences are not related to differences in grade‐average instruction time. As long as the course schedule for a subject and grade does not respond to grade differences in student or teacher skills then one would not expect performance‐induced changes in the course schedule to occur and introduce bias. However, inadequate treatment of learning dynamics can introduce correlation between lagged instruction time and the error which would violate the strict exogeneity assumption. Unless learning fully depreciates each year, a better 9th grade education will raise achievement in 10th grade as well as 9th grade. Therefore, additional 9th grade instruction time will tend to increase 10th grade achievement. As Meghir and Rivkin (2011) illustrate, fixed effect estimates based on achievement differences across grades will tend to introduce attenuation bias in models that compare achievement in the respective grades and do not account for prior achievement. Even though our analysis does not compare achievement of the same student in successive grades, persistence in the structure of instruction time across cohorts would still attenuate estimates based on instructional time differences between 9th and 10th grade. Importantly, the direction of bias introduced by this specification error is unambiguously toward zero, meaning that the school‐by‐subject fixed effect estimates are likely to provide a lower bound of the average instruction time effect.8 Persistence in the structure of instruction time across grades also complicates the interpretation of the estimates from the school‐by‐grade specifications discussed above. Specifically, identification based on mathematics and language arts instruction time differences in 10th grade, for example, does not produce an unbiased estimate of the effects of instruction time on achievement in 10th grade if the difference in 10th grade is correlated with the difference in 9th grade. Rather, the estimate would capture the effect of instruction time in 10th grade plus persistent effects from differences in previous grades. The magnitude and direction of the bias would depend upon the correlation between instruction time differences across grades and the structure of knowledge depreciation. In this sample, the correlation equals 0.41 indicating that the school‐by‐grade fixed effect estimates will tend to overstate the effect of instruction time in a grade. A final complication arises from the possibility that parents may respond to instruction time when determining family education inputs (Todd and Wolpin, 2003). The direction of bias that would arise from an endogenous family response is unclear. For example, if parents judge the school to lack instruction time in a particular subject, they may compensate by studying more with their child at home. Assuming that more parental help is positively related to student achievement and negatively related to classroom instruction time, failing to account for the endogenous parental response would tend to bias downward the estimated effect of instruction time. As an informal specification test, we include subject‐specific measures of out‐of‐school instruction time. The 2009 wave of PISA asks ‘How many hours do you typically spend per week attending <out‐of‐school‐time lessons> in the following subjects (at school, at home or somewhere else)?’ The student can respond ‘do not attend; less than 2 hours; 2 to 4 hours; 4 to 6 hours; or 6 or more hours’. We aggregate student responses to these questions to the school‐by‐grade‐by‐subject level for the same reason we aggregate instruction time. Table A2 shows that the inclusion of this variable has little to no effect on the instruction time estimates, providing evidence that any such parental behaviour does not introduce bias in this framework. Even with the numerous fixed effects, alternative models and specification checks, it remains possible that unobserved factors could confound the estimates. Therefore, the results do not provide clearly unbiased estimates of the causal relationship between achievement and instruction time that would be produced by an ideal random assignment experiment without non‐random attrition. This should be kept in mind when interpreting and evaluating the findings. 2.2. Dimensions of Heterogeneity We explore the possibility that there are diminishing returns to instruction time and that the effect depends on the classroom environment. The number of classes per week and length of a class combine to determine the total number of minutes per week; it may matter if, for example, 180 minutes per week are divided into four 45‐minute classes or three 60‐minute classes. Information on the number of classes per week and minutes of an average class period potentially enables us to identify diminishing returns along each of these dimensions. In reality, there is little variation across subjects in the length of classes at a school and, therefore, we focus on the number of classes and total minutes and use quadratic and higher‐order terms to investigate the presence and magnitude of diminishing returns. When we investigate heterogeneity by classroom environment, we use an index constructed from school administrator responses to a series of questions about student behaviour and student–teacher relations. Although the index does not vary within schools, it can be interacted with instruction time to produce information on heterogeneity in the return to additional instruction time by classroom environment. Table 1 illustrates the frequency distributions of responses to each of the questions pertaining to the classroom environment. The majority of schools report having higher quality learning environments (i.e. that learning is hindered ‘not at all’ or ‘very little’). Nonetheless, a number of schools report lower quality environments (i.e. environments where learning is hindered ‘to some extent’ or ‘a lot’). To produce the index of classroom quality, we use factor analysis that takes the ordinal character of the responses into consideration. Table 2 lists the variable factor loadings. A single combination of factors explains 98.25% of the variance in response to the classroom quality questions. The factor weightings illustrate the high correlation of all student behaviour and student–teacher interaction variables in the construction of the classroom environment index. Therefore, it is not possible to identify the effects of disruption, the quality of student–teacher interactions, student attendance, or disrespectful behaviour towards teachers or peers separately. Note that we reorder responses to the questions listed in Table 1 so that higher index values indicate a higher quality, less disruptive learning environment. Table 2 Factor Analysis of Questions on Student and Teacher Behaviour . Classroom quality . Factor loadings . Scoring coefficients . Lack of student absences 0.7048 0.1573 Lack of student disruption 0.7680 0.1753 Favourable teacher–student relations 0.6657 0.1149 Lack of student skipping 0.7735 0.2127 Students respect teachers 0.8124 0.2327 Lack of student drug use 0.7010 0.1428 Lack of student bullying 0.7289 0.1693 . Classroom quality . Factor loadings . Scoring coefficients . Lack of student absences 0.7048 0.1573 Lack of student disruption 0.7680 0.1753 Favourable teacher–student relations 0.6657 0.1149 Lack of student skipping 0.7735 0.2127 Students respect teachers 0.8124 0.2327 Lack of student drug use 0.7010 0.1428 Lack of student bullying 0.7289 0.1693 Notes The factor analysis takes place at the school level and results are merged back to the student‐level file. We then standardise the classroom quality scale to have a mean of zero and a standard deviation of one. Higher values on the classroom quality scale reflect higher quality environments. The eigenvalue for the classroom quality factor is 3.81 and the proportion of variance it explains is 98.25%. Given the ordered categorical nature of the variables, we use a Polychoric correlation matrix to conduct the factor analysis. Open in new tab Table 2 Factor Analysis of Questions on Student and Teacher Behaviour . Classroom quality . Factor loadings . Scoring coefficients . Lack of student absences 0.7048 0.1573 Lack of student disruption 0.7680 0.1753 Favourable teacher–student relations 0.6657 0.1149 Lack of student skipping 0.7735 0.2127 Students respect teachers 0.8124 0.2327 Lack of student drug use 0.7010 0.1428 Lack of student bullying 0.7289 0.1693 . Classroom quality . Factor loadings . Scoring coefficients . Lack of student absences 0.7048 0.1573 Lack of student disruption 0.7680 0.1753 Favourable teacher–student relations 0.6657 0.1149 Lack of student skipping 0.7735 0.2127 Students respect teachers 0.8124 0.2327 Lack of student drug use 0.7010 0.1428 Lack of student bullying 0.7289 0.1693 Notes The factor analysis takes place at the school level and results are merged back to the student‐level file. We then standardise the classroom quality scale to have a mean of zero and a standard deviation of one. Higher values on the classroom quality scale reflect higher quality environments. The eigenvalue for the classroom quality factor is 3.81 and the proportion of variance it explains is 98.25%. Given the ordered categorical nature of the variables, we use a Polychoric correlation matrix to conduct the factor analysis. Open in new tab 3. Results We report a series of estimates that characterise the relationship between achievement and instruction time using the fixed‐effect specification described in the previous Section. Because class length tends not to vary across subject or grade within a school, we present results for both the number of classes and total hours per week in most Tables. The initial set of results reports the average effect of instruction time on achievement. Subsequently, we explore the existence of non‐linear effects of both hours and classes and potential heterogeneity in the effects of instruction time by classroom environment. Prior to presenting the fixed effect results, we describe the within‐school variation across subjects in class time and achievement used to identify the estimates. 3.1. Instruction Time Differences Between Subjects In Table 3, we describe the distribution of weekly language‐arts instruction time conditional on mathematics instruction time for both total weekly minutes and the number of classes. Although the diagonal elements have the highest frequencies, a substantial share of schools report instruction time disparities between subjects. Consider first the top panel on weekly minutes. Among students reporting mathematics minutes between 200 and 219, only slightly more than half report language arts minutes that fall in the same category. Among those with other than 200–219 minutes of language‐arts instruction time, the majority spends more time in language arts than mathematics classes. Not surprisingly, at lower levels of mathematics instruction time a larger share of students spend more as opposed to less time in language arts classes. Notice that class time differences tend to exceed 20 minutes per week at higher values of mathematics instructions, consistent with the fact that minutes per class in these categories tend to exceed 40 minutes. Table 3 Distributions of Weekly Language Arts Instructional Minutes and Classes Conditional on Mathematics Instruction Time Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . Observations . 0–99 0.410 0.041 0.022 0.005 0.016 0.009 0.017 8,261 100–179 0.322 0.578 0.131 0.179 0.080 0.078 0.065 48,909 180–199 0.150 0.104 0.472 0.007 0.134 0.081 0.037 35,938 200–219 0.017 0.137 0.005 0.570 0.008 0.160 0.052 36,350 220–239 0.026 0.053 0.181 0.006 0.469 0.057 0.035 31,211 240–279 0.026 0.053 0.148 0.162 0.230 0.483 0.160 53,413 280+ 0.050 0.035 0.040 0.071 0.064 0.132 0.635 39,817 All 1.000 1.000 1.000 1.000 1.000 1.000 1.000 Observations 9,041 43,439 41,109 34,176 35,761 51,452 38,921 253,899 Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . Observations . 0–99 0.410 0.041 0.022 0.005 0.016 0.009 0.017 8,261 100–179 0.322 0.578 0.131 0.179 0.080 0.078 0.065 48,909 180–199 0.150 0.104 0.472 0.007 0.134 0.081 0.037 35,938 200–219 0.017 0.137 0.005 0.570 0.008 0.160 0.052 36,350 220–239 0.026 0.053 0.181 0.006 0.469 0.057 0.035 31,211 240–279 0.026 0.053 0.148 0.162 0.230 0.483 0.160 53,413 280+ 0.050 0.035 0.040 0.071 0.064 0.132 0.635 39,817 All 1.000 1.000 1.000 1.000 1.000 1.000 1.000 Observations 9,041 43,439 41,109 34,176 35,761 51,452 38,921 253,899 Panel (b) Number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . Observations . 0–2 0.496 0.113 0.027 0.023 0.030 19,187 3 0.224 0.484 0.146 0.062 0.041 42,435 4 0.186 0.311 0.536 0.210 0.098 80,036 5 0.060 0.067 0.215 0.555 0.199 70,031 6+ 0.034 0.025 0.076 0.150 0.631 42,210 All 1.000 1.000 1.000 1.000 1.000 Observations 19,088 41,238 83,095 73,678 36,800 253,899 Panel (b) Number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . Observations . 0–2 0.496 0.113 0.027 0.023 0.030 19,187 3 0.224 0.484 0.146 0.062 0.041 42,435 4 0.186 0.311 0.536 0.210 0.098 80,036 5 0.060 0.067 0.215 0.555 0.199 70,031 6+ 0.034 0.025 0.076 0.150 0.631 42,210 All 1.000 1.000 1.000 1.000 1.000 Observations 19,088 41,238 83,095 73,678 36,800 253,899 Notes Here, we present the joint distribution of students by separate groupings of weekly mathematics and language arts instruction time (panel (a)) and number of classes per week (panel (b)). Open in new tab Table 3 Distributions of Weekly Language Arts Instructional Minutes and Classes Conditional on Mathematics Instruction Time Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . Observations . 0–99 0.410 0.041 0.022 0.005 0.016 0.009 0.017 8,261 100–179 0.322 0.578 0.131 0.179 0.080 0.078 0.065 48,909 180–199 0.150 0.104 0.472 0.007 0.134 0.081 0.037 35,938 200–219 0.017 0.137 0.005 0.570 0.008 0.160 0.052 36,350 220–239 0.026 0.053 0.181 0.006 0.469 0.057 0.035 31,211 240–279 0.026 0.053 0.148 0.162 0.230 0.483 0.160 53,413 280+ 0.050 0.035 0.040 0.071 0.064 0.132 0.635 39,817 All 1.000 1.000 1.000 1.000 1.000 1.000 1.000 Observations 9,041 43,439 41,109 34,176 35,761 51,452 38,921 253,899 Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . Observations . 0–99 0.410 0.041 0.022 0.005 0.016 0.009 0.017 8,261 100–179 0.322 0.578 0.131 0.179 0.080 0.078 0.065 48,909 180–199 0.150 0.104 0.472 0.007 0.134 0.081 0.037 35,938 200–219 0.017 0.137 0.005 0.570 0.008 0.160 0.052 36,350 220–239 0.026 0.053 0.181 0.006 0.469 0.057 0.035 31,211 240–279 0.026 0.053 0.148 0.162 0.230 0.483 0.160 53,413 280+ 0.050 0.035 0.040 0.071 0.064 0.132 0.635 39,817 All 1.000 1.000 1.000 1.000 1.000 1.000 1.000 Observations 9,041 43,439 41,109 34,176 35,761 51,452 38,921 253,899 Panel (b) Number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . Observations . 0–2 0.496 0.113 0.027 0.023 0.030 19,187 3 0.224 0.484 0.146 0.062 0.041 42,435 4 0.186 0.311 0.536 0.210 0.098 80,036 5 0.060 0.067 0.215 0.555 0.199 70,031 6+ 0.034 0.025 0.076 0.150 0.631 42,210 All 1.000 1.000 1.000 1.000 1.000 Observations 19,088 41,238 83,095 73,678 36,800 253,899 Panel (b) Number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . Observations . 0–2 0.496 0.113 0.027 0.023 0.030 19,187 3 0.224 0.484 0.146 0.062 0.041 42,435 4 0.186 0.311 0.536 0.210 0.098 80,036 5 0.060 0.067 0.215 0.555 0.199 70,031 6+ 0.034 0.025 0.076 0.150 0.631 42,210 All 1.000 1.000 1.000 1.000 1.000 Observations 19,088 41,238 83,095 73,678 36,800 253,899 Notes Here, we present the joint distribution of students by separate groupings of weekly mathematics and language arts instruction time (panel (a)) and number of classes per week (panel (b)). Open in new tab A similar pattern holds for classes per week, the primary source of within‐school instruction time variation. Students who attend three mathematics classes per week are far more likely to attend four or more language‐arts classes than fewer than three. However, students who attend five mathematics classes per week are less likely to attend six or more language‐arts classes than fewer than five. Table 3 documents the existence of adequate within‐school instruction time variation to identify effects and we now describe patterns of test score differences to examine whether the raw test score data are consistent with the belief that longer classes raise achievement. Table 4 reports differences in average standardised test scores (mathematics minus language arts) by the joint distribution of mathematics and language arts instruction time based on both minutes and classes per week. Average test scores are standardised to have a mean of zero and a standard deviation of one for each grade and subject. This Table has the same structure as Table 3 but replaces the conditional distributions with the average standardised score differences. Table 4 Average Mathematics Minus Language Arts Standardised Score Difference by Instructional Time in Mathematics and Language Arts Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . 0–99 0.034 0.103 −0.026 −0.009 0.326 0.139 0.107 100–179 0.027 −0.003 0.051 0.013 0.069 0.001 0.031 180–199 0.006 0.024 −0.008 −0.046 0.006 0.001 −0.001 200–219 0.046 −0.050 −0.034 0.004 0.002 −0.011 0.104 220–239 0.266 0.068 0.002 0.011 0.011 0.040 0.127 240–279 0.000 −0.117 −0.038 −0.082 −0.200 −0.028 0.069 280+ −0.073 −0.146 −0.076 0.009 0.032 0.063 0.037 Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . 0–99 0.034 0.103 −0.026 −0.009 0.326 0.139 0.107 100–179 0.027 −0.003 0.051 0.013 0.069 0.001 0.031 180–199 0.006 0.024 −0.008 −0.046 0.006 0.001 −0.001 200–219 0.046 −0.050 −0.034 0.004 0.002 −0.011 0.104 220–239 0.266 0.068 0.002 0.011 0.011 0.040 0.127 240–279 0.000 −0.117 −0.038 −0.082 −0.200 −0.028 0.069 280+ −0.073 −0.146 −0.076 0.009 0.032 0.063 0.037 Panel (b): number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . 0–2 −0.014 0.038 0.019 0.092 0.177 3 0.021 −0.027 0.035 0.042 0.034 4 −0.040 −0.018 −0.000 −0.011 0.075 5 −0.146 −0.069 −0.102 −0.025 0.032 6+ −0.226 0.032 −0.012 0.008 0.116 Panel (b): number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . 0–2 −0.014 0.038 0.019 0.092 0.177 3 0.021 −0.027 0.035 0.042 0.034 4 −0.040 −0.018 −0.000 −0.011 0.075 5 −0.146 −0.069 −0.102 −0.025 0.032 6+ −0.226 0.032 −0.012 0.008 0.116 Notes Here we subtract language arts scores from mathematics scores and present averages by the same groupings used in Table 3. In cells with positive values, mathematics performance was greater than language arts performance. Open in new tab Table 4 Average Mathematics Minus Language Arts Standardised Score Difference by Instructional Time in Mathematics and Language Arts Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . 0–99 0.034 0.103 −0.026 −0.009 0.326 0.139 0.107 100–179 0.027 −0.003 0.051 0.013 0.069 0.001 0.031 180–199 0.006 0.024 −0.008 −0.046 0.006 0.001 −0.001 200–219 0.046 −0.050 −0.034 0.004 0.002 −0.011 0.104 220–239 0.266 0.068 0.002 0.011 0.011 0.040 0.127 240–279 0.000 −0.117 −0.038 −0.082 −0.200 −0.028 0.069 280+ −0.073 −0.146 −0.076 0.009 0.032 0.063 0.037 Panel (a): minutes per week . . Mathematics . Language arts . 0–99 . 100–179 . 180–199 . 200–219 . 220–239 . 240–279 . 280+ . 0–99 0.034 0.103 −0.026 −0.009 0.326 0.139 0.107 100–179 0.027 −0.003 0.051 0.013 0.069 0.001 0.031 180–199 0.006 0.024 −0.008 −0.046 0.006 0.001 −0.001 200–219 0.046 −0.050 −0.034 0.004 0.002 −0.011 0.104 220–239 0.266 0.068 0.002 0.011 0.011 0.040 0.127 240–279 0.000 −0.117 −0.038 −0.082 −0.200 −0.028 0.069 280+ −0.073 −0.146 −0.076 0.009 0.032 0.063 0.037 Panel (b): number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . 0–2 −0.014 0.038 0.019 0.092 0.177 3 0.021 −0.027 0.035 0.042 0.034 4 −0.040 −0.018 −0.000 −0.011 0.075 5 −0.146 −0.069 −0.102 −0.025 0.032 6+ −0.226 0.032 −0.012 0.008 0.116 Panel (b): number of class periods per week . . Mathematics . Language arts . 0–2 . 3 . 4 . 5 . 6+ . 0–2 −0.014 0.038 0.019 0.092 0.177 3 0.021 −0.027 0.035 0.042 0.034 4 −0.040 −0.018 −0.000 −0.011 0.075 5 −0.146 −0.069 −0.102 −0.025 0.032 6+ −0.226 0.032 −0.012 0.008 0.116 Notes Here we subtract language arts scores from mathematics scores and present averages by the same groupings used in Table 3. In cells with positive values, mathematics performance was greater than language arts performance. Open in new tab A finding that entries above the diagonal (where instruction time for mathematics exceeds instruction time for language arts) tend to be more positive than entries along the diagonal (where there is little or no difference between subjects), which in turn tend to be more positive than entries below the diagonal (where instruction time for language arts exceeds that for mathematics), would be consistent with a positive effect of instruction time. The pattern in Table 4 provides support for such an effect. In the top panel there are only five negative entries above the diagonal, and Table 3 shows that these are mostly the smallest of the above‐diagonal cells. For example, the largest negative entry of −0.046 comes from a cell with only 1% of the students that attend mathematics classes for between 200 and 219 minutes per week. In contrast, there are nine negative entries below the diagonal including the largest entries. The positive entries below the diagonal again tend to fall in very small cells. Finally, entries along the diagonal tend to fall in between those above and those below. 3.2. Instruction Time Effects This subsection reports estimates of the effects of instruction time on achievement for a series of specifications. We begin with results from basic linear models and then present estimates from models with more flexible parameterisations of the relationship between achievement and time. All Tables report co‐efficients from specifications with school‐by‐grade fixed effects and specifications with school‐by‐subject fixed effects as well as robust standard errors clustered by school. The dependent variable in all regressions is the school‐grade‐subject average PISA standardised score. The main sample includes 507,798 school‐grade‐student‐subject observations and roughly half of the main sample comes from schools with both 9th and 10th grade. Therefore, roughly half the sample does not contribute to the identification of the estimates based on the school‐by‐subject fixed effect specification. In the following Tables, estimates from regressions including school‐by‐subject fixed effects will therefore have a sample size of 253,286. Table 5 reports estimates of the relationship between achievement and instruction time, as measured by both weekly hours and the number of weekly class periods for specifications without fixed effects, with school‐by‐grade fixed effects and with school‐by‐subject fixed effects. The two panels share a similar pattern of highly significant estimates that decline by more than 60% following the inclusion of school‐by‐grade fixed effects and another roughly 30% when the school‐by‐subject effects replace the school‐by‐grade effects. Table 5 Estimated Effects of Weekly Hours of Instruction and Class Periods on Achievement . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.087*** 0.031*** 0.023*** (0.007) (0.005) (0.007) Panel (b) Weekly number of class periods 0.088*** 0.034*** 0.025*** (0.008) (0.006) (0.007) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.087*** 0.031*** 0.023*** (0.007) (0.005) (0.007) Panel (b) Weekly number of class periods 0.088*** 0.034*** 0.025*** (0.008) (0.006) (0.007) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 Notes The dependent variable in all regressions is school‐by‐grade‐by‐subject average standardised test score based on the PV1MATH and PV1READ variables. Estimates are insensitive to the choice of plausible value. All regressions also include a country‐by‐grade‐by‐subject effect. The samples are limited to students who have both mathematics and language arts components in their 2009 PISA test booklet and valid class‐time information for both subjects. The main sample consists of 507,798 observations for 253,899 students from 16,310 schools. The school‐by‐subject fixed effect estimates require two grades within a school, a restriction that reduces the sample to 253,286 observations from 7,374 schools. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table 5 Estimated Effects of Weekly Hours of Instruction and Class Periods on Achievement . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.087*** 0.031*** 0.023*** (0.007) (0.005) (0.007) Panel (b) Weekly number of class periods 0.088*** 0.034*** 0.025*** (0.008) (0.006) (0.007) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.087*** 0.031*** 0.023*** (0.007) (0.005) (0.007) Panel (b) Weekly number of class periods 0.088*** 0.034*** 0.025*** (0.008) (0.006) (0.007) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 Notes The dependent variable in all regressions is school‐by‐grade‐by‐subject average standardised test score based on the PV1MATH and PV1READ variables. Estimates are insensitive to the choice of plausible value. All regressions also include a country‐by‐grade‐by‐subject effect. The samples are limited to students who have both mathematics and language arts components in their 2009 PISA test booklet and valid class‐time information for both subjects. The main sample consists of 507,798 observations for 253,899 students from 16,310 schools. The school‐by‐subject fixed effect estimates require two grades within a school, a restriction that reduces the sample to 253,286 observations from 7,374 schools. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab The smaller estimates from the specifications with school‐by‐subject fixed effects are consistent with the specification issues raised in the previous subsection. Factors that could contribute to the observed pattern include subject‐specific skills that are positively related to instruction time and not accounted for in the specifications with school‐by‐grade fixed effects, correlation between instruction‐time differences in the current and prior grades that inflate estimates from the school‐by‐grade fixed effect specifications, attenuation bias in the specifications with school‐by‐subject fixed effects introduced by violation of the assumption that 9th grade instruction time has no effect on 10th grade achievement, or larger measurement error‐induced attenuation bias in the models with school‐by‐subject fixed effects. Although little direct evidence exists on subject‐specific skills, available information provides mixed findings on the likelihood that the other previously described factors attenuate the school‐by‐subject fixed effect estimates. First, the R2 values reported in Table A3 show that the residual variation used to identify the school‐by‐subject fixed effect estimates is roughly equal to that used to identify the school‐by‐grade fixed effect estimates; roughly 10% of the instruction time variance remains following the removal of school‐by‐subject or school‐by‐grade fixed effects. Note that consistent with the larger standard errors, the sample size is much smaller in the school‐by‐subject fixed effects regressions. Second, available evidence does support the belief that the effects of instruction time in prior years contribute to the observed pattern. Jacob et al. (2008), Kane and Staiger (2008) and Rothstein (2010) find that at least a portion of the knowledge acquired in a grade persists into the future. In addition, the correlation between school average instruction‐time differences in 9th and 10th grades is 0.41 in the PISA data. Such persistence in effects and correlation in instruction time differences would lead the effects of instruction time in prior years to inflate the school‐by‐grade fixed effect estimates and to attenuate the school‐by‐subject fixed effect estimates as discussed in Section 2. Note that the instruction‐time co‐efficient remains positive in the fully saturated specification with both school‐by‐grade and school‐by‐subject fixed effects (not reported), though the estimate is much smaller and quite imprecise. Unfortunately, the final column in Table A3 shows that only approximately 2% of the variation in our instruction time measures remains in specifications that include both the school‐by‐grade and school‐by‐subject fixed effects. In Figure 2, we present additional evidence on the relationship between instruction time and achievement. Each Figure plots the mean residuals from two separate regressions where instruction time and achievement, respectively, are regressed on country‐by‐school‐by‐grade effects and school‐by‐grade (top panel) or school‐by‐subject (bottom panel) fixed effects. In all the Figures, the relationship between study time and achievement is positive and strong, though as expected the slope is less steep in regressions with school‐by‐subject fixed effects. Fig. 2. Open in new tabDownload slide Instruction‐time Residuals Plotted Against Standardised Achievement Residuals. (a) School‐by‐grade fixed effects. (b) School‐by‐subject fixed effects Notes. Similar to Chetty et al. (2011), this Figure presents the relationships between achievement and instruction time non‐parametrically. To plot each Figure, we separately regress both instruction time and standardised test scores on country‐by‐grade‐by‐subject fixed effects as well as school‐by‐grade or school‐by‐subject fixed effects. We then calculate residuals from the instruction time and standardised test score regressions, group them based on the instruction time residuals and plot the grouped residuals against each other. Fig. 2. Open in new tabDownload slide Instruction‐time Residuals Plotted Against Standardised Achievement Residuals. (a) School‐by‐grade fixed effects. (b) School‐by‐subject fixed effects Notes. Similar to Chetty et al. (2011), this Figure presents the relationships between achievement and instruction time non‐parametrically. To plot each Figure, we separately regress both instruction time and standardised test scores on country‐by‐grade‐by‐subject fixed effects as well as school‐by‐grade or school‐by‐subject fixed effects. We then calculate residuals from the instruction time and standardised test score regressions, group them based on the instruction time residuals and plot the grouped residuals against each other. We now investigate the possibility of diminishing returns to additional hours. Table 6 reports results from the three specifications with weekly hours entered as a quadratic and the results in both fixed effect specifications strongly support the hypothesis of diminishing returns. Importantly, the marginal return to an additional hour diminishes quite slowly, remaining positive up to around the 6th or 7th hour in both specifications, a number that exceeds the 95th percentile in the instruction‐time distribution. Table 6 Estimated Effects of Weekly Instructional Hours on Achievement from Quadratic Specifications . (1) . (2) . (3) . Weekly hours of instruction 0.3525*** 0.1003*** 0.0833*** (0.0261) (0.0157) (0.0180) Squared weekly hours of instruction −0.0290*** −0.0077*** −0.0061*** (0.0029) (0.0017) (0.0017) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 . (1) . (2) . (3) . Weekly hours of instruction 0.3525*** 0.1003*** 0.0833*** (0.0261) (0.0157) (0.0180) Squared weekly hours of instruction −0.0290*** −0.0077*** −0.0061*** (0.0029) (0.0017) (0.0017) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table 6 Estimated Effects of Weekly Instructional Hours on Achievement from Quadratic Specifications . (1) . (2) . (3) . Weekly hours of instruction 0.3525*** 0.1003*** 0.0833*** (0.0261) (0.0157) (0.0180) Squared weekly hours of instruction −0.0290*** −0.0077*** −0.0061*** (0.0029) (0.0017) (0.0017) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 . (1) . (2) . (3) . Weekly hours of instruction 0.3525*** 0.1003*** 0.0833*** (0.0261) (0.0157) (0.0180) Squared weekly hours of instruction −0.0290*** −0.0077*** −0.0061*** (0.0029) (0.0017) (0.0017) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 507,798 507,798 253,286 No. of schools 16,310 16,310 7,374 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table 7 reports results from fixed‐effect specifications that group weekly minutes and classes based on shares of students in five instruction time categories. Although both fixed‐effect specifications produce a generally positive relationship between achievement and minutes, there are some inconsistencies. For example, in column (2) with school‐by‐subject fixed effects, the estimate for the highest category in the class period specification is negative. However, this category is likely to contain substantial error in measurement. Attending greater than six classes per week may reflect efforts to remediate low performance or may result from reporting error and a number of observations that report weekly minutes above 280 may also suffer from reporting error. Table 7 Estimated Effects of Weekly Instructional Minutes and Classes Per Week on Achievement from Specifications with Instructional Time Categories . (1) . (2) . Panel (a): average shares of students in each minute per week category (relative to 200–219) 0–99 −0.115*** −0.277*** (0.035) (0.048) 100–179 −0.098*** −0.053** (0.018) (0.026) 180–199 −0.005 −0.030 (0.021) (0.033) 220–239 −0.045* 0.035 (0.023) (0.035) 240–279 0.080*** 0.051* (0.017) (0.030) 280+ 0.010 0.035 (0.025) (0.034) Panel (b): average shares in each weekly classes category (relative to 4) 0–2 −0.163*** −0.243*** (0.022) (0.034) 3 −0.071*** −0.045** (0.013) (0.019) 5 0.045*** 0.017 (0.012) (0.022) 6–10 0.053*** −0.013 (0.019) (0.029) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 . (1) . (2) . Panel (a): average shares of students in each minute per week category (relative to 200–219) 0–99 −0.115*** −0.277*** (0.035) (0.048) 100–179 −0.098*** −0.053** (0.018) (0.026) 180–199 −0.005 −0.030 (0.021) (0.033) 220–239 −0.045* 0.035 (0.023) (0.035) 240–279 0.080*** 0.051* (0.017) (0.030) 280+ 0.010 0.035 (0.025) (0.034) Panel (b): average shares in each weekly classes category (relative to 4) 0–2 −0.163*** −0.243*** (0.022) (0.034) 3 −0.071*** −0.045** (0.013) (0.019) 5 0.045*** 0.017 (0.012) (0.022) 6–10 0.053*** −0.013 (0.019) (0.029) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table 7 Estimated Effects of Weekly Instructional Minutes and Classes Per Week on Achievement from Specifications with Instructional Time Categories . (1) . (2) . Panel (a): average shares of students in each minute per week category (relative to 200–219) 0–99 −0.115*** −0.277*** (0.035) (0.048) 100–179 −0.098*** −0.053** (0.018) (0.026) 180–199 −0.005 −0.030 (0.021) (0.033) 220–239 −0.045* 0.035 (0.023) (0.035) 240–279 0.080*** 0.051* (0.017) (0.030) 280+ 0.010 0.035 (0.025) (0.034) Panel (b): average shares in each weekly classes category (relative to 4) 0–2 −0.163*** −0.243*** (0.022) (0.034) 3 −0.071*** −0.045** (0.013) (0.019) 5 0.045*** 0.017 (0.012) (0.022) 6–10 0.053*** −0.013 (0.019) (0.029) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 . (1) . (2) . Panel (a): average shares of students in each minute per week category (relative to 200–219) 0–99 −0.115*** −0.277*** (0.035) (0.048) 100–179 −0.098*** −0.053** (0.018) (0.026) 180–199 −0.005 −0.030 (0.021) (0.033) 220–239 −0.045* 0.035 (0.023) (0.035) 240–279 0.080*** 0.051* (0.017) (0.030) 280+ 0.010 0.035 (0.025) (0.034) Panel (b): average shares in each weekly classes category (relative to 4) 0–2 −0.163*** −0.243*** (0.022) (0.034) 3 −0.071*** −0.045** (0.013) (0.019) 5 0.045*** 0.017 (0.012) (0.022) 6–10 0.053*** −0.013 (0.019) (0.029) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab 3.3. Heterogeneity by Classroom Environment The notion that the return to additional time depends crucially on the quality of the learning environment fits with the emphasis on the role of disruption in education production presented in Lazear (2001) and more general consideration of the quality of teachers and schools. In this subsection, we investigate the possibility of variation in the return to instruction time by reported student and teacher behaviours. Because the classroom quality index does not vary within schools, its direct effect on achievement cannot be identified. However, we can interact the quality measure with the instruction time variables in order to investigate heterogeneity in the returns to instruction time along this dimension. We re‐scale the classroom quality index measure to have a mean of zero and standard deviation of one across all countries and schools. The results in Table 8 provide modest support for the hypothesis that the return to additional instruction time increases with the quality of the classroom environment. In both the school‐by‐grade and school‐by‐subject fixed effect specifications, the coefficients on the classroom environment interactions are positive, though small and not significant at the 10% level. The interaction‐term co‐efficient magnitude of 0.007 in the school‐by‐grade fixed effect specification suggests that a one standard deviation improvement in classroom environment raises the return to an additional hour of class time by <0.01 standard deviations. The fact that these survey questions provide noisy information about the quality of the classroom environment raises the possibility of attenuation bias. Table 8 Estimated Effects of Weekly Instructional Hours and Class Periods on Achievement, by Classroom Quality . (1) . (2) . Panel (a) Weekly hours of instruction 0.0305*** 0.0233*** (0.0053) (0.0067) Weekly hours × classroom quality 0.0067 0.0031 (0.0050) (0.0065) Panel (b) Weekly number of class periods 0.0334*** 0.0252*** (0.0055) (0.0068) Weekly classes × classroom quality 0.0057 0.0092 (0.0048) (0.0062) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 . (1) . (2) . Panel (a) Weekly hours of instruction 0.0305*** 0.0233*** (0.0053) (0.0067) Weekly hours × classroom quality 0.0067 0.0031 (0.0050) (0.0065) Panel (b) Weekly number of class periods 0.0334*** 0.0252*** (0.0055) (0.0068) Weekly classes × classroom quality 0.0057 0.0092 (0.0048) (0.0062) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 Notes Because the classroom quality variable does not vary within a school, its direct effect cannot be identified in the fixed‐effect models. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table 8 Estimated Effects of Weekly Instructional Hours and Class Periods on Achievement, by Classroom Quality . (1) . (2) . Panel (a) Weekly hours of instruction 0.0305*** 0.0233*** (0.0053) (0.0067) Weekly hours × classroom quality 0.0067 0.0031 (0.0050) (0.0065) Panel (b) Weekly number of class periods 0.0334*** 0.0252*** (0.0055) (0.0068) Weekly classes × classroom quality 0.0057 0.0092 (0.0048) (0.0062) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 . (1) . (2) . Panel (a) Weekly hours of instruction 0.0305*** 0.0233*** (0.0053) (0.0067) Weekly hours × classroom quality 0.0067 0.0031 (0.0050) (0.0065) Panel (b) Weekly number of class periods 0.0334*** 0.0252*** (0.0055) (0.0068) Weekly classes × classroom quality 0.0057 0.0092 (0.0048) (0.0062) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 507,798 253,286 No. of schools 16,310 7,374 Notes Because the classroom quality variable does not vary within a school, its direct effect cannot be identified in the fixed‐effect models. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab In order to increase the precision of the estimates, we add science test scores to the regressions and limit the sample to students who take at least two of the three tests. This does introduce the possibility of attenuation bias in the school by grade fixed effect estimates if there are spillovers between science and the other subjects, and Table A4 shows a substantial decline in coefficient magnitudes for these specifications despite an increase in the magnitude of the school by subject fixed effect estimates. Table A5 shows that the interaction‐term coefficients become significant at the 1% level in the weekly hours and classes specifications with school by grade fixed effects, though the magnitudes of the estimates remain quite small. In contrast, the estimates remain insignificant in the school‐by‐subject fixed effect specifications but this is not surprising, given that that an additional school‐by‐subject fixed effect at each school accompanies the addition of science tests. The model of education production in Lazear (2001) raises the possibility of a nonlinear relationship between the level of disruption and learning but the categorical structure of the variables used to generate the classroom quality index does not suggest a particular functional form. Therefore, we estimate a more flexible specification that includes interactions with indicators between instruction time and quartiles of the classroom environment distributions. The results in Table 9 show a monotonically increasing return to additional instruction time as the quality of the classroom environment increases in the school‐by‐grade fixed effect specification. More specifically, the estimated benefit of additional class time for students in schools in the top half of the classroom quality distribution is significant and more than twice as large as the benefit for students attending schools in the bottom half of the distribution: the coefficients for the 3rd and 4th quartile interactions exceed 0.02. Perhaps not surprisingly, the interaction terms in the school‐by‐subject specifications are small and not precisely estimated. Table 9 Estimated Effects of Instructional Time on Achievement, by Quartile of Classroom Quality . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.017* 0.018 0.020** 0.008 (0.010) (0.012) (0.009) (0.013) Instruction time × 2nd quality quartile 0.0004 0.014 0.004 0.032* (0.012) (0.018) (0.011) (0.018) Instruction time × 3rd quality quartile 0.024** −0.001 0.023** 0.006 (0.012) (0.018) (0.012) (0.018) Instruction time × 4th quality quartile 0.027** 0.008 0.027** 0.028 (0.013) (0.018) (0.013) (0.017) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 507,798 253,286 507,798 253,286 No. of schools 16,310 7,374 16,310 7,374 . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.017* 0.018 0.020** 0.008 (0.010) (0.012) (0.009) (0.013) Instruction time × 2nd quality quartile 0.0004 0.014 0.004 0.032* (0.012) (0.018) (0.011) (0.018) Instruction time × 3rd quality quartile 0.024** −0.001 0.023** 0.006 (0.012) (0.018) (0.012) (0.018) Instruction time × 4th quality quartile 0.027** 0.008 0.027** 0.028 (0.013) (0.018) (0.013) (0.017) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 507,798 253,286 507,798 253,286 No. of schools 16,310 7,374 16,310 7,374 Notes Because the classroom quality variable does not vary within a school, its direct effect cannot be identified in the fixed‐effect models. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table 9 Estimated Effects of Instructional Time on Achievement, by Quartile of Classroom Quality . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.017* 0.018 0.020** 0.008 (0.010) (0.012) (0.009) (0.013) Instruction time × 2nd quality quartile 0.0004 0.014 0.004 0.032* (0.012) (0.018) (0.011) (0.018) Instruction time × 3rd quality quartile 0.024** −0.001 0.023** 0.006 (0.012) (0.018) (0.012) (0.018) Instruction time × 4th quality quartile 0.027** 0.008 0.027** 0.028 (0.013) (0.018) (0.013) (0.017) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 507,798 253,286 507,798 253,286 No. of schools 16,310 7,374 16,310 7,374 . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.017* 0.018 0.020** 0.008 (0.010) (0.012) (0.009) (0.013) Instruction time × 2nd quality quartile 0.0004 0.014 0.004 0.032* (0.012) (0.018) (0.011) (0.018) Instruction time × 3rd quality quartile 0.024** −0.001 0.023** 0.006 (0.012) (0.018) (0.012) (0.018) Instruction time × 4th quality quartile 0.027** 0.008 0.027** 0.028 (0.013) (0.018) (0.013) (0.017) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 507,798 253,286 507,798 253,286 No. of schools 16,310 7,374 16,310 7,374 Notes Because the classroom quality variable does not vary within a school, its direct effect cannot be identified in the fixed‐effect models. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab After adding science tests in Table A6, we find a very similar, monotonically increasing pattern of estimates. Similar to the linear interactions with the classroom quality scale, the estimates including science tests are more significant than those excluding science tests. Again, none of the school‐by‐subject fixed effect coefficients are significant at the 5% level. 4. Conclusions and Policy Implications Instruction time has become an important issue in school reform discussions, as many advocate for increases in time devoted to mathematics and language arts instruction. A shortage of compelling empirical evidence has hindered the decision‐making process, and a primary goal of this article is to build on the contributions of recent work and provide additional information. The analysis uses panel data methods made possible by the richness of the PISA data and the fixed effects models accounts for student and school heterogeneity, including differences by subject in some specifications. The empirical analysis provides strong evidence in favour of the notion that additional time raises achievement. Given the character of the deficiencies of the two fixed effects models, the results suggest that the effect is positive and modest in magnitude. Although instruction time is found to exhibit diminishing returns, the rate of decrease appears to be quite gradual. Perhaps the most important finding, despite the lack of precision in some specifications, is that the benefit of additional instruction time appears to vary with the quality of the classroom environment. Specifically, the results show that schools with low‐quality classroom environments likely realise a much smaller benefit from additional instruction time. Thus, there would appear to be substantial complementarities between policies that improve the classroom environment such as the strict discipline demanded in KIPP academy schools and those that expand instruction time. Additional work that focuses on the interrelationship between instructional quality, school climate and instruction time could provide stronger and richer evidence on the character of the return to expanded time. Such an analysis would require better measures of the quality of teaching, curriculum, disruption and other aspects of the classroom environment. A Appendix Table A1 Descriptive Statistics . Mathematics . Language arts . Mean . SD . Mean . SD . Standardised test score 0.000 1.000 0.000 1.000 Length in hours of an average class 0.857 0.230 0.852 0.224 Weekly number of class periods 4.368 1.417 4.403 1.441 Weekly hours of instruction 3.688 1.437 3.688 1.404 Standardised classroom quality 0.000 1.000 0.000 1.000 Sample size 253,899 No. of schools 16,310 . Mathematics . Language arts . Mean . SD . Mean . SD . Standardised test score 0.000 1.000 0.000 1.000 Length in hours of an average class 0.857 0.230 0.852 0.224 Weekly number of class periods 4.368 1.417 4.403 1.441 Weekly hours of instruction 3.688 1.437 3.688 1.404 Standardised classroom quality 0.000 1.000 0.000 1.000 Sample size 253,899 No. of schools 16,310 Notes Test scores and classroom quality are standardised by grade and subject to having a mean of zero and standard deviation of one. The sample of 253,899 is based on the number of students and corresponds to Tables 3 and 4. The main analysis sample is twice the student‐level sample as the data are reshaped to vary country‐school‐student‐subject. Open in new tab Table A1 Descriptive Statistics . Mathematics . Language arts . Mean . SD . Mean . SD . Standardised test score 0.000 1.000 0.000 1.000 Length in hours of an average class 0.857 0.230 0.852 0.224 Weekly number of class periods 4.368 1.417 4.403 1.441 Weekly hours of instruction 3.688 1.437 3.688 1.404 Standardised classroom quality 0.000 1.000 0.000 1.000 Sample size 253,899 No. of schools 16,310 . Mathematics . Language arts . Mean . SD . Mean . SD . Standardised test score 0.000 1.000 0.000 1.000 Length in hours of an average class 0.857 0.230 0.852 0.224 Weekly number of class periods 4.368 1.417 4.403 1.441 Weekly hours of instruction 3.688 1.437 3.688 1.404 Standardised classroom quality 0.000 1.000 0.000 1.000 Sample size 253,899 No. of schools 16,310 Notes Test scores and classroom quality are standardised by grade and subject to having a mean of zero and standard deviation of one. The sample of 253,899 is based on the number of students and corresponds to Tables 3 and 4. The main analysis sample is twice the student‐level sample as the data are reshaped to vary country‐school‐student‐subject. Open in new tab Table A2 Estimated Effects of Weekly Hours of Instruction and Class Periods on Achievement Controlling for Out‐of‐school Study‐time . Weekly hours of instruction . Weekly number of class periods . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Instruction time 0.033*** 0.034*** 0.021*** 0.021*** 0.035*** 0.036*** 0.023*** 0.023*** (0.005) (0.005) (0.007) (0.007) (0.006) (0.006) (0.007) (0.007) Out‐of‐school lessons (rel. to 2 to <4 hours) None 0.073*** 0.164*** 0.074*** 0.165*** (0.018) (0.022) (0.018) (0.022) <2 hours per week −0.026 −0.057** −0.024 −0.056** (0.019) (0.026) (0.019) (0.026) 4 to <6 hours per week 0.021 −0.048 0.019 −0.046 (0.023) (0.030) (0.023) (0.030) 6+ hours per week 0.027 −0.102*** 0.022 −0.101*** (0.030) (0.038) (0.031) (0.038) School‐by‐grade fixed effect Y Y N N Y Y N N School‐by‐subject fixed effect N N Y Y N N Y Y Sample size 504,393 504,393 250,929 250,929 504,393 504,393 250,929 250,929 No. of schools 16,140 16,140 7,367 7,367 16,140 16,140 7,367 7,367 . Weekly hours of instruction . Weekly number of class periods . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Instruction time 0.033*** 0.034*** 0.021*** 0.021*** 0.035*** 0.036*** 0.023*** 0.023*** (0.005) (0.005) (0.007) (0.007) (0.006) (0.006) (0.007) (0.007) Out‐of‐school lessons (rel. to 2 to <4 hours) None 0.073*** 0.164*** 0.074*** 0.165*** (0.018) (0.022) (0.018) (0.022) <2 hours per week −0.026 −0.057** −0.024 −0.056** (0.019) (0.026) (0.019) (0.026) 4 to <6 hours per week 0.021 −0.048 0.019 −0.046 (0.023) (0.030) (0.023) (0.030) 6+ hours per week 0.027 −0.102*** 0.022 −0.101*** (0.030) (0.038) (0.031) (0.038) School‐by‐grade fixed effect Y Y N N Y Y N N School‐by‐subject fixed effect N N Y Y N N Y Y Sample size 504,393 504,393 250,929 250,929 504,393 504,393 250,929 250,929 No. of schools 16,140 16,140 7,367 7,367 16,140 16,140 7,367 7,367 Notes The out‐of‐school study variables represent the share of students in each category by, school, grade and subject. There are fewer observations in this Table because we now exclude observations missing out‐of‐school study‐time information. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table A2 Estimated Effects of Weekly Hours of Instruction and Class Periods on Achievement Controlling for Out‐of‐school Study‐time . Weekly hours of instruction . Weekly number of class periods . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Instruction time 0.033*** 0.034*** 0.021*** 0.021*** 0.035*** 0.036*** 0.023*** 0.023*** (0.005) (0.005) (0.007) (0.007) (0.006) (0.006) (0.007) (0.007) Out‐of‐school lessons (rel. to 2 to <4 hours) None 0.073*** 0.164*** 0.074*** 0.165*** (0.018) (0.022) (0.018) (0.022) <2 hours per week −0.026 −0.057** −0.024 −0.056** (0.019) (0.026) (0.019) (0.026) 4 to <6 hours per week 0.021 −0.048 0.019 −0.046 (0.023) (0.030) (0.023) (0.030) 6+ hours per week 0.027 −0.102*** 0.022 −0.101*** (0.030) (0.038) (0.031) (0.038) School‐by‐grade fixed effect Y Y N N Y Y N N School‐by‐subject fixed effect N N Y Y N N Y Y Sample size 504,393 504,393 250,929 250,929 504,393 504,393 250,929 250,929 No. of schools 16,140 16,140 7,367 7,367 16,140 16,140 7,367 7,367 . Weekly hours of instruction . Weekly number of class periods . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Instruction time 0.033*** 0.034*** 0.021*** 0.021*** 0.035*** 0.036*** 0.023*** 0.023*** (0.005) (0.005) (0.007) (0.007) (0.006) (0.006) (0.007) (0.007) Out‐of‐school lessons (rel. to 2 to <4 hours) None 0.073*** 0.164*** 0.074*** 0.165*** (0.018) (0.022) (0.018) (0.022) <2 hours per week −0.026 −0.057** −0.024 −0.056** (0.019) (0.026) (0.019) (0.026) 4 to <6 hours per week 0.021 −0.048 0.019 −0.046 (0.023) (0.030) (0.023) (0.030) 6+ hours per week 0.027 −0.102*** 0.022 −0.101*** (0.030) (0.038) (0.031) (0.038) School‐by‐grade fixed effect Y Y N N Y Y N N School‐by‐subject fixed effect N N Y Y N N Y Y Sample size 504,393 504,393 250,929 250,929 504,393 504,393 250,929 250,929 No. of schools 16,140 16,140 7,367 7,367 16,140 16,140 7,367 7,367 Notes The out‐of‐school study variables represent the share of students in each category by, school, grade and subject. There are fewer observations in this Table because we now exclude observations missing out‐of‐school study‐time information. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table A3 Percent of Variation in Instruction Time Measures Explained by the Fixed Effects . (1) . (2) . (3) . (4) . (5) . Weekly hours of instruction 0% 52% 90% 89% 97% Weekly number of class periods 0% 57% 91% 92% 98% Country‐by‐grade‐by‐subject effects N Y Y Y Y School‐by‐grade fixed effects N N Y N Y School‐by‐subject fixed effects N N N Y Y . (1) . (2) . (3) . (4) . (5) . Weekly hours of instruction 0% 52% 90% 89% 97% Weekly number of class periods 0% 57% 91% 92% 98% Country‐by‐grade‐by‐subject effects N Y Y Y Y School‐by‐grade fixed effects N N Y N Y School‐by‐subject fixed effects N N N Y Y Notes Average weekly hours of instruction and average weekly number of class periods are used as dependent variables. The independent variables used in each regression are indicated in the Table. The percentage indicates the R2 from each regression. Regressions in columns 1, 2 and 3 are based on a sample of 507,798 observations. Regressions with school‐by‐subject fixed effects (columns 4 and 5) require two grades within a school, a restriction that lowers the sample to 253,286 observations. Open in new tab Table A3 Percent of Variation in Instruction Time Measures Explained by the Fixed Effects . (1) . (2) . (3) . (4) . (5) . Weekly hours of instruction 0% 52% 90% 89% 97% Weekly number of class periods 0% 57% 91% 92% 98% Country‐by‐grade‐by‐subject effects N Y Y Y Y School‐by‐grade fixed effects N N Y N Y School‐by‐subject fixed effects N N N Y Y . (1) . (2) . (3) . (4) . (5) . Weekly hours of instruction 0% 52% 90% 89% 97% Weekly number of class periods 0% 57% 91% 92% 98% Country‐by‐grade‐by‐subject effects N Y Y Y Y School‐by‐grade fixed effects N N Y N Y School‐by‐subject fixed effects N N N Y Y Notes Average weekly hours of instruction and average weekly number of class periods are used as dependent variables. The independent variables used in each regression are indicated in the Table. The percentage indicates the R2 from each regression. Regressions in columns 1, 2 and 3 are based on a sample of 507,798 observations. Regressions with school‐by‐subject fixed effects (columns 4 and 5) require two grades within a school, a restriction that lowers the sample to 253,286 observations. Open in new tab Table A4 Estimated Effects of Weekly Hours of Instruction and Class Periods on Achievement in Mathematics, Science and Language Arts . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.110*** 0.011*** 0.035*** (0.005) (0.002) (0.005) Panel (b) Weekly number of class periods 0.104*** 0.011*** 0.038*** (0.005) (0.002) (0.005) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 931,755 931,755 466,812 No. of schools 16,317 16,317 7,565 . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.110*** 0.011*** 0.035*** (0.005) (0.002) (0.005) Panel (b) Weekly number of class periods 0.104*** 0.011*** 0.038*** (0.005) (0.002) (0.005) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 931,755 931,755 466,812 No. of schools 16,317 16,317 7,565 Notes The dependent variable is now school‐by‐grade‐by‐subject average standardised test scores based on PV1MATH, PV1SCIE and PV1READ. We now drop any student without at least two subjects in their test booklet as well as any student not reporting class time information for each subject. All regressions also include a country‐by‐grade‐by‐subject fixed effect. The main sample consists of 931,755 observations from 16,317 schools. The school‐by‐subject fixed effect estimates require two grades within a school, a restriction that leaves 466,812 observations. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table A4 Estimated Effects of Weekly Hours of Instruction and Class Periods on Achievement in Mathematics, Science and Language Arts . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.110*** 0.011*** 0.035*** (0.005) (0.002) (0.005) Panel (b) Weekly number of class periods 0.104*** 0.011*** 0.038*** (0.005) (0.002) (0.005) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 931,755 931,755 466,812 No. of schools 16,317 16,317 7,565 . (1) . (2) . (3) . Panel (a) Weekly hours of instruction 0.110*** 0.011*** 0.035*** (0.005) (0.002) (0.005) Panel (b) Weekly number of class periods 0.104*** 0.011*** 0.038*** (0.005) (0.002) (0.005) School‐by‐grade fixed effect N Y N School‐by‐subject fixed effect N N Y Sample size 931,755 931,755 466,812 No. of schools 16,317 16,317 7,565 Notes The dependent variable is now school‐by‐grade‐by‐subject average standardised test scores based on PV1MATH, PV1SCIE and PV1READ. We now drop any student without at least two subjects in their test booklet as well as any student not reporting class time information for each subject. All regressions also include a country‐by‐grade‐by‐subject fixed effect. The main sample consists of 931,755 observations from 16,317 schools. The school‐by‐subject fixed effect estimates require two grades within a school, a restriction that leaves 466,812 observations. Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table A5 Estimated Effects of Weekly Instructional Hours and Class Periods by Classroom Quality in Mathematics, Science, and Language Arts . (1) . (2) . Panel (a) Weekly hours of instruction 0.0109*** 0.0348*** (0.0021) (0.0050) Weekly hours × classroom quality 0.0055*** 0.0025 (0.0017) (0.0045) Panel (b) Weekly number of class periods 0.0101*** 0.0383*** (0.0019) (0.0046) Weekly classes × classroom quality 0.0044*** 0.0052 (0.0014) (0.0038) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 931,755 466,812 No. of schools 16,317 7,565 . (1) . (2) . Panel (a) Weekly hours of instruction 0.0109*** 0.0348*** (0.0021) (0.0050) Weekly hours × classroom quality 0.0055*** 0.0025 (0.0017) (0.0045) Panel (b) Weekly number of class periods 0.0101*** 0.0383*** (0.0019) (0.0046) Weekly classes × classroom quality 0.0044*** 0.0052 (0.0014) (0.0038) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 931,755 466,812 No. of schools 16,317 7,565 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table A5 Estimated Effects of Weekly Instructional Hours and Class Periods by Classroom Quality in Mathematics, Science, and Language Arts . (1) . (2) . Panel (a) Weekly hours of instruction 0.0109*** 0.0348*** (0.0021) (0.0050) Weekly hours × classroom quality 0.0055*** 0.0025 (0.0017) (0.0045) Panel (b) Weekly number of class periods 0.0101*** 0.0383*** (0.0019) (0.0046) Weekly classes × classroom quality 0.0044*** 0.0052 (0.0014) (0.0038) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 931,755 466,812 No. of schools 16,317 7,565 . (1) . (2) . Panel (a) Weekly hours of instruction 0.0109*** 0.0348*** (0.0021) (0.0050) Weekly hours × classroom quality 0.0055*** 0.0025 (0.0017) (0.0045) Panel (b) Weekly number of class periods 0.0101*** 0.0383*** (0.0019) (0.0046) Weekly classes × classroom quality 0.0044*** 0.0052 (0.0014) (0.0038) School‐by‐grade fixed effect Y N School‐by‐subject fixed effect N Y Sample size 931,755 466,812 No. of schools 16,317 7,565 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table A6 Estimated Effects of Instructional Time by Quartile of Classroom Quality in Mathematics, Science and Language Arts . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.001 0.026*** 0.002 0.026*** (0.004) (0.009) (0.003) (0.008) Instruction time × 2nd quality quartile 0.006 0.019 0.006 0.020* (0.004) (0.013) (0.004) (0.012) Instruction time × 3rd quality quartile 0.013*** 0.006 0.011*** 0.010 (0.005) (0.013) (0.004) (0.011) Instruction time × 4th quality quartile 0.019*** 0.009 0.016*** 0.017 (0.004) (0.012) (0.004) (0.011) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 931,755 466,812 931,755 466,812 No. of schools 16,317 7,565 16,317 7,565 . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.001 0.026*** 0.002 0.026*** (0.004) (0.009) (0.003) (0.008) Instruction time × 2nd quality quartile 0.006 0.019 0.006 0.020* (0.004) (0.013) (0.004) (0.012) Instruction time × 3rd quality quartile 0.013*** 0.006 0.011*** 0.010 (0.005) (0.013) (0.004) (0.011) Instruction time × 4th quality quartile 0.019*** 0.009 0.016*** 0.017 (0.004) (0.012) (0.004) (0.011) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 931,755 466,812 931,755 466,812 No. of schools 16,317 7,565 16,317 7,565 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Table A6 Estimated Effects of Instructional Time by Quartile of Classroom Quality in Mathematics, Science and Language Arts . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.001 0.026*** 0.002 0.026*** (0.004) (0.009) (0.003) (0.008) Instruction time × 2nd quality quartile 0.006 0.019 0.006 0.020* (0.004) (0.013) (0.004) (0.012) Instruction time × 3rd quality quartile 0.013*** 0.006 0.011*** 0.010 (0.005) (0.013) (0.004) (0.011) Instruction time × 4th quality quartile 0.019*** 0.009 0.016*** 0.017 (0.004) (0.012) (0.004) (0.011) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 931,755 466,812 931,755 466,812 No. of schools 16,317 7,565 16,317 7,565 . Weekly instructional hours . Weekly number of class periods . (1) . (2) . (3) . (4) . Instruction time 0.001 0.026*** 0.002 0.026*** (0.004) (0.009) (0.003) (0.008) Instruction time × 2nd quality quartile 0.006 0.019 0.006 0.020* (0.004) (0.013) (0.004) (0.012) Instruction time × 3rd quality quartile 0.013*** 0.006 0.011*** 0.010 (0.005) (0.013) (0.004) (0.011) Instruction time × 4th quality quartile 0.019*** 0.009 0.016*** 0.017 (0.004) (0.012) (0.004) (0.011) School‐by‐grade fixed effect Y N Y N School‐by‐subject fixed effect N Y N Y Sample size 931,755 466,812 931,755 466,812 No. of schools 16,317 7,565 16,317 7,565 Notes Robust standard errors clustered by school are in parentheses. ***Significant at the 1% level; **significant at the 5% level; *significant at the 10% level. Open in new tab Footnotes 1 " See Farbman (2012) for more on the potential benefits of additional time. 2 " In a recent paper, Angrist et al. (2010) attempt to isolate the contributions of various factors to the educational success of KIPP students. 3 " Recent work includes Gijselaers and Schmidt (1995), Coates (2003), Wiermann (2005), Marcotte (2007), Marcotte and Hemelt (2008), Bellei (2009), Lavy (2010), Fryer (2011), Mandel and Süssmuth (2011), Lavy (2012) and Kuehn and Landeras (2012). Lavy (2010) emphasises the identification problem and adopts an empirical approach that provides a foundation for our work in this article. Nomi and Allensworth (2013) use regression discontinuity design to identify the effects of doubling algebra class time but differences in student composition, teacher supports, and other factors between students in the single and double class algebra programmes prevent the identification of the instruction‐time effect. 4 " Each student is assigned five achievement measures for each subject called plausible values. To estimate regressions using plausible values, one must estimate separate regressions with each of the five plausible values and then average across the estimates. See Adams and Wu (2002) for a detailed description of plausible values. Practically speaking, however, estimates from larger samples will be very similar regardless of which plausible value is used. Here, we present estimates based on the first plausible value through the estimates are insensitive to choice of plausible value. Upon request, Tables are available from the authors. 5 " We test the sensitivity of our estimates to different restrictions on weekly number of classes and average class lengths. In general, the estimates are insensitive to how we restrict the data. Upon request, Tables are available from the authors. 6 " A recent working paper by Borghans and Schils (2012) discusses in more detail the variation in PISA test booklets in the 2006 data. 7 " The variable ‘bookid’ denotes which subjects are contained in each student’s test booklet. For the analyses based on mathematics and language arts, we drop those with booklet ID 2, 4, 6, 13, 22, 24, and 26 because these booklets do not contain both mathematics and language arts components. We also drop those with booklet ID 20 which denotes special‐needs students taking a one‐hour version of the test. The subject clusters and book IDs are described in the 2009 PISA technical report on page 30 (OECD, 2012). 8 " The focus on students that are 15 years old introduces another complication in this model that may raise a problem. Because 9th grade students are relatively older than 10th grade students, they are slightly more likely to be in the upper part of the achievement distribution for their grade. The age composition difference may lead to instruction time differences across grades, perhaps due to tracking. In terms of bias, however, there would have to be a systematic relationship between the magnitudes of age‐related differences in skills and instruction time. Given that schools face the same sampling rules with regard to age, there should be limited differences across schools in age composition by grade. Nonetheless, differences over time in school support for students across the skill distribution could be related to current age‐related instruction‐time differences. We would expect this effect to be quite small and this is supported by the similarity in estimates across fixed effect specifications. We thank a referee for highlighting this issue. References Adams , R. and Wu , M. ( 2002 ). 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Author notes " We thank Marcus Casey, Robert Kaestner, Cuiping Long, Darren Lubotsky, Ben Ost, Houston Stokes, Javaeria Qureshi, two anonymous referees, and seminar participants at UIC, Calvin College and the National Institute for Educational Evaluation in the Ministry of Education of Spain for helpful comments. © 2015 Royal Economic Society

Kesternich,, Iris;Siflinger,, Bettina;Smith, James, P.;Winter, Joachim, K.

doi: 10.1111/ecoj.12281pmid: N/A

Abstract We investigate long‐run effects of hunger episodes experienced during childhood on health status and behavioural outcomes in later life. We combine self‐reported data on hunger experiences from SHARELIFE with administrative data on food supply (caloric rations) in post‐war Germany. The data suggest that individual behaviour is a pathway between early life‐shocks and adult health. We find that lower‐income adults who experienced hunger spend a larger fraction of income on food. Taken together, our results confirm that in addition to the well‐documented biological channel from early life circumstances to adult health, there are also behavioural pathways. The foetal origins hypothesis establishes a biological link between health shocks experienced in utero and adult health (Smith, 1999; Almond and Currie, 2011 provide excellent overviews). Through adverse events, in particular under‐nutrition, the foetus is programmed to have certain metabolic characteristics which then impact on health in later life. A well‐established biological channel explains these effects, at least in part: Hunger has long‐run effects if under‐nutrition occurs in certain sensitive periods of growth or fat storage required for later growth (Barker, 2004). In this article, we study individual behaviour as a complementary pathway between early‐life shocks and adult health. While there is an emerging literature on cognitive skills as a link between childhood circumstances and adult outcomes, other behavioural channels have received much less attention (Heckman, 2012). We argue that an early‐life event – a prolonged experience of severe hunger during childhood – is not only an immediate negative biological shock to the health stock but also affects subsequent behaviour over the entire life cycle, which impacts health at older ages. Thus, a one‐time shock can change the entire future path of health investments and health over time. Such a mechanism provides an additional rationale for the (causal) effect of early‐life shocks on late‐life health outcomes (and also on socioeconomic status (SES) outcomes which are a function of the time path of health). We illustrate this channel using retrospective data on long‐run effects of a major health shock in Germany: the hunger periods experienced throughout the country in the immediate post‐World War II years. To test the hypothesis of a behavioural channel linking early‐life events and adult outcomes, one would like a panel data set containing information on health, health shocks and health‐related behaviours over long periods of time, ideally starting at birth and extending through adult life. Such data sets unfortunately do not exist for the time period of our investigation. Our research relies instead on retrospective life data from the European Survey of Health, Aging, and Retirement in Europe (SHARE) that recently became available. SHARE covers representative samples of the population aged 50 and over in 13 European countries, with about 20,000 observations. In this analysis, we concentrate on Germany which was not only among the countries most directly affected by World War II in general but also by hunger associated with the war (Kesternich et al., 2014). We also make extensive use of external data on amounts of calories available in different regions of Germany in the post‐war period. The shock we exploit is hunger in post‐World War II Germany and the subsequent behaviour we consider is food consumption. Our hypothesis is that individuals who suffered from hunger in early life ‘eat more’ in later life as a precaution against the risk of new hunger episodes.1 In this article, we look beyond short‐run impacts by suggesting a behavioural mechanism whereby early‐life hunger predicts food consumption late in life. Engel curves for food consumption are significantly different for individuals who suffered from hunger and those who did not. We find that the effect of hunger on food shares is strongest for low‐income individuals. This confirms our assumption that poorer individuals are more at risk of ever becoming hungry again and thus eat more as a type of precautionary measure. Our research also contributes to the literature on how early life experiences shape preferences, of which Malmendier and Nagel (2011) is an example. An important methodological contribution is that we do not only rely on self‐reported measures of hunger but also on data on food supply (measured in calories available per capita per month, which varied in post‐war Germany not only over time but by occupation zone). Our data on caloric rations indicate that self‐reports are indeed a reliable measure for experience of hunger episodes as these self‐reports accurately match both regional and time variation in the hunger episodes. This article is divided into four Sections. Section 1 documents the main episodes of hunger in pre and post‐war Germany and the principal economic reasons for those hunger episodes. Section 2 highlights the central elements of the main data on which we rely in this research. It shows the correspondence between retrospective self‐reported episodes of hunger and our objective contemporaneously reported caloric data. In Section 3, we model the relationship between childhood hunger and caloric restriction on later‐life food consumption and obesity. We summarise our main conclusions in Section 4. 1. The Nutritional Situation in Germany during and after World War II In Germany, food rationing using food stamps started just before WWII on 28 August 1939. From this date until the end of the war, Germany’s food supply and distribution was organised centrally, and food and many other things could only be bought with food stamps (Schlange‐Schoeningen, 1955). From the start of WWII to the end of 1941, daily rations of food were quite high, just below 2,500 kcal (Eitner, 1991). Thus, cuts were small for those who had not lived in luxury before the war. Starting at the end of 1941, food rations were reduced to about 2,000 kcal per day. Increased workloads, night shifts and stress of bombing decreased time spent sleeping and raised caloric needs (Eitner, 1991).2 Severe famine conditions really started towards the end of WWII, continued through the first years of allied occupation and lasted until 1948.3 There were several reasons for this famine. First, with the end of the war, centralised war‐time food distribution and production in Germany completely collapsed. The administrations of four Allied occupation zones (British, US, French and Soviet) set and enforced caloric goals separately for their respective regions. The official rations lay between 1,200 and 1,400 kcal per day in 1946 and 1947 (Schlange‐Schoeningen, 1955). Since the German currency was not backed by a national government, it was basically without value, and trade took place against food stamps or other products. Second, agricultural productivity dropped to about 2/3 to 3/4 of the pre‐war levels (Liebe, 1947). The main reasons were lack of fertilisers, large‐scale war destruction of farm buildings and machinery and death and displacement of workers. In total, the harvest of 1946 was at about 67%, the one of 1947 at about 50–55% of a normal harvest (Haeusser and Maugg, 2011). Agricultural output across the four occupation zones varied. The Soviet and French zones did worse than the UK and US zones, as large parts of local production (fertiliser, meat, milk) were confiscated and distributed to military personnel or sent to occupying countries (Schlange‐Schoeningen, 1955). Until the French zone was united with the UK and US zone, its inhabitants faced a worse nutritional situation than their counterparts in the Anglo‐Saxon zones (about 200–300 kcal per day less). As the war was especially atrocious for the Soviet Union (losing more than 20 million people), the attitude towards the occupied German country was even harsher. Thus, the nutritional situation was worse in the Soviet zone. Besides the drop in agricultural output in today’s territory, Germany lost its pre‐war Eastern parts to Poland, the Czech Republic and the Soviet Union. These Eastern parts were a vital part of the German agricultural system. Until the end of the war, about 30% of agricultural produce and inputs of agricultural production, for example seeds, were produced in the Eastern part of the German Reich (Rothenberger, 1980).4 Problems with agricultural production could not be attenuated by food imports from other countries, since harvests were also bad in the traditional grain producing countries such as Canada, Australia and Argentina (Haeusser and Maugg, 2011). Third, severe problems in food production were exacerbated by breakdowns of trade and transport within Germany. Before WWII, German agricultural production was fairly specialised due to differences in geography but there was ample trade of food products between different parts of Germany. Industries producing agricultural inputs relied on suppliers from all over the Reich (Rothenberger, 1980). After the war, trade between four occupation zones came to a virtual standstill, which amplified problems in food supply due to a shortage in inputs such as seeds and fertilisers. Large‐scale destruction of transport infrastructure (roads, railway tracks and bridges) was another reason for breakdowns of trade between and within occupation zones. Transport by barges on rivers and by rail was nearly impossible after the war, as debris of destroyed bridges blocked major waterways.5 Individuals resorted to basic means of transport (horse‐drawn transport, and handcarts (Farquharson, 1985). Moreover, trade was hampered as occupation zones were unequally endowed with agricultural potential. This led to zones of different nutritional potential, each of which had to meet its own demand completely from local production (Schlange‐Schoeningen, 1955). Trade was made impossible by the fact that the command of allied governments ended at these zone frontiers, so steering of the economy ended there as well (Rothenberger, 1980). The three Western zones were completely blocked off from the Eastern zone that had a higher nutritional potential.6 In addition to these supply side problems, there was increased demand in nutritional products, at least in Western regions. About 10 million refugees from the formerly Eastern parts of the German Reich flooded into the remaining parts (Kulischer, 1948). A large share of these refugees was hosted by the British occupation zone. In 1946, the famine situation improved through food relief shipments from the US. Food relief shipments to Germany in the form of CARE Package shipments to individuals started to be allowed from June 1946. Slowly, trade and agricultural production resumed. The occupation governments understood how big an impediment the condition of the transport sector was, and efforts to restore this sector had been successful from 1947 onwards (Haeusser and Maugg, 2011). With the unification of Western occupation zones and a currency reform on 20 June 1948, the nutritional situation of West Germans significantly improved and supply picked up considerably. In the Eastern part, there was a land and currency reform. The economy was transformed into a socialist system, and improvements in food supply were slower. 2. Data In this Section, we present our data. We first describe the individual‐level survey data that provide both retrospective information on early‐life circumstances and adult outcomes. We then discuss sources of administrative data caloric rations and how we constructed the monthly and regional food supply variables. Finally, we describe how the analytic sample was constructed from these two main sources of data. 2.1. SHARE and Retrospective Early‐life Data from SHARELIFE SHARE is a multidisciplinary cross‐national panel interview survey on health, socio‐economic status and social and family networks of individuals aged 50 or over in continental Europe. The original 2004/2005 SHARE baseline included nationally representative samples in 11 European countries (Denmark, Sweden, Austria, France, Germany, Switzerland, Belgium, Netherlands, Spain, Italy and Greece) drawn from population registries, or from multi‐stage sampling (http://www.share-project.org/). For these countries, a second wave of data collection took place in 2006, the third wave of data collection on this panel (SHARELIFE) was completed in 2008 and a fourth wave was conducted in 2010. In addition to a standard set of demographic attributes, SHARE includes SES variables including net family income and education, and expenditures on food both inside and outside the home. SHARELIFE provides retrospective histories based on life history calendar methods including region living, childhood SES and experiences of hunger. Information in the life history includes family composition and type of home (number of rooms, running water, toilet, etc.), number of books and occupation of father. SHARELIFE provides data on within‐country region of residence and type of housing during the full life of respondents (childhood and adulthood). Respondents were asked about region and type of accommodation when born. Then they were asked if they ever moved and, if yes, when, where, and why. The questions were asked in a loop for each move. 2.2. Caloric Rations and Self‐reported Hunger In SHARELIFE, respondents were asked: ‘(Looking back on your life), was there a period during which you suffered from hunger?’ If respondents said ‘yes’, they were asked when it started and ended so we know duration of hunger episodes. Respondents can only report one hunger period, presumably the most salient. Figure 1 shows the percentage of respondents suffering from hunger by time in all SHARE countries in WWII. Hunger periods respondents reported coincide closely with well‐established historical facts: hunger prevalence picks up with the war’s end for Austria and Germany and during the war for other countries. Germany has by far the most respondents reporting suffering from hunger, especially in years at the end and right after WWII. At its peak, one quarter of the German population reporting suffering from hunger. Fig. 1. Open in new tabDownload slide Self‐reported Hunger by SHARE Countries, 1920–60 Fig. 1. Open in new tabDownload slide Self‐reported Hunger by SHARE Countries, 1920–60 Our main reason for choosing Germany is that during and after WWII, food production and supply were under state control and organised centrally. Besides individuals’ self‐reports on periods of hunger, we collected administrative data on official caloric rations in war‐time Germany, the occupation zones and East and West Germany. Our data include caloric measures from January 1929 to December 1971 (Liebe, 1947; Klatt, 1950; Schlange‐Schoeningen, 1955; Rothenberger, 1980; Farquharson, 1985; Boldorf, 1998). Since food supply was not restricted in Germany before 1939, we use average caloric intake per day from the League of Nations for Germany (Liebe, 1947). From 1939, till the end of WWII the rationing period was one year and new caloric rations were determined in September (Schlange‐Schoeningen, 1955). In April/May 1945, the Allies divided the remaining German territory into four occupation zones independently administered by the US, UK, the Soviet Union and France. Thereafter, official caloric rations were distinguished by occupation zone. Rationing periods were updated every four weeks in all but the Soviet zone, leading to considerable variation in official caloric rations by region and time. Changes in official rations were less regular in the Soviet zone (Schwarzer, 1995). In May 1947, the UK and US zones merged into a united economic territory, providing identical daily caloric rations every four weeks. On 20 June 1948, a currency reform took place in Western zones leading to an immediate improvement in food supply: in July 1948, official caloric rations were about 500 kcal per day higher compared to the month before (Rothenberger, 1980). In 1949 the UK, US and French zones merged into the Trizone which became the Federal Republic of Germany. From 1950, food rationing was completely eliminated and recommended levels of about 3,000 kcal per day were again achieved (Klatt, 1950). In the German Democratic Republic, however, food supply was still problematic so that food rationing was not abolished before 1956 (Schwarzer, 1995). Administrative data are not afflicted with memory misreports, and are exogenous to the individual. We merge the monthly caloric rations to the respondents’ region of residency by year.7 We illustrate the relation between self‐reported hunger and official caloric rations in Figure 2(a). The upper line presents variation in official caloric ration from January 1930 to January 1970. The lower line displays hunger self‐reports. The two measures vary quite closely over time and are especially coincident in the post‐WWII years. When official caloric rations start to decrease in 1939, the fraction of respondents reporting hunger increases at the same time. The official caloric intake achieves its minimum in the summer months of years 1946/7. Fig. 2. Open in new tabDownload slide (a) Amount of Official Caloric Intake per Day Plotted Against the Fraction of Self‐reported Hunger2, January 1930–January 1970. (b) Amount of Official Caloric Intake per Day by Occupation Zone and Months per Year, January 1930–January 1970 Fig. 2. Open in new tabDownload slide (a) Amount of Official Caloric Intake per Day Plotted Against the Fraction of Self‐reported Hunger2, January 1930–January 1970. (b) Amount of Official Caloric Intake per Day by Occupation Zone and Months per Year, January 1930–January 1970 Figure 2(b) displays variation in caloric rations by year for the four occupation zones. Clearly caloric restrictions took place in all four zones after the war. The restrictions remained in force for much longer in the Soviet zone, while the peak restrictions were in place somewhat longer in the French zone. To account for heterogeneous effects of hunger episodes by stages during childhood (infant, child, adolescence), we generate age‐specific average caloric intakes per day at age 0–3, 4–7, 8–16 and 0–16. Figure 3 illustrates the relation between mean self‐reported hunger by our SHARE respondents and the average calories available in the region where our respondents lived between age 0 and 16. The relationship between the administrative calorie data and self‐reported hunger is strong and monotonic – the higher the available calories, the lower the fraction of respondents suffering from hunger during that time. Fig. 3. Open in new tabDownload slide Polynomial Plot of Fraction of Self‐reported Hunger Against Average kcal per Day/1,000 Fig. 3. Open in new tabDownload slide Polynomial Plot of Fraction of Self‐reported Hunger Against Average kcal per Day/1,000 One concern for our analysis is that effects of hunger are simply picking up the effects of childhood SES. Figure 4 shows variation in hunger in Germany over this time period for those in low, medium and high childhood SES. This Figure demonstrates that hunger was a common experience no matter what one’s family’s social class was. If anything at its peak, those in high childhood SES families may have experienced more hunger. If self‐reports are reliable measures for the experience of hunger, we should find a significant association between caloric rations and hunger self‐reports.8 To evaluate, we conduct an analysis regressing self‐reported hunger on age‐specific caloric rations. Self‐reported hunger is a binary variable that takes the value one if a respondent reported suffered hunger before age 17. The caloric measure is the official caloric ration provided per day, averaged over a specific child age band. To control for region‐specific differences, we include occupation zones dummies with the US zone as the reference group. All models also include an age quadratic and dummies for middle SES and high SES as a child with low childhood SES as the reference group.9 Standard errors are clustered on birthdate‐occupation zone. The basic model results in the second column of Table 1 suggest a strong association between the official caloric rations and self‐reported hunger. The estimated coefficient for the age group 0–16 implies that an increase in the average daily caloric ration of 1,000 kcal per day increases the probability of suffering from hunger by 24.2 percentage points. Fig. 4. Open in new tabDownload slide Fraction of Self‐reported Hunger by Socio‐economic Status, 1930–60 Fig. 4. Open in new tabDownload slide Fraction of Self‐reported Hunger by Socio‐economic Status, 1930–60 Table 1 OLS Regressions of Hunger at Age 0–16 on Negative Average Daily Caloric Intake Between Ages 0 and 16 Variables . (1) . (2) . (3) . (minus) average cal/1,000 age 0–16 0.242*** 0.120** (0.052) (0.059) Male 0.153 (0.151) (minus) average cal/1,000 age 0–16 × male 0.056 (0.052) Urban area (at birth) 0.274* (0.152) (minus) average cal/1,000 age 0–16 × urban area 0.094* (0.052) Father_absent 0.577*** (0.215) (minus) average cal/1,000 age 0–16 × father absent 0.199** (0.078) UK zone (at birth) 0.036 0.042* 0.043* (0.022) (0.022) (0.023) French zone (at birth) 0.044 0.036 0.035 (0.041) (0.042) (0.043) Soviet zone (at birth) 0.052** 0.006 0.003 (0.023) (0.023) (0.023) Childhood SES medium −0.002 −0.000 −0.004 (0.026) (0.026) (0.025) Childhood SES high 0.019 0.020 0.013 (0.029) (0.029) (0.029) Constant −0.034 0.816*** 0.458** (0.031) (0.175) (0.192) Observations 1,040 1,040 1,040 R2 0.123 0.143 0.166 Variables . (1) . (2) . (3) . (minus) average cal/1,000 age 0–16 0.242*** 0.120** (0.052) (0.059) Male 0.153 (0.151) (minus) average cal/1,000 age 0–16 × male 0.056 (0.052) Urban area (at birth) 0.274* (0.152) (minus) average cal/1,000 age 0–16 × urban area 0.094* (0.052) Father_absent 0.577*** (0.215) (minus) average cal/1,000 age 0–16 × father absent 0.199** (0.078) UK zone (at birth) 0.036 0.042* 0.043* (0.022) (0.022) (0.023) French zone (at birth) 0.044 0.036 0.035 (0.041) (0.042) (0.043) Soviet zone (at birth) 0.052** 0.006 0.003 (0.023) (0.023) (0.023) Childhood SES medium −0.002 −0.000 −0.004 (0.026) (0.026) (0.025) Childhood SES high 0.019 0.020 0.013 (0.029) (0.029) (0.029) Constant −0.034 0.816*** 0.458** (0.031) (0.175) (0.192) Observations 1,040 1,040 1,040 R2 0.123 0.143 0.166 Notes Standard errors in parentheses. ***p < 0.01, **p < 0.05, *p < 0.1. Models also include an age quadratic. Standard errors are clustered on occupation zone‐month of birth level. Open in new tab Table 1 OLS Regressions of Hunger at Age 0–16 on Negative Average Daily Caloric Intake Between Ages 0 and 16 Variables . (1) . (2) . (3) . (minus) average cal/1,000 age 0–16 0.242*** 0.120** (0.052) (0.059) Male 0.153 (0.151) (minus) average cal/1,000 age 0–16 × male 0.056 (0.052) Urban area (at birth) 0.274* (0.152) (minus) average cal/1,000 age 0–16 × urban area 0.094* (0.052) Father_absent 0.577*** (0.215) (minus) average cal/1,000 age 0–16 × father absent 0.199** (0.078) UK zone (at birth) 0.036 0.042* 0.043* (0.022) (0.022) (0.023) French zone (at birth) 0.044 0.036 0.035 (0.041) (0.042) (0.043) Soviet zone (at birth) 0.052** 0.006 0.003 (0.023) (0.023) (0.023) Childhood SES medium −0.002 −0.000 −0.004 (0.026) (0.026) (0.025) Childhood SES high 0.019 0.020 0.013 (0.029) (0.029) (0.029) Constant −0.034 0.816*** 0.458** (0.031) (0.175) (0.192) Observations 1,040 1,040 1,040 R2 0.123 0.143 0.166 Variables . (1) . (2) . (3) . (minus) average cal/1,000 age 0–16 0.242*** 0.120** (0.052) (0.059) Male 0.153 (0.151) (minus) average cal/1,000 age 0–16 × male 0.056 (0.052) Urban area (at birth) 0.274* (0.152) (minus) average cal/1,000 age 0–16 × urban area 0.094* (0.052) Father_absent 0.577*** (0.215) (minus) average cal/1,000 age 0–16 × father absent 0.199** (0.078) UK zone (at birth) 0.036 0.042* 0.043* (0.022) (0.022) (0.023) French zone (at birth) 0.044 0.036 0.035 (0.041) (0.042) (0.043) Soviet zone (at birth) 0.052** 0.006 0.003 (0.023) (0.023) (0.023) Childhood SES medium −0.002 −0.000 −0.004 (0.026) (0.026) (0.025) Childhood SES high 0.019 0.020 0.013 (0.029) (0.029) (0.029) Constant −0.034 0.816*** 0.458** (0.031) (0.175) (0.192) Observations 1,040 1,040 1,040 R2 0.123 0.143 0.166 Notes Standard errors in parentheses. ***p < 0.01, **p < 0.05, *p < 0.1. Models also include an age quadratic. Standard errors are clustered on occupation zone‐month of birth level. Open in new tab We estimated three additional models similar to the second column in Table 1 that examined the relationship between caloric restrictions and the reporting of hunger in the three age intervals 0–3, 4–7 and 8–16. The estimated coefficients of the Kcal variables on hunger in the same childhood age interval were 0.029 (age interval 0–3), 0.123 (age interval 4–7) and 0.158 (age interval 8–16). All three estimated coefficients are statistically significant at the 1% level. The smaller coefficient for the age interval 0–3 could indicate understandably more memory related issues in that age range or more protective behaviour of parents of young infants during hunger episodes. Controlling for specific caloric rations, there are other factors that may matter for the experience of hunger and these are included in the third column of Table 1. We know that the hunger experience in post‐war Germany was stronger in urban areas than in the countryside. This is reflected by a positive and significant main effect of the variable urban (at birth) as well as a positive and significant interaction of urban residence with our measure for caloric deprivation. Urban residents were less able than their rural counterparts to supplement food rations with home production, especially during periods of severe caloric restrictions. In contrast, controls right at the farm were not as strict so that rural residents could keep some food for themselves. In addition, refugees tended to move to cities so there were more people there than there should have been. Similarly, as documented in Kesternich et al. (2014), many post‐war children grew up at least temporarily without their fathers. The absence of the father in the household also increases the likelihood to report having suffered from hunger, an effect that is stronger when caloric restrictions were more severe. The absence of fathers not only reduced resources but made it more difficult to travel to the countryside (say by bicycle) to barter for food and bring it back home.10 Interestingly, we find a significant and positive effect on the probability to have suffered from hunger for our respondents being born in the British zone as compared to our reference group, the US zone, even after controlling for caloric restrictions in the model in the second column. The difference between the British and US zones most likely lie on the one hand in the fact that cities were more heavily destroyed in the British zone but also in the ways the administration was organised. While the US zone relied on a federal idea and soon began to entrust the local organisation to the local administration, the British zone was organised centrally, so that changes came about much more slowly than in the US zone (Schlange‐Schoeningen, 1955). The first two columns of Table 1 show the relationship between hunger and zone without controlling for these other variables that were interacted with caloric restrictions. Without a caloric control, reported hunger was lower in the US zone that the other three zones. Reported hunger was highest in the Soviet zone, but that result goes away once we control for the official level of caloric restriction. This suggests that the principal problem in the Soviet zone was the low levels of caloric rations compared to the other zones. Given the results in Table 1, we presume that the official caloric rations are a good measure to proxy self‐reported hunger. In contrast to the respondents’ hunger reports, the calories used here are exogenous to the individual and not affected by any recall bias.11 Lastly, in order to show that the experience of hunger is not just a measure for low childhood SES, we find that childhood SES does not predict the experience of hunger. 2.3. Construction of the Analytic Dataset For the analysis we consider a sample of 1,785 respondents from Germany who participated both in SHARELIFE and either in wave 2 or wave 4 of the SHARE survey. Information from wave 2 is used if the respondent did not participate in wave 4, or if the required information is not available in wave 4. Official caloric rations are available for the post‐war German territory and vary over time as well as over the occupation zones. Therefore, we exclude respondents who were not born within today’s German borders. Treatment periods refer to the years 1945–8 when Germany suffered from extreme food shortages. Since we are interested in the consequences of under‐nutrition during childhood, we exclude respondents who were born before January 1929 and after December 1960.12 Our final sample consists of 1,350 respondents. To measure food consumption behaviour, we generate a food share variable as the fraction of household food expenditures in total household net income. SHARE interviews (wave 2 and 4) collect data on household food consumption expenditures by asking for the average monthly amount spent on food at home and outside home during the last 12 months. We add the values of these two items and obtain the total household food expenditures as the enumerator of the share. The denominator is defined by the total household net income in an average month which SHARE collects using a one‐shot question. Due to potential misreports and implausible values in the income question, we trim the income distributions of waves 2 and 4 at the 5th and 95th percentiles, obtaining 1,094 individuals with a food share value. In wave 4, some respondents reported implausibly high values of monthly household net income. We correct these numbers by replacing wave 4 values with those of wave 2 if income in wave 4 was at least five times higher than in wave 2. Finally, we trim the food share distribution by eliminating values below the 5th and above 95th percentile.13 Our final analytic data set consists of 991 observations with valid food share and income values. We generate the logarithm of the total household net income as well as two income splines splitting up the income distribution at its median. We moreover compute a number of interactions between these different income measures and self‐reported hunger as well as the caloric measures. Table 2 provides the descriptive statistics on the main outcomes of interest, income and hunger quantities, and the control variables. Table 2 Summary Statistics of the Analytical Data Set Variables . N . Mean . SD . Min . Max . Food share 991 0.21 0.078 0.059 0.40 Log HH net income 1,091 7.83 0.64 6.70 10.46 Quadratic log HH net income 1,091 61.76 10.68 44.85 109.48 log HH net income (lo) 1,091 7.55 0.26 6.70 7.74 log HH net income (hi) 1,091 0.28 0.49 0 2.72 Hunger measures Hunger at age 0–16 1,091 0.11 0.32 0 1 Hunger at age 0–3 1,091 0.02 0.13 0 1 Hunger at age 4–7 1,091 0.06 0.24 0 1 Hunger at age 8–16 1,091 0.09 0.29 0 1 (minus) average kcal per day/1,000 at age 0–16 1,091 −2.63 0.38 −3.1 −1.99 (minus) average kcal per day/1,000 at age 0–3 1,091 −2.47 0.62 −3.1 −1.20 (minus) average kcal per day/1,000 at age 4–7 1,091 −2.52 0.65 −3.1 −1.20 (minus) average kcal per day/1,000 at age 8–16 1,091 −2.75 0.50 −3.1 −1.55 Control variables US zone (at birth) 1,091 0.26 0.44 0 1 UK zone (at birth) 1,091 0.33 0.47 0 1 Soviet zone (at birth) 1,091 0.35 0.47 0 1 French zone (at birth) 1,091 0.06 0.24 0 1 Age‐50 1,068 14.82 7.55 −4 32 (Age‐50)2 1,068 276 242 0 1,024 Male 1,091 0.50 0.5 0 1 Urban area (at birth) 1,091 0.35 0.48 0 1 Household size 1,068 2.06 0.74 1 7 Being in partnership 951 0.80 0.40 0 1 Years of education 1,091 13.14 3.06 6 25 Missing years of education 1,091 0.06 0.23 0 1 Childhood SES medium 1,062 0.55 0.50 0 1 Childhood SES high 1,091 0.27 0.45 0 1 Health: being obese 1,042 0.197 0.40 0 1 Variables . N . Mean . SD . Min . Max . Food share 991 0.21 0.078 0.059 0.40 Log HH net income 1,091 7.83 0.64 6.70 10.46 Quadratic log HH net income 1,091 61.76 10.68 44.85 109.48 log HH net income (lo) 1,091 7.55 0.26 6.70 7.74 log HH net income (hi) 1,091 0.28 0.49 0 2.72 Hunger measures Hunger at age 0–16 1,091 0.11 0.32 0 1 Hunger at age 0–3 1,091 0.02 0.13 0 1 Hunger at age 4–7 1,091 0.06 0.24 0 1 Hunger at age 8–16 1,091 0.09 0.29 0 1 (minus) average kcal per day/1,000 at age 0–16 1,091 −2.63 0.38 −3.1 −1.99 (minus) average kcal per day/1,000 at age 0–3 1,091 −2.47 0.62 −3.1 −1.20 (minus) average kcal per day/1,000 at age 4–7 1,091 −2.52 0.65 −3.1 −1.20 (minus) average kcal per day/1,000 at age 8–16 1,091 −2.75 0.50 −3.1 −1.55 Control variables US zone (at birth) 1,091 0.26 0.44 0 1 UK zone (at birth) 1,091 0.33 0.47 0 1 Soviet zone (at birth) 1,091 0.35 0.47 0 1 French zone (at birth) 1,091 0.06 0.24 0 1 Age‐50 1,068 14.82 7.55 −4 32 (Age‐50)2 1,068 276 242 0 1,024 Male 1,091 0.50 0.5 0 1 Urban area (at birth) 1,091 0.35 0.48 0 1 Household size 1,068 2.06 0.74 1 7 Being in partnership 951 0.80 0.40 0 1 Years of education 1,091 13.14 3.06 6 25 Missing years of education 1,091 0.06 0.23 0 1 Childhood SES medium 1,062 0.55 0.50 0 1 Childhood SES high 1,091 0.27 0.45 0 1 Health: being obese 1,042 0.197 0.40 0 1 Open in new tab Table 2 Summary Statistics of the Analytical Data Set Variables . N . Mean . SD . Min . Max . Food share 991 0.21 0.078 0.059 0.40 Log HH net income 1,091 7.83 0.64 6.70 10.46 Quadratic log HH net income 1,091 61.76 10.68 44.85 109.48 log HH net income (lo) 1,091 7.55 0.26 6.70 7.74 log HH net income (hi) 1,091 0.28 0.49 0 2.72 Hunger measures Hunger at age 0–16 1,091 0.11 0.32 0 1 Hunger at age 0–3 1,091 0.02 0.13 0 1 Hunger at age 4–7 1,091 0.06 0.24 0 1 Hunger at age 8–16 1,091 0.09 0.29 0 1 (minus) average kcal per day/1,000 at age 0–16 1,091 −2.63 0.38 −3.1 −1.99 (minus) average kcal per day/1,000 at age 0–3 1,091 −2.47 0.62 −3.1 −1.20 (minus) average kcal per day/1,000 at age 4–7 1,091 −2.52 0.65 −3.1 −1.20 (minus) average kcal per day/1,000 at age 8–16 1,091 −2.75 0.50 −3.1 −1.55 Control variables US zone (at birth) 1,091 0.26 0.44 0 1 UK zone (at birth) 1,091 0.33 0.47 0 1 Soviet zone (at birth) 1,091 0.35 0.47 0 1 French zone (at birth) 1,091 0.06 0.24 0 1 Age‐50 1,068 14.82 7.55 −4 32 (Age‐50)2 1,068 276 242 0 1,024 Male 1,091 0.50 0.5 0 1 Urban area (at birth) 1,091 0.35 0.48 0 1 Household size 1,068 2.06 0.74 1 7 Being in partnership 951 0.80 0.40 0 1 Years of education 1,091 13.14 3.06 6 25 Missing years of education 1,091 0.06 0.23 0 1 Childhood SES medium 1,062 0.55 0.50 0 1 Childhood SES high 1,091 0.27 0.45 0 1 Health: being obese 1,042 0.197 0.40 0 1 Variables . N . Mean . SD . Min . Max . Food share 991 0.21 0.078 0.059 0.40 Log HH net income 1,091 7.83 0.64 6.70 10.46 Quadratic log HH net income 1,091 61.76 10.68 44.85 109.48 log HH net income (lo) 1,091 7.55 0.26 6.70 7.74 log HH net income (hi) 1,091 0.28 0.49 0 2.72 Hunger measures Hunger at age 0–16 1,091 0.11 0.32 0 1 Hunger at age 0–3 1,091 0.02 0.13 0 1 Hunger at age 4–7 1,091 0.06 0.24 0 1 Hunger at age 8–16 1,091 0.09 0.29 0 1 (minus) average kcal per day/1,000 at age 0–16 1,091 −2.63 0.38 −3.1 −1.99 (minus) average kcal per day/1,000 at age 0–3 1,091 −2.47 0.62 −3.1 −1.20 (minus) average kcal per day/1,000 at age 4–7 1,091 −2.52 0.65 −3.1 −1.20 (minus) average kcal per day/1,000 at age 8–16 1,091 −2.75 0.50 −3.1 −1.55 Control variables US zone (at birth) 1,091 0.26 0.44 0 1 UK zone (at birth) 1,091 0.33 0.47 0 1 Soviet zone (at birth) 1,091 0.35 0.47 0 1 French zone (at birth) 1,091 0.06 0.24 0 1 Age‐50 1,068 14.82 7.55 −4 32 (Age‐50)2 1,068 276 242 0 1,024 Male 1,091 0.50 0.5 0 1 Urban area (at birth) 1,091 0.35 0.48 0 1 Household size 1,068 2.06 0.74 1 7 Being in partnership 951 0.80 0.40 0 1 Years of education 1,091 13.14 3.06 6 25 Missing years of education 1,091 0.06 0.23 0 1 Childhood SES medium 1,062 0.55 0.50 0 1 Childhood SES high 1,091 0.27 0.45 0 1 Health: being obese 1,042 0.197 0.40 0 1 Open in new tab 3. Empirical Strategy and Results The objective of this study is to show that individual behaviour can be a pathway between an early‐life shock – hunger – and later‐life health outcomes. First, we analyse food share as the behavioural component which is defined as the share of household food expenditure (at home and outside the house) in total household net income. As explained in the previous Sections, our measures for experiencing a period of under‐nutrition are a binary indicator variable, based on self‐report, for whether the respondent suffered from hunger, and measures of average calorie supply that vary across occupation zones and by month.14 In a second step, we specify models that relate early life hunger and later‐life obesity. To see whether the food spending translates into measures of body weight, we use the probability of being obese as adult health measure and estimate the same specifications as for the behavioural food share model. 3.1. Engel Curves We start by specifying the link between hunger episodes during childhood and food shares. To model food shares, we use a variant of the well‐known parametric Working‐Leser specification of an Engel curve. Engel curves state that fractions of income spent on food decrease as income increases for given tastes and preferences. An Engel curve is assumed to be shape‐invariant, suggesting that changes in policies and demographic variables shift and scale the function without altering overall shape (Blundell et al., 2007). We assume that experiencing hunger during childhood represents such an Engel curve shifter. Individuals might change spending on food in response to the childhood experience of hunger leading to higher food shares in adult life. We analyse this relation by interacting hunger measures with the logarithm of the household income. Food expenditures are not necessarily a linear function of income (Lewbel, 2008). In our main specification, we model non‐linearities in income by introducing splines of the logarithmic income that are split at the median income. In addition, we interact these income splines and the hunger self‐reports, allowing us to detect different reactions for low and high‐income households to the experience of hunger (Lewbel, 2010). The Engel curve equation for the models estimated in Tables 3 and 4 is FSi=β0+β1Hi,age+β2I(<p50)i+β3I(≥p50)i+β4Hi,age×I(<p50)i+β5Hi,age×I(≥p50)i+xi′γ+εi,(1) where Ii refers to the logarithm of total household net income, Hi,age is self‐reported hunger at a specific age, I(< p50)i and I(≥ p50)i are the splines of the logarithmic income that split the corresponding distribution at its median. The coefficients β4 and measure β5 measure the impact of suffering from hunger along the upper and the lower 50% quantiles of the income dimension. xit is a vector of other covariates,15 and εi is the error term.16 Table 3 OLS Regression Food Share on Self‐reported Hunger, Splines (Median Split) Log Net HH Income and Interaction Terms, Ages 0–16, 0–3, 4–7 and 8–16 Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.050*** −0.056*** −0.054*** −0.049*** (0.013) (0.012) (0.012) (0.013) log HH net income (hi) −0.081*** −0.076*** −0.077*** −0.082*** (0.012) (0.011) (0.011) (0.011) Hunger at age 0–16 0.547** (0.246) Hunger age 0–16 × log HH net income (lo) −0.075** (0.033) Hunger age 0–16 × log HH net income (hi) 0.044 (0.032) Hunger at age 0–3 1.139** (0.515) Hunger age 0–3 × log HH net income (lo) −0.151** (0.069) Hunger age 0–3 × log HH net income (hi) −0.014 (0.045) Hunger at age 4–7 0.926** (0.376) Hunger age 4–7 × log HH net income (lo) −0.123** (0.050) Hunger age 4–7 × log HH net income (hi) 0.032 (0.042) Hunger at age 8–16 0.721*** (0.271) Hunger age 8–16 × log HH net income (lo) −0.099*** (0.036) Hunger age 8–16 × log HH net income (hi) 0.081* (0.041) Constant 0.534*** 0.580*** 0.563*** 0.530*** (0.090) (0.088) (0.088) (0.090) Observations 943 943 943 943 R2 0.208 0.205 0.206 0.213 Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.050*** −0.056*** −0.054*** −0.049*** (0.013) (0.012) (0.012) (0.013) log HH net income (hi) −0.081*** −0.076*** −0.077*** −0.082*** (0.012) (0.011) (0.011) (0.011) Hunger at age 0–16 0.547** (0.246) Hunger age 0–16 × log HH net income (lo) −0.075** (0.033) Hunger age 0–16 × log HH net income (hi) 0.044 (0.032) Hunger at age 0–3 1.139** (0.515) Hunger age 0–3 × log HH net income (lo) −0.151** (0.069) Hunger age 0–3 × log HH net income (hi) −0.014 (0.045) Hunger at age 4–7 0.926** (0.376) Hunger age 4–7 × log HH net income (lo) −0.123** (0.050) Hunger age 4–7 × log HH net income (hi) 0.032 (0.042) Hunger at age 8–16 0.721*** (0.271) Hunger age 8–16 × log HH net income (lo) −0.099*** (0.036) Hunger age 8–16 × log HH net income (hi) 0.081* (0.041) Constant 0.534*** 0.580*** 0.563*** 0.530*** (0.090) (0.088) (0.088) (0.090) Observations 943 943 943 943 R2 0.208 0.205 0.206 0.213 Notes Standard errors are clustered on the household level; ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, household size, years of education, dummies for medium and high childhood SES and a dummy for missing education. Open in new tab Table 3 OLS Regression Food Share on Self‐reported Hunger, Splines (Median Split) Log Net HH Income and Interaction Terms, Ages 0–16, 0–3, 4–7 and 8–16 Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.050*** −0.056*** −0.054*** −0.049*** (0.013) (0.012) (0.012) (0.013) log HH net income (hi) −0.081*** −0.076*** −0.077*** −0.082*** (0.012) (0.011) (0.011) (0.011) Hunger at age 0–16 0.547** (0.246) Hunger age 0–16 × log HH net income (lo) −0.075** (0.033) Hunger age 0–16 × log HH net income (hi) 0.044 (0.032) Hunger at age 0–3 1.139** (0.515) Hunger age 0–3 × log HH net income (lo) −0.151** (0.069) Hunger age 0–3 × log HH net income (hi) −0.014 (0.045) Hunger at age 4–7 0.926** (0.376) Hunger age 4–7 × log HH net income (lo) −0.123** (0.050) Hunger age 4–7 × log HH net income (hi) 0.032 (0.042) Hunger at age 8–16 0.721*** (0.271) Hunger age 8–16 × log HH net income (lo) −0.099*** (0.036) Hunger age 8–16 × log HH net income (hi) 0.081* (0.041) Constant 0.534*** 0.580*** 0.563*** 0.530*** (0.090) (0.088) (0.088) (0.090) Observations 943 943 943 943 R2 0.208 0.205 0.206 0.213 Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.050*** −0.056*** −0.054*** −0.049*** (0.013) (0.012) (0.012) (0.013) log HH net income (hi) −0.081*** −0.076*** −0.077*** −0.082*** (0.012) (0.011) (0.011) (0.011) Hunger at age 0–16 0.547** (0.246) Hunger age 0–16 × log HH net income (lo) −0.075** (0.033) Hunger age 0–16 × log HH net income (hi) 0.044 (0.032) Hunger at age 0–3 1.139** (0.515) Hunger age 0–3 × log HH net income (lo) −0.151** (0.069) Hunger age 0–3 × log HH net income (hi) −0.014 (0.045) Hunger at age 4–7 0.926** (0.376) Hunger age 4–7 × log HH net income (lo) −0.123** (0.050) Hunger age 4–7 × log HH net income (hi) 0.032 (0.042) Hunger at age 8–16 0.721*** (0.271) Hunger age 8–16 × log HH net income (lo) −0.099*** (0.036) Hunger age 8–16 × log HH net income (hi) 0.081* (0.041) Constant 0.534*** 0.580*** 0.563*** 0.530*** (0.090) (0.088) (0.088) (0.090) Observations 943 943 943 943 R2 0.208 0.205 0.206 0.213 Notes Standard errors are clustered on the household level; ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, household size, years of education, dummies for medium and high childhood SES and a dummy for missing education. Open in new tab Table 4 OLS Regression Food Share on Negative Average Daily Caloric Intake (Divided by 1,000) Between Ages 0–16, 0–3, 4–7 and 8–16, Log Net HH Income, Splines (Median Split) of Log Net HH Income and Interaction Terms Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.232*** −0.100** −0.171*** −0.164*** (0.067) (0.048) (0.043) (0.052) log HH net income (hi) 0.027 −0.076* −0.032 −0.010 (0.064) (0.040) (0.036) (0.060) (minus) average cal/1,000 age 0–16 0.471** (0.185) (minus) average cal age 0–16) × log HH net income (lo) −0.062** (0.025) (minus) average cal age 0–16 × log HH net income (hi) 0.042* (0.023) (minus) average cal/1,000 age 0–3 0.113 (0.134) (minus) average cal age 0–3 × log HH net income (lo) −0.013 (0.018) (minus) average cal age 0–3 × log HH net income (hi) 0.004 (0.014) (minus) average cal/1,000 age 4–7 0.306*** (0.119) (minus) average cal age 4–7 × log HH net income (lo) −0.040** (0.016) (minus) average cal age 4–7 × log HH net income (hi) 0.021* (0.013) (minus) average cal/1,000 age 8–16 0.239* (0.139) (minus) average cal age 8–16 × log HH net income (lo) −0.035* (0.019) (minus) average cal age 8–16 × log HH net income (hi) 0.027 (0.020) Constant 1.930*** 0.973*** 1.459*** 1.321*** (0.502) (0.358) (0.321) (0.383) Observations 943 943 943 943 R2 0.248 0.249 0.248 0.248 Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.232*** −0.100** −0.171*** −0.164*** (0.067) (0.048) (0.043) (0.052) log HH net income (hi) 0.027 −0.076* −0.032 −0.010 (0.064) (0.040) (0.036) (0.060) (minus) average cal/1,000 age 0–16 0.471** (0.185) (minus) average cal age 0–16) × log HH net income (lo) −0.062** (0.025) (minus) average cal age 0–16 × log HH net income (hi) 0.042* (0.023) (minus) average cal/1,000 age 0–3 0.113 (0.134) (minus) average cal age 0–3 × log HH net income (lo) −0.013 (0.018) (minus) average cal age 0–3 × log HH net income (hi) 0.004 (0.014) (minus) average cal/1,000 age 4–7 0.306*** (0.119) (minus) average cal age 4–7 × log HH net income (lo) −0.040** (0.016) (minus) average cal age 4–7 × log HH net income (hi) 0.021* (0.013) (minus) average cal/1,000 age 8–16 0.239* (0.139) (minus) average cal age 8–16 × log HH net income (lo) −0.035* (0.019) (minus) average cal age 8–16 × log HH net income (hi) 0.027 (0.020) Constant 1.930*** 0.973*** 1.459*** 1.321*** (0.502) (0.358) (0.321) (0.383) Observations 943 943 943 943 R2 0.248 0.249 0.248 0.248 Notes Standard errors are clustered on occupation zone‐month of birth level; ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, household size, years of education, dummies for medium and high childhood SES, a dummy for missing education and occupation zone dummies. Open in new tab Table 4 OLS Regression Food Share on Negative Average Daily Caloric Intake (Divided by 1,000) Between Ages 0–16, 0–3, 4–7 and 8–16, Log Net HH Income, Splines (Median Split) of Log Net HH Income and Interaction Terms Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.232*** −0.100** −0.171*** −0.164*** (0.067) (0.048) (0.043) (0.052) log HH net income (hi) 0.027 −0.076* −0.032 −0.010 (0.064) (0.040) (0.036) (0.060) (minus) average cal/1,000 age 0–16 0.471** (0.185) (minus) average cal age 0–16) × log HH net income (lo) −0.062** (0.025) (minus) average cal age 0–16 × log HH net income (hi) 0.042* (0.023) (minus) average cal/1,000 age 0–3 0.113 (0.134) (minus) average cal age 0–3 × log HH net income (lo) −0.013 (0.018) (minus) average cal age 0–3 × log HH net income (hi) 0.004 (0.014) (minus) average cal/1,000 age 4–7 0.306*** (0.119) (minus) average cal age 4–7 × log HH net income (lo) −0.040** (0.016) (minus) average cal age 4–7 × log HH net income (hi) 0.021* (0.013) (minus) average cal/1,000 age 8–16 0.239* (0.139) (minus) average cal age 8–16 × log HH net income (lo) −0.035* (0.019) (minus) average cal age 8–16 × log HH net income (hi) 0.027 (0.020) Constant 1.930*** 0.973*** 1.459*** 1.321*** (0.502) (0.358) (0.321) (0.383) Observations 943 943 943 943 R2 0.248 0.249 0.248 0.248 Variables . (1) . (2) . (3) . (4) . Foodshare . Foodshare . Foodshare . Foodshare . log HH net income (lo) −0.232*** −0.100** −0.171*** −0.164*** (0.067) (0.048) (0.043) (0.052) log HH net income (hi) 0.027 −0.076* −0.032 −0.010 (0.064) (0.040) (0.036) (0.060) (minus) average cal/1,000 age 0–16 0.471** (0.185) (minus) average cal age 0–16) × log HH net income (lo) −0.062** (0.025) (minus) average cal age 0–16 × log HH net income (hi) 0.042* (0.023) (minus) average cal/1,000 age 0–3 0.113 (0.134) (minus) average cal age 0–3 × log HH net income (lo) −0.013 (0.018) (minus) average cal age 0–3 × log HH net income (hi) 0.004 (0.014) (minus) average cal/1,000 age 4–7 0.306*** (0.119) (minus) average cal age 4–7 × log HH net income (lo) −0.040** (0.016) (minus) average cal age 4–7 × log HH net income (hi) 0.021* (0.013) (minus) average cal/1,000 age 8–16 0.239* (0.139) (minus) average cal age 8–16 × log HH net income (lo) −0.035* (0.019) (minus) average cal age 8–16 × log HH net income (hi) 0.027 (0.020) Constant 1.930*** 0.973*** 1.459*** 1.321*** (0.502) (0.358) (0.321) (0.383) Observations 943 943 943 943 R2 0.248 0.249 0.248 0.248 Notes Standard errors are clustered on occupation zone‐month of birth level; ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, household size, years of education, dummies for medium and high childhood SES, a dummy for missing education and occupation zone dummies. Open in new tab Table 3 presents results obtained from estimation of food shares on hunger, logarithm of household net income, interactions of hunger with median logarithmic income splines and other relevant covariates. Not surprisingly, income has a strong negative impact on food shares reflecting the standard Engel curve relation (Blundell et al., 2007). In all childhood age bands, hunger increases food shares especially for those below median income. Let us first consider our main estimates for everyone who experienced hunger between ages 0 and 16 (Table 3, column 1). For those respondents who have not suffered from hunger, if income increases by 1%, food share decreases for 0.050 for low‐income households, and a steeper decrease of 0.081 for high‐income households. The experience of hunger significantly increases the share of household food spending as can be seen by the positive and significant main effect of hunger. We also find strong positive statistically significant positive impacts of hunger main effects on food shares for ages 0–3 and 4–7, 8–16.17 This relationship is largely driven by those whose log net household income is below the sample median. As income increases towards the median income in these groups, differences between those who experienced hunger and other respondents becomes progressively smaller. It may even revert for incomes above the median but these effects are generally not statistically significant. Thus, poor respondents who experienced hunger as a child spend more of their income on food. We interpret their behaviour as risk aversion against once again experiencing hunger which is a real risk for low‐income households but not for well‐to‐do households. Thus, as those respondents get richer, they then substitute away from food and towards other goods faster than those respondents who did not suffer from hunger. Next, we replace Hi in (1) with (minus) the average kcal available per day in the respective age period (remember that less calories are associated with more hunger, so that we now expect a positive association with our variable and the experience of hunger). In contrast to self‐reported hunger, which might be correlated with unobserved factors such as growing up in a family of farmers, caloric rations are exogenous to the individual as they were fixed by administrations of occupation zones and vary over time. Table 4 reports the results with the caloric restrictions variables instead of self‐reported hunger. The impact of log net household income on the food share is similar in sign as in regressions using hunger self‐reports. The main effect of low calorie restrictions per day now is statistically significant for our main specification (age 0–16), as well as for children when they are older than age three (groups 4–7 and 8–16). Thus, the greater the caloric restrictions per day to which the individuals were exposed as children, the higher the amounts they spend on food relative to their income as older adults. Moreover, the interaction terms of the caloric measure and income are significantly different from zero. These results using exogenous caloric restrictions confirm the findings from the self‐reported hunger regressions in Table 3. They suggest that as adults, low‐income individuals in particular who suffered from hunger in early life have a different adult food consumption behaviour than those who did not experience childhood hunger. The within specific childhood age results indicate that these results are not simply the reflection of the Barker type very early childhood results. We illustrate the relation found in these models by plotting food share predictions for the hunger experience at age 0–16 against log net household income. Figure 5 represents Engel curves stratified by whether the individual suffered from childhood hunger or not. For both groups, we find an increasing food share as income decreases. Hunger differences in slopes of income coefficients are significant for low incomes. Those with a log income below the median spend a considerably higher fraction of their income on food when they experienced hunger as a child than those who did not. With increasing income, the food share of hunger and no hunger group converge for median incomes and then diverge somewhat again. Fig. 5. Open in new tabDownload slide Plot of Food Share Predictions Against Logarithm of Income by Hunger Using Column 1 Specification in Table 3 Fig. 5. Open in new tabDownload slide Plot of Food Share Predictions Against Logarithm of Income by Hunger Using Column 1 Specification in Table 3 The more income respondents earn, the more the behavioural consumption differences associated with childhood hunger decrease. Thus, having suffered from childhood hunger might change individuals’ adult behaviour which in turn might have consequences on later‐life health outcomes. One explanation for why we only see significant changes in food consumption for low‐income individuals is that these individuals take precaution against the risk of new hunger episodes. One possible limitation of our analysis up to this point is that the childhood experience of hunger and childhood exposure to caloric limitations is measured at the individual level while the outcome under investigation (food shares) is measured at the household level. For food shares, measurement of both the numerator (food expenditures) and the denominator (net household income) is at the household level. This is rectified in the analysis presented in Table 5 where the household experience of hunger and exposure to caloric restrictions during childhood ages 0–16 are modelled. In the models in Table 5, instead of the individual level of hunger, we define hunger on the household level as ‘at least one household member has suffered from hunger’ and instead of the individual‐level caloric restriction the household average of daily caloric rations respectively. Results obtained in Table 5 are quantitatively very similar to the individual models in Tables 3 and 4. The main effects of the childhood experience of hunger and caloric restriction of the respondent and spouse statistically increase food shares but these effects attenuate as net incomes increase. Table 5 OLS Regression of Food Share on Household Average of Average kcal/day, and at Least One Household Member Suffered from Hunger, Ages 0–16 Variables . Foodshare . Foodshare . log HH net income < median −0.236*** −0.048*** (0.070) (0.013) log HH net income ≥ median 0.028 −0.080*** (0.067) (0.012) (minus) average kcal/day age 0–16 0.486** (0.194) (minus) average kcal age 0–16 × loginc(lo), HH average −0.063** (0.026) (minus) average kcal age 0–16 × loginc(hi), HH average 0.042* (0.023) Hunger age 0–16 at least one HH member 0.493* (0.279) Hunger age 0–16 × loginc(lo), at least one HH member −0.067* (0.037) Hunger age 0–16 × loginc(hi), at least one HH member 0.017 (0.030) Constant 1.970*** 0.521*** (0.523) (0.092) Observations 943 943 R2 0.248 0.208 Variables . Foodshare . Foodshare . log HH net income < median −0.236*** −0.048*** (0.070) (0.013) log HH net income ≥ median 0.028 −0.080*** (0.067) (0.012) (minus) average kcal/day age 0–16 0.486** (0.194) (minus) average kcal age 0–16 × loginc(lo), HH average −0.063** (0.026) (minus) average kcal age 0–16 × loginc(hi), HH average 0.042* (0.023) Hunger age 0–16 at least one HH member 0.493* (0.279) Hunger age 0–16 × loginc(lo), at least one HH member −0.067* (0.037) Hunger age 0–16 × loginc(hi), at least one HH member 0.017 (0.030) Constant 1.970*** 0.521*** (0.523) (0.092) Observations 943 943 R2 0.248 0.208 Notes Standard errors are clustered on occupation zone‐month of birth level (column 1) and on the household level (column 2); ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, household size, years of education, dummies for medium and high childhood SES and a dummy for missing education. We additionally control for occupation zone dummies in column (1). Open in new tab Table 5 OLS Regression of Food Share on Household Average of Average kcal/day, and at Least One Household Member Suffered from Hunger, Ages 0–16 Variables . Foodshare . Foodshare . log HH net income < median −0.236*** −0.048*** (0.070) (0.013) log HH net income ≥ median 0.028 −0.080*** (0.067) (0.012) (minus) average kcal/day age 0–16 0.486** (0.194) (minus) average kcal age 0–16 × loginc(lo), HH average −0.063** (0.026) (minus) average kcal age 0–16 × loginc(hi), HH average 0.042* (0.023) Hunger age 0–16 at least one HH member 0.493* (0.279) Hunger age 0–16 × loginc(lo), at least one HH member −0.067* (0.037) Hunger age 0–16 × loginc(hi), at least one HH member 0.017 (0.030) Constant 1.970*** 0.521*** (0.523) (0.092) Observations 943 943 R2 0.248 0.208 Variables . Foodshare . Foodshare . log HH net income < median −0.236*** −0.048*** (0.070) (0.013) log HH net income ≥ median 0.028 −0.080*** (0.067) (0.012) (minus) average kcal/day age 0–16 0.486** (0.194) (minus) average kcal age 0–16 × loginc(lo), HH average −0.063** (0.026) (minus) average kcal age 0–16 × loginc(hi), HH average 0.042* (0.023) Hunger age 0–16 at least one HH member 0.493* (0.279) Hunger age 0–16 × loginc(lo), at least one HH member −0.067* (0.037) Hunger age 0–16 × loginc(hi), at least one HH member 0.017 (0.030) Constant 1.970*** 0.521*** (0.523) (0.092) Observations 943 943 R2 0.248 0.208 Notes Standard errors are clustered on occupation zone‐month of birth level (column 1) and on the household level (column 2); ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, household size, years of education, dummies for medium and high childhood SES and a dummy for missing education. We additionally control for occupation zone dummies in column (1). Open in new tab The major alternative hypothesis to the behavioural pathway emphasised in this article would be a biological pathway with the Barker hypothesis as the main biological mechanism highlighted in the literature (Barker, 1992, 2004). We provide several tests that are centred on distinguishing between a biological and behavioural pathway. The emphasis in the Barker hypothesis rests on in utero biological pathways from nutrition decrements experienced by the pregnant mother during famines and periods of low food availability which mothers then pass on to their foetus. Two of the most established consequences in later adult life are reduced height and lower cognition. In contrast, our effects of caloric rationing appear to have effects in all ages during childhood which argues against an exclusive Barker type biological pathway. For example, most adolescents (92% of them) who experienced WWII hunger in our sample did not also experience inter‐utero or early childhood hunger but still show significant long‐term effects in terms of behaviour. Second, an exclusive biological pathway during childhood should affect cognition. However, when we regress two measures of adult cognition (word recall and numeracy) on childhood hunger we find effects only in the 0–3 age group.18 Third, another possible biological pathway is through height. Once again, we only find a statistically significant effect of hunger on height for men when the hunger experience was during ages 0–3. Combined, these findings support an important biological pathway during ages 0–3, and not in the other childhood age groups. Finally, our effects are concentrated at the lowest adult incomes, a pathway that appears more behavioural than biological. Given the evidence of a behavioural effect of hunger, we show in the next subsection that food consumption is not only the outcome but serves as a channel through which the adverse childhood shock of hunger periods affects late‐life outcomes. Our hypothesis is that having experienced hunger has an effect on late‐life outcomes via food consumption – a behavioural channel. If this is correct, we would expect that the food share has an effect on health risks, once we control for hunger and income. 3.2. Early‐life Hunger Experiences and Adult Obesity To analyse whether the high food spending translates into higher weight, we estimate the probability of being obese, which is defined as a binary variable that takes the value one if a respondent has a body mass index (BMI) above 30, zero otherwise. Table 6 presents the results from an OLS estimation of the probability of being obese. Across the full set of childhood ages 0–16, the main effect of the experience of hunger is to raise the probability of later adult life obesity, an effect once again that attenuates as adult incomes rise. The narrow childhood age range models also indicate similar findings which are statistically significant in all three childhood age ranges. The higher the household’s income, the smaller the effect of the hunger experience on obesity. This obesity model in Table 6 includes measures of childhood SES so the hunger effect is independent of childhood SES. High childhood SES suffer less from obesity as adults even controlling for current income. Table 6 OLS Regression of Probability of Being Obese on Self‐reported Hunger, Splines (Median Split) Log Net HH Income and Interaction Terms, Ages 0–16, 0–3, 4–7 and 8–16 Variables . (1) . (2) . (3) . (4) . Pr(obesity) . Pr(obesity) . Pr(obesity) . Pr(obesity) . log HH net income (lo) −0.107 −0.126* −0.130* −0.103 (0.072) (0.070) (0.071) (0.072) log HH net income (hi) −0.118** −0.115*** −0.109** −0.126*** (0.046) (0.044) (0.045) (0.046) Hunger at age 0–16 3.814** (1.936) Hunger age 0–16 × log HH net income (lo) −0.497* (0.256) Hunger age 0–16 × log HH net income (hi) 0.028 (0.160) Hunger age 0–3 7.085** (3.079) Hunger age 0–3 × log HH net income (lo) −0.920** (0.419) Hunger age 0–3 × log HH net income (hi) −0.122 (0.343) Hunger at age 4–7 4.574* (2.652) Hunger age 4–7 × log HH net income (lo) −0.589* (0.351) Hunger age 4–7 × log HH net income (hi) −0.030 (0.207) Hunger at age 8–16 4.687** (2.091) Hunger age 8–16 × log HH net income (lo) −0.619** (0.276) Hunger age 8–16 × log HH net income (hi) 0.130 (0.202) Constant 1.228** 1.368*** 1.404*** 1.204** (0.531) (0.520) (0.523) (0.531) Observations 842 842 842 842 R2 0.057 0.057 0.056 0.056 Variables . (1) . (2) . (3) . (4) . Pr(obesity) . Pr(obesity) . Pr(obesity) . Pr(obesity) . log HH net income (lo) −0.107 −0.126* −0.130* −0.103 (0.072) (0.070) (0.071) (0.072) log HH net income (hi) −0.118** −0.115*** −0.109** −0.126*** (0.046) (0.044) (0.045) (0.046) Hunger at age 0–16 3.814** (1.936) Hunger age 0–16 × log HH net income (lo) −0.497* (0.256) Hunger age 0–16 × log HH net income (hi) 0.028 (0.160) Hunger age 0–3 7.085** (3.079) Hunger age 0–3 × log HH net income (lo) −0.920** (0.419) Hunger age 0–3 × log HH net income (hi) −0.122 (0.343) Hunger at age 4–7 4.574* (2.652) Hunger age 4–7 × log HH net income (lo) −0.589* (0.351) Hunger age 4–7 × log HH net income (hi) −0.030 (0.207) Hunger at age 8–16 4.687** (2.091) Hunger age 8–16 × log HH net income (lo) −0.619** (0.276) Hunger age 8–16 × log HH net income (hi) 0.130 (0.202) Constant 1.228** 1.368*** 1.404*** 1.204** (0.531) (0.520) (0.523) (0.531) Observations 842 842 842 842 R2 0.057 0.057 0.056 0.056 Notes Standard errors are clustered on the household level; ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, being in partnership, years of education, dummies for medium and high childhood SES and a dummy for missing education. Open in new tab Table 6 OLS Regression of Probability of Being Obese on Self‐reported Hunger, Splines (Median Split) Log Net HH Income and Interaction Terms, Ages 0–16, 0–3, 4–7 and 8–16 Variables . (1) . (2) . (3) . (4) . Pr(obesity) . Pr(obesity) . Pr(obesity) . Pr(obesity) . log HH net income (lo) −0.107 −0.126* −0.130* −0.103 (0.072) (0.070) (0.071) (0.072) log HH net income (hi) −0.118** −0.115*** −0.109** −0.126*** (0.046) (0.044) (0.045) (0.046) Hunger at age 0–16 3.814** (1.936) Hunger age 0–16 × log HH net income (lo) −0.497* (0.256) Hunger age 0–16 × log HH net income (hi) 0.028 (0.160) Hunger age 0–3 7.085** (3.079) Hunger age 0–3 × log HH net income (lo) −0.920** (0.419) Hunger age 0–3 × log HH net income (hi) −0.122 (0.343) Hunger at age 4–7 4.574* (2.652) Hunger age 4–7 × log HH net income (lo) −0.589* (0.351) Hunger age 4–7 × log HH net income (hi) −0.030 (0.207) Hunger at age 8–16 4.687** (2.091) Hunger age 8–16 × log HH net income (lo) −0.619** (0.276) Hunger age 8–16 × log HH net income (hi) 0.130 (0.202) Constant 1.228** 1.368*** 1.404*** 1.204** (0.531) (0.520) (0.523) (0.531) Observations 842 842 842 842 R2 0.057 0.057 0.056 0.056 Variables . (1) . (2) . (3) . (4) . Pr(obesity) . Pr(obesity) . Pr(obesity) . Pr(obesity) . log HH net income (lo) −0.107 −0.126* −0.130* −0.103 (0.072) (0.070) (0.071) (0.072) log HH net income (hi) −0.118** −0.115*** −0.109** −0.126*** (0.046) (0.044) (0.045) (0.046) Hunger at age 0–16 3.814** (1.936) Hunger age 0–16 × log HH net income (lo) −0.497* (0.256) Hunger age 0–16 × log HH net income (hi) 0.028 (0.160) Hunger age 0–3 7.085** (3.079) Hunger age 0–3 × log HH net income (lo) −0.920** (0.419) Hunger age 0–3 × log HH net income (hi) −0.122 (0.343) Hunger at age 4–7 4.574* (2.652) Hunger age 4–7 × log HH net income (lo) −0.589* (0.351) Hunger age 4–7 × log HH net income (hi) −0.030 (0.207) Hunger at age 8–16 4.687** (2.091) Hunger age 8–16 × log HH net income (lo) −0.619** (0.276) Hunger age 8–16 × log HH net income (hi) 0.130 (0.202) Constant 1.228** 1.368*** 1.404*** 1.204** (0.531) (0.520) (0.523) (0.531) Observations 842 842 842 842 R2 0.057 0.057 0.056 0.056 Notes Standard errors are clustered on the household level; ***p < 0.01, **p < 0.05, *p < 0.1. We control for age, age², gender, born in rural/urban region, being in partnership, years of education, dummies for medium and high childhood SES and a dummy for missing education. Open in new tab When we add a measure of food share to the model in Table 6, the estimated effects of hunger diminishes. The results provide an important implication. An adverse hunger shock seems not to only affect health outcomes when the individual is still in utero (Barker, 1992; Lumey and Stein, 1997). Instead, the hunger experiences made during the whole age of childhood seems to have negative consequences on late‐life health. In particular, individuals who have suffered from hunger during adolescence show worse health outcomes later in life. 4. Conclusion In this study, we show that an adverse life event during childhood affects not only adult health outcomes but also individuals’ behaviour at older ages (and presumably over the whole life cycle). While the health effects of shocks in utero and at various stages of childhood on adult health are well established, most of the existing literature focused on biological channels, with some recent research also investigating the effects of shocks on cognitive skills. Our results suggest another causal link: retrospective survey data on hunger experiences in post‐war Germany, combined with administrative data on food supply (caloric rations) during those times and detailed data on adult outcomes, show that relatively short periods of severe hunger affect not only health outcomes of older individuals (higher body weight and higher rates of obesity) but also food consumption patterns. Our results further show that the behavioural effects are not limited to in utero or very early years of childhood but are present at all childhood ages, consistent with a later‐life behavioural pathway. This suggests that policy interventions focusing on this group of children might be particularly useful. This complements existing research that stressed biological channels for which the most sensitive periods of childhood are much earlier. If the pathways between early‐life shocks and late‐life outcomes are not only biological but also behavioural, then there are ampler possibilities to counteract these pathways. We also contribute to the literature on endogenous preference formation. Our finding that preferences are not only influenced by preferences of parents or role models (Dohmen et al., 2011) but also by large shocks experienced during childhood and youth, provides a complementary explanation for a correlation of preferences between generations. Perhaps more importantly, this result further strengthens the case for interventions in early childhood and adolescence (Heckman, 2012). Footnotes 1 " Several papers use retrospective data on childhood circumstances and adult outcomes in SHARELIFE to study long‐run effects of early‐life shocks across Europe (Van den Berg et al., 2011; Jürges, 2013; Halmdienst and Winter‐Ebmer, 2014). None of these papers or our own earlier research (Kesternich et al., 2014) consider the behavioural channel analysed in this article. 2 " Some of the decrease was due to productive capacity being channelled into war production and to men being absent (this work was done often by elderly women and prisoners of war or forced labourers). 3 " The first hunger oedema was reported in the summer of 1945 (Farquharson, 1985). 4 " Germans living in these regions, mainly farmers, were forced to move westwards. While inhabitants of other parts of Poland and the Czech Republic were moved there and took over the farms, production after the war was only at about 50% of what had been produced before (Rothenberger, 1980). 5 " In the British occupation zone, 1,000 out of 13,000 km of railway tracks were operational in spring 1945. 6 " There were some attempts of the British zone to trade steel against food produced in the Soviet zone but largely these attempts failed (Farquharson, 1985). The French saw their occupation zone as a separate entity so that the economic relationships with the other zones were cut to a large extent. 7 " The state of Baden‐Wuerttemberg was split up between the US zone and the French zone. Since about two‐thirds of the territory and the state’s largest cities fall in the US zone, we assign all respondents from Baden‐Wuerttemberg to the US zone. 8 " The ability to remember events during the 0–3 age groups is a legitimate question. But it is important to note that salient events that happen between ages 0–3, especially of the magnitude of which we are discussing also become part of family lore and tend to be frequently discussed and are at least in part remembered due to frequent family conversations about these events. 9 " The information in the life history includes family composition and type of home (number of rooms, running water, toilet, etc.), number of books, and occupation of father. These measures were used to create an index of childhood SES at age 10 based on Mazzonna (2014). 10 " We also tested whether number of siblings or being male affected reports of hunger interacted with caloric restrictions but found no effect. 11 " Official caloric rations do provide inter‐individual variation in caloric rations at the occupation zone and month of birth level. 12 " Individuals born before 1929 might have also been affected by WWI or the world economic crisis and thus show a differential food consumption behaviour. 13 " The trimming of the distributions guarantees that no implausible shares are left in our data. Such values occur if respondents report, for example, yearly instead of monthly food expenditures or income values. 14 " To do IV, we need to instrument a non‐linear function of income and hunger. However, our first stage results point towards weak instruments in that the ‘F’ statistics in the first stage are often below 10. Thus, we prefer not to use IV even though we get significant results for age groups 0–16 and 4–7 in the second stage. 15 " We control for age, age², gender, born in rural/urban region, household size, years of education, dummies for medium and high childhood SES and a dummy for missing education. 16 " To test the influence of outliers, we also ran a set of median regressions for our hunger and kcal models. The median regression results were quite similar to those contained in the article. 17 " In these narrow childhood models, the alternative to not experiencing hunger within a specific narrow age range includes the experience of hunger in another childhood age range as well as no experience of hunger at all during childhood. When we estimated models where the alternative to experience of hunger within a narrow age range was only no experience of hunger at all during childhood, we obtained results similar to those reported in the text. There is very little overlap in the experience of hunger in the 0–3 and 8–16 age groups given the long number of years between them. 18 " The estimated effects of hunger in ages 0–3 on word recall is −0.758* and on numeracy is −0.531** where the stars have the same meaning as in the regression Tables. There are no statistically significant negative effects in either the 4–7 or 8–16 age groups. Word recall is the average recall of an immediate and delayed recall of 10 words. Numeracy is based on four arithmetic questions and the score is based on the number of correct answers. References Almond , D. and Currie , J. ( 2011 ). ‘ Killing me softly: the fetal origins hypothesis ’, Journal of Economic Perspectives , vol. 25 ( 3 ), pp. 153 – 72 . Google Scholar Crossref Search ADS PubMed WorldCat Barker , D. ( 1992 ). Fetal and Infant Origins of Adult Disease , London : BMJ Publishing Group . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Barker , D. 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Blume, eds.), The New Palgrave Dictionary of Economics , Palgrave Macmillan. The New Palgrave Dictionary of Economics Online, Palgrave Macmillan. doi: 10.1057/9780230226203.0476. OpenURL Placeholder Text WorldCat Lewbel , A. ( 2010 ). ‘ Shape‐invariant demand functions ’, Review of Economics and Statistics , vol. 92 ( 3 ), pp. 549 – 56 . Google Scholar Crossref Search ADS WorldCat Liebe , H. ( 1947 ). ‘Drei Grundprobleme der deutschen Wirtschaft’, in ( Deutsches Institut für Wirtschaftsforschung , ed.), Die deutsche Wirtschaft zwei Jahre nach dem Zusammenbruch. Tatsachen und Probleme , pp. 72 – 103 , Berlin : Nauck . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Lumey , L. and Stein , A. ( 1997 ). ‘ In utero exposure to famine and subsequent fertility: the Dutch Famine Birth Cohort Study ’, American Journal of Public Health , vol. 87 ( 12 ), pp. 1962 – 6 . Google Scholar Crossref Search ADS PubMed WorldCat Malmendier , U. and Nagel , S. ( 2011 ). ‘ Depression babies: do macroeconomic experiences affect risk taking? ’, Quarterly Journal of Economics , vol. 126 ( 1 ), pp. 373 – 416 . Google Scholar Crossref Search ADS WorldCat Mazzonna , F. ( 2014 ). ‘ The long‐lasting effects of family background: a European cross‐country comparison ’, Economics of Education Review , vol. 40 ( C ), pp. 25 – 42 . Google Scholar Crossref Search ADS WorldCat Rothenberger , K. ( 1980 ). Die Hungerjahre nach dem Zweiten Weltkrieg. Ernaehrung und Landwirtschaft in Rheinland‐Pfalz 1945‐1950 , Berlin : Boldt Verlag . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Schlange‐Schoeningen , H. ( 1955 ). Im Schatten des Hungers. Dokumentarisches zur Ernaehrungspolitik und Ernaehrungswirtschaft in den Jahren 1945–1949 , Berlin : P. Parey . Google Scholar Google Preview OpenURL Placeholder Text WorldCat COPAC Schwarzer , O. ( 1995 ). ‘ Der Lebensstandard in der SBZ/DDR 1945‐1989 ’, Jahrbuch für Wirtschaftsgeschichte , vol. 1995 ( 2 ), pp. 119 – 46 . OpenURL Placeholder Text WorldCat Smith , J.P. ( 1999 ). ‘ Healthy bodies and thick wallets ’, Journal of Economic Perspectives , vol. 13 ( 2 ), pp. 145 – 66 . Google Scholar Crossref Search ADS WorldCat Van den Berg , G. , Pinger , P. and Schoch , J. ( 2011 ). ‘ Instrumental variable estimation of the causal effect of hunger early in life on health later in life ’, IZA Working Paper No. 6110. Author notes " This article uses data from SHARELIFE release 1, as of 24 November 2010, SHARE waves 1 and 2 release 2.6.0, as of 29 November 2013 and SHARE wave 4 release 1.1.1, as of 28 March 2013. The SHARE data collection has been primarily funded by the European Commission through the 5th framework and 6th framework programme. SHARELIFE was supported through the 7th framework programme. Additional funding from the US National Institute on Aging as well as from various national sources is gratefully acknowledged. Kesternich recognises funding by the DFG through SFB‐Transregio 15 and Smith through NIA. Gracia Brückmann provided excellent research assistance. © 2015 Royal Economic Society

Priks,, Mikael

doi: 10.1111/ecoj.12327pmid: N/A

Abstract I study the effects of surveillance cameras on crime in the Stockholm subway system. Beginning in 2006, surveillance cameras were installed in subway stations at different points in time. Difference‐in‐difference analysis reveals that introduction of the cameras reduced crime by approximately 25% at stations in the city centre. The types of crimes deterred by cameras are planned crime, that is, pickpocketing and robbery. It is also shown that some of the crimes were displaced to surrounding areas. The cost of preventing one crime by the use of surveillance cameras is approximately US$ 2,000. Surveillance cameras have become a common method to combat crime. In the UK alone, an estimated 4 million cameras have been installed (Associated Press, 2007). There is a major concern, however, regarding their intrusion upon privacy. To motivate the use of surveillance cameras, it is therefore important to begin by carefully studying the extent to which cameras deter crime. Here, I exploit the fact that surveillance cameras were introduced in the Stockholm subway system at different points in time during the period 2006–8. Surveillance cameras were found to reduce the overall crime rate by approximately 25% at stations in the city centre. Such a station recorded on average approximately 11 crimes per month before introduction of the cameras. The reduction therefore amounts to almost three fewer crimes per station and month. The effect was immediate, which indicates that it was due to deterrence, and lasting. The analysis also shows that the cameras did not deter crime in the periphery. I also had access to data on crime in the areas adjacent to the subway stations. The results indicate that 15% of the deterred crimes appear to have been displaced to the area surrounding the stations where cameras were not used. A cost‐benefit analysis reveals that surveillance cameras annually deter approximately 575 crimes, 75 of which are displaced to places nearby, at a cost of US$ 1,000,000. Hence, the cost of preventing one crime is estimated to be approximately US$ 2,000. In a standard economics model, criminals receive utility from committing a crime and disutility from getting caught, which depends on the monitoring technology as well as the extent to which criminals care about this cost. This implies that some types of crimes should be more sensitive to camera surveillance than others. Criminals who commit planned crimes, such as professional pickpockets and robbers, are likely to be observant to signs displaying surveillance cameras not only because they tend to be cautious but also because the cameras constitute a large threat ex post when victims report a felony. On the other hand, criminals involved in drug‐related crimes (drug dealing, possession and use) may be under the influence of drugs and therefore less cautious. In such instances, there are also normally no victims involved who would call for the assistance of camera surveillance in a prosecution. Crimes that are committed in the heat of the moment, such as assault, should also be less sensitive to signs displaying surveillance cameras. The results are in line with these predictions. Planned types of crime were reduced to a large extent (pickpocketing by 20% and robbery by 60%) but drug‐related crime and assaults were unaffected by the cameras. Moreover, 15% of the deterred pickpocketing incidents were displaced to the adjacent area and, as expected, drug‐related crime and assaults outside stations were unaffected by the cameras. Why, then, do cameras tend to deter planned crime in the city but not in the periphery? Since organised gangs prey in stations in the city where there are many victims (pickpocketing constitutes 16% of crime at city stations and only 8% elsewhere), deterrent effects there are to be expected. Moreover, since guards and police officers patrol closer to the stations in the city as compared to the suburbs, cameras should be relatively efficient in the city in the sense that law enforcement officials can use them for a rapid response by guards and police. In the suburbs, this process takes more time, so that criminals have more leeway to escape. I am not able to discriminate between these two different hypotheses, however. A few studies have examined the effects of cameras in subway stations; see Burrows (1980), Webb and Laycock (1992), and Grandmaison and Tremblay (1997). However, in the first two studies, the installation of cameras was accompanied by other interventions, such as passenger alarms and mirrors, and in the last two there were no signs to signal the presence of cameras. Grandmaison and Tremblay (1997) study a pilot project in Montreal where 13 out of 54 subway stations were selected for the project. This selection was not random and large stations with considerable crime were overrepresented. Apart from Webb and Laycock (1992), who show a temporary effect of cameras on robbery, this literature does not find that cameras have any deterrent effects. Another aspect of the literature examines the effects of surveillance cameras on crime in more general terms. King et al. (2008) evaluate a programme where surveillance cameras were introduced on the streets in San Francisco. Interestingly, they too find that the cameras reduced property crimes by approximately 20% and that violent crime was unaffected by the introduction of cameras. Priks (2014) shows that surveillance cameras reduce unruly behaviour inside soccer stadiums. Welsh and Farrington (2003), and Welsh and Farrington (2009) report evidence from a number of studies analysing the effects of cameras on street crime, burglary and auto theft in public areas. These latter studies use before‐and‐after measures of crime and mostly comparable control areas but they tend to suffer from the fact that either the installation of surveillance cameras was potentially endogenous to previous crime,1 or that several types of interventions were introduced simultaneously, or both. Setting the identification problems aside, the overall result from this literature indicates that cameras deter property crime in parking lots only.2 This literature also reveals no or small displacement effects (Welsh and Farrington, 2003; Gill and Spriggs, 2005; Waples et al., 2009).3 In this article, I used placebo treatments for the time periods before the cameras were installed and found no evidence of significant changes in crime prior to the installation of cameras. This, in combination with the fact that the introduction of surveillance cameras was the only policy intervention, allows me to address the deterrent effect of the cameras. The outline is as follows. Section 1 describes the data. Section 2 reports the empirical strategy and results. Section 3 analyses displacement effects. Section 4 provides a discussion. 1. Data The dates of installation of the cameras were obtained from the Stockholm Public Transit Authority (Storstockholms Lokaltrafik (SL)). SL is owned by the Stockholm County Council. It operates parts of the public transport system in Stockholm County and is responsible for selling the rights for private firms to operate other parts of the system, such as the subway network. Prior to 2006, there were no surveillance cameras in the subway stations. Towards the end of 2006 and continuing through 2007 and 2008, SL installed surveillance cameras in all of the stations. According to Swedish law, the use of surveillance cameras has to be clearly indicated. Signs are displayed at the entrances to every subway stations as well as on the platforms, next to the signs displaying the direction of the trains. SL operates a call centre where passengers and the public can phone in and provide information about ongoing crime. This centre, which was already in place prior to introduction of the cameras, is manned by three officers at all times. Following a phone call, the officers can use the cameras in real time to order guards to the crime scenes. According to the employees at SL in charge of the operation, there was no concurrent joint project and the introduction of cameras was not prompted by a rise in crime.4 The main purpose was instead to increase the passengers’ perception of safety partly by enhancing fire safety.5 The installations therefore began in some underground stations with only one exit. After this was completed, SL did not request any particular order. However, the order of introduction was to some extent influenced by the exogenous circumstance that the application time for permits to use cameras varied (from 48 to 184 days). A potential concern might be that the order of the introduction was somehow released in the media and that criminals could thereby take extra precautions in advance. But according to the employee in charge of the installations, Mats Lönn, the list was secret except for some suppliers of goods that were informed. Another aspect is that criminals could observe employees as they installed the cameras. But this process only took between a few days and, in rare cases, a couple of weeks, so it should not substantially influence the analysis. I used daily data from January 1, 2004 to December 31, 2009. I had access to the exact dates of installation in all 100 stations, apart from the two suburb stations Gubbängen and Axelsberg and the city station Östermalmstorg, which I therefore excluded. Figure 1 is a map of the Stockholm subway system. As in many other cities, it is characterised by some very large stations in the city centre, which serve as nodes for several lines, and many much smaller stations in the suburbs which are served by only one line. The branches of all three lines pass through the central station, T‐Centralen, which is by far the largest station both in terms of crime and the number of passengers. I define stations within the major junctions Fridhemsplan, Östermalmstorg, Gullmarsplan and Liljeholmen as city stations.6 Fig. 1. Open in new tabDownload slide The Stockholm Subway System Fig. 1. Open in new tabDownload slide The Stockholm Subway System Figure 2 illustrates the distribution of the timing for introduction of the cameras. It shows that surveillance cameras tended to be installed somewhat earlier in the city as compared to the suburbs. On the other hand, the largest station (T‐Centralen) was not among the early stations (cameras were installed in February 2007) and the third largest station in terms of number of passengers (Fridhemsplan) had cameras installed as late as January 2008. Fig. 2. Open in new tabDownload slide Timing of the Installation of Surveillance Cameras Fig. 2. Open in new tabDownload slide Timing of the Installation of Surveillance Cameras Data on crime were obtained from the Swedish National Police Force and refer to all crimes filed containing words related to ‘subway station’ during the period under study. I have coded crimes that according to the police took place outside the entrances separately. To do this consistently, I scrutinised the data set manually and coded the observations as taking place outside the station if one of the following words were included: outside, parking lot, bicycle stand, close to, next to, by, and bus stop or if it was otherwise clear that the crime took place in the vicinity of the station. Apart from isolating the effect inside stations, this allows me to study displacement effects. The types of crime are coded in a very detailed way. The data set obtained covers 258 types of crime in the subway stations. When grouped together into categories, the most common types of crime in the subway are drug‐related incidents (17%), assault (16%), pickpocketing (12%) and violence against officials (12%).7 Table 1 shows the summary statistics for crime in the city centre and outside the city centre as well as crime inside and outside the stations and the number of passengers. Table 1 Summary Statistics . Mean . SD . Minimum . Maximum . Number of observations . Crime if city = 1 and camera = 0 0.37 1.14 0 29 19,709 Crime if city = 1 and camera = 1 0.37 1.21 0 25 17,555 Crime if city = 0 and camera = 0 0.06 0.39 0 22 104,856 Crime if city = 0 and camera = 1 0.09 0.52 0 16 70,504 Passengers if city = 1 and camera = 0 31,904 33,864 6,000 155,000 19,709 Passengers if city = 1 and camera = 1 32,390 35,903 6,000 163,900 17,555 Passengers if city = 0 and camera = 0 5,360 3,662 1,000 21,000 104,856 Passengers if city = 0 and camera = 1 6,025 4,079 1,000 25,200 70,504 Crime per passenger if city = 1 and camera = 0 0.11 0.48 0 29 19,709 Crime per passenger if city = 1 and camera = 1 0.13 0.57 0 22 17,555 Crime per passenger if city = 0 and camera = 0 0.13 0.93 0 54 104,856 Crime per passenger if city = 0 and camera = 1 0.17 1.18 0 48 70,504 Pickpocketing per passenger if city = 1 and camera = 0 0.017 0.093 0 1.65 19,709 Pickpocketing per passenger if city = 1 and camera = 1 0.013 0.091 0 2.77 17,555 Pickpocketing per passenger if city = 0 and camera = 0 0.009 0.147 0 9.23 104,856 Pickpocketing per passenger if city = 0 and camera = 1 0.011 0.168 0 9.60 70,504 Crime per passenger outside stations if city = 1 and camera = 0 0.003 0.054 0 2.77 19,709 Crime per passenger outside stations if city = 1 and camera = 1 0.003 0.061 0 3.29 17,555 Crime per passenger outside stations if city = 0 and camera = 0 0.009 0.210 0 16.22 96,364 Crime per passenger outside stations if city = 0 and camera = 1 0.005 0.140 0 9.88 63,652 . Mean . SD . Minimum . Maximum . Number of observations . Crime if city = 1 and camera = 0 0.37 1.14 0 29 19,709 Crime if city = 1 and camera = 1 0.37 1.21 0 25 17,555 Crime if city = 0 and camera = 0 0.06 0.39 0 22 104,856 Crime if city = 0 and camera = 1 0.09 0.52 0 16 70,504 Passengers if city = 1 and camera = 0 31,904 33,864 6,000 155,000 19,709 Passengers if city = 1 and camera = 1 32,390 35,903 6,000 163,900 17,555 Passengers if city = 0 and camera = 0 5,360 3,662 1,000 21,000 104,856 Passengers if city = 0 and camera = 1 6,025 4,079 1,000 25,200 70,504 Crime per passenger if city = 1 and camera = 0 0.11 0.48 0 29 19,709 Crime per passenger if city = 1 and camera = 1 0.13 0.57 0 22 17,555 Crime per passenger if city = 0 and camera = 0 0.13 0.93 0 54 104,856 Crime per passenger if city = 0 and camera = 1 0.17 1.18 0 48 70,504 Pickpocketing per passenger if city = 1 and camera = 0 0.017 0.093 0 1.65 19,709 Pickpocketing per passenger if city = 1 and camera = 1 0.013 0.091 0 2.77 17,555 Pickpocketing per passenger if city = 0 and camera = 0 0.009 0.147 0 9.23 104,856 Pickpocketing per passenger if city = 0 and camera = 1 0.011 0.168 0 9.60 70,504 Crime per passenger outside stations if city = 1 and camera = 0 0.003 0.054 0 2.77 19,709 Crime per passenger outside stations if city = 1 and camera = 1 0.003 0.061 0 3.29 17,555 Crime per passenger outside stations if city = 0 and camera = 0 0.009 0.210 0 16.22 96,364 Crime per passenger outside stations if city = 0 and camera = 1 0.005 0.140 0 9.88 63,652 Notes The unit of analysis is days for crime and years for passengers. Crime per passenger and pickpocketing per passenger are multiplied by 10,000. Open in new tab Table 1 Summary Statistics . Mean . SD . Minimum . Maximum . Number of observations . Crime if city = 1 and camera = 0 0.37 1.14 0 29 19,709 Crime if city = 1 and camera = 1 0.37 1.21 0 25 17,555 Crime if city = 0 and camera = 0 0.06 0.39 0 22 104,856 Crime if city = 0 and camera = 1 0.09 0.52 0 16 70,504 Passengers if city = 1 and camera = 0 31,904 33,864 6,000 155,000 19,709 Passengers if city = 1 and camera = 1 32,390 35,903 6,000 163,900 17,555 Passengers if city = 0 and camera = 0 5,360 3,662 1,000 21,000 104,856 Passengers if city = 0 and camera = 1 6,025 4,079 1,000 25,200 70,504 Crime per passenger if city = 1 and camera = 0 0.11 0.48 0 29 19,709 Crime per passenger if city = 1 and camera = 1 0.13 0.57 0 22 17,555 Crime per passenger if city = 0 and camera = 0 0.13 0.93 0 54 104,856 Crime per passenger if city = 0 and camera = 1 0.17 1.18 0 48 70,504 Pickpocketing per passenger if city = 1 and camera = 0 0.017 0.093 0 1.65 19,709 Pickpocketing per passenger if city = 1 and camera = 1 0.013 0.091 0 2.77 17,555 Pickpocketing per passenger if city = 0 and camera = 0 0.009 0.147 0 9.23 104,856 Pickpocketing per passenger if city = 0 and camera = 1 0.011 0.168 0 9.60 70,504 Crime per passenger outside stations if city = 1 and camera = 0 0.003 0.054 0 2.77 19,709 Crime per passenger outside stations if city = 1 and camera = 1 0.003 0.061 0 3.29 17,555 Crime per passenger outside stations if city = 0 and camera = 0 0.009 0.210 0 16.22 96,364 Crime per passenger outside stations if city = 0 and camera = 1 0.005 0.140 0 9.88 63,652 . Mean . SD . Minimum . Maximum . Number of observations . Crime if city = 1 and camera = 0 0.37 1.14 0 29 19,709 Crime if city = 1 and camera = 1 0.37 1.21 0 25 17,555 Crime if city = 0 and camera = 0 0.06 0.39 0 22 104,856 Crime if city = 0 and camera = 1 0.09 0.52 0 16 70,504 Passengers if city = 1 and camera = 0 31,904 33,864 6,000 155,000 19,709 Passengers if city = 1 and camera = 1 32,390 35,903 6,000 163,900 17,555 Passengers if city = 0 and camera = 0 5,360 3,662 1,000 21,000 104,856 Passengers if city = 0 and camera = 1 6,025 4,079 1,000 25,200 70,504 Crime per passenger if city = 1 and camera = 0 0.11 0.48 0 29 19,709 Crime per passenger if city = 1 and camera = 1 0.13 0.57 0 22 17,555 Crime per passenger if city = 0 and camera = 0 0.13 0.93 0 54 104,856 Crime per passenger if city = 0 and camera = 1 0.17 1.18 0 48 70,504 Pickpocketing per passenger if city = 1 and camera = 0 0.017 0.093 0 1.65 19,709 Pickpocketing per passenger if city = 1 and camera = 1 0.013 0.091 0 2.77 17,555 Pickpocketing per passenger if city = 0 and camera = 0 0.009 0.147 0 9.23 104,856 Pickpocketing per passenger if city = 0 and camera = 1 0.011 0.168 0 9.60 70,504 Crime per passenger outside stations if city = 1 and camera = 0 0.003 0.054 0 2.77 19,709 Crime per passenger outside stations if city = 1 and camera = 1 0.003 0.061 0 3.29 17,555 Crime per passenger outside stations if city = 0 and camera = 0 0.009 0.210 0 16.22 96,364 Crime per passenger outside stations if city = 0 and camera = 1 0.005 0.140 0 9.88 63,652 Notes The unit of analysis is days for crime and years for passengers. Crime per passenger and pickpocketing per passenger are multiplied by 10,000. Open in new tab Figure 3 plots crime in 2004 and month of installation in the city centre (starting in September 2006). In line with the information provided by SL officials, there is no correlation between installation time and high‐crime stations. Fig. 3. Open in new tabDownload slide Crime in 2004 and Dates of Installation in the City Note. The outlier is the central station where more crimes are committed compared to the other stations in the city. Fig. 3. Open in new tabDownload slide Crime in 2004 and Dates of Installation in the City Note. The outlier is the central station where more crimes are committed compared to the other stations in the city. Figure 4 shows the overall level of crime per day in the subway stations on a monthly basis. According to statistics from SL, the number of passengers declines during the summer. There are 15% fewer passengers as compared to the average in June, 30% fewer passengers in July, and 20% fewer passengers in August. The Figure shows a pattern whereby crime follows these fluctuations. The crime level is quite low in the summer, particularly in July. There is also an increase in crime towards the end of 2008. Fig. 4. Open in new tabDownload slide Crime in the Stockholm Subway Fig. 4. Open in new tabDownload slide Crime in the Stockholm Subway 2. Method and Results I began by estimating the effects of cameras in the subway system as a whole and then in the city separately. Let Yit denote the number of reported crimes per passenger at station i in period t, where days is used as the unit of analysis.8 I ran the following OLS regression: Yit=αi+βcamerait+θt+ωit+vit,(1) where αi is a station fixed effect. Camera equals 1 for days when cameras were installed and 0 otherwise. Parameter β measures the effect of having cameras in the areas studied (the whole subway system or in the city). Parameter θt denotes time‐specific (year or day by year) fixed effects in period t. This is a difference‐in‐difference design that allows me to identify the effects of cameras on crime. In some specifications, I also allow for station‐specific linear trends ωit ⁠. Adding these trends is essentially a type of regression discontinuity design, with time as the ‘running variable’, which allows a study of the jump at the time of introduction of cameras. In the baseline specifications, all stations are equally accounted for independently of their size. In some specifications, I weighted the observations by the number of passengers per station.9 Standard errors are clustered by the station in all specifications. I also ran the following OLS equation using the whole data set assuming that time trends in the city and outside the city were the same: Yit=αi+βcamerait+γcamerait×cityt+θt+ωit+vit.(2) City equals 1 if the station is defined as located in the city and 0 otherwise. Parameter β measures the effect of having cameras at the 80 stations that are not included in the city sample. β + γ measures the effect of surveillance cameras on crime at the 17 stations included in the city sample. In order to study trends, the break at the time of introduction and possible dynamic effects, I also performed an event time study where I ran a similar regression as in (1) except that camerait was divided into monthly event time dummy variables ∑τ=−TTβτcameraiτ ⁠. The event time indicator variables track the month when cameras were introduced in one of the stations and the months prior and subsequent to the introduction. Table 2 reports the main results. Columns 1 and 2 show that there is no general effect of surveillance cameras on crime in the subway system as a whole. Columns 3–6 present the results from regressions where the sample is the city centre. Column 3 reports the results with year fixed effects and the other columns day by year fixed effects. Column 5 reports the results when station‐specific linear trends are added and in Column 6 the observations are weighted by the number of passengers per station. The estimated effect of the cameras on crime in the city is large and highly significant in all specifications. Column 7 reports results from an interaction model where the whole data set is included. Column 8 reports results from the same regression with station‐specific trends. The F‐test of the joint significance of the variable camera and the interaction variable camera × city shows that the result is significant in both specifications.10 The average number of crimes per day and passenger (multiplied by 10,000) before the introduction was 0.11. Using the identical estimated effects from the specifications in columns 4 and 5, −0.029, the introduction of cameras reduced crime in subway stations in the city by approximately 25%. Since an average station in the city had approximately 135 crimes per year before cameras, the reduction amounts to almost 34 crimes per station and year. Table 2 Surveillance Cameras and Crime in the Subway Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Camera −0.006 0.003 −0.034** −0.029** −0.029** −0.015* 0.013 0.022 (0.010) (0.013) (0.012) (0.011) (0.012) (0.007) (0.015) (0.015) Camera × city −0.028* −0.037*** (0.016) (0.012) Station‐specific linear trends No No No No Yes No No Yes Year fixed effects Yes No Yes No No No No No Day by year fixed effects No Yes No Yes Yes Yes Yes Yes Obervations weighted by passengers No No No No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 4.34 2.89 (0.04) (0.09) R 2 0.00 0.02 0.01 0.07 0.07 0.08 0.02 0.02 Observations 212,624 212,624 37,264 37,264 37,264 37,264 212,624 212,624 Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Camera −0.006 0.003 −0.034** −0.029** −0.029** −0.015* 0.013 0.022 (0.010) (0.013) (0.012) (0.011) (0.012) (0.007) (0.015) (0.015) Camera × city −0.028* −0.037*** (0.016) (0.012) Station‐specific linear trends No No No No Yes No No Yes Year fixed effects Yes No Yes No No No No No Day by year fixed effects No Yes No Yes Yes Yes Yes Yes Obervations weighted by passengers No No No No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 4.34 2.89 (0.04) (0.09) R 2 0.00 0.02 0.01 0.07 0.07 0.08 0.02 0.02 Observations 212,624 212,624 37,264 37,264 37,264 37,264 212,624 212,624 Notes *** indicates significance at the 1% level, ** at the 5% level, and * at the 10% level. The regresssions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1, 2, 7 and 8 include the whole data set. Open in new tab Table 2 Surveillance Cameras and Crime in the Subway Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Camera −0.006 0.003 −0.034** −0.029** −0.029** −0.015* 0.013 0.022 (0.010) (0.013) (0.012) (0.011) (0.012) (0.007) (0.015) (0.015) Camera × city −0.028* −0.037*** (0.016) (0.012) Station‐specific linear trends No No No No Yes No No Yes Year fixed effects Yes No Yes No No No No No Day by year fixed effects No Yes No Yes Yes Yes Yes Yes Obervations weighted by passengers No No No No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 4.34 2.89 (0.04) (0.09) R 2 0.00 0.02 0.01 0.07 0.07 0.08 0.02 0.02 Observations 212,624 212,624 37,264 37,264 37,264 37,264 212,624 212,624 Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . Camera −0.006 0.003 −0.034** −0.029** −0.029** −0.015* 0.013 0.022 (0.010) (0.013) (0.012) (0.011) (0.012) (0.007) (0.015) (0.015) Camera × city −0.028* −0.037*** (0.016) (0.012) Station‐specific linear trends No No No No Yes No No Yes Year fixed effects Yes No Yes No No No No No Day by year fixed effects No Yes No Yes Yes Yes Yes Yes Obervations weighted by passengers No No No No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 4.34 2.89 (0.04) (0.09) R 2 0.00 0.02 0.01 0.07 0.07 0.08 0.02 0.02 Observations 212,624 212,624 37,264 37,264 37,264 37,264 212,624 212,624 Notes *** indicates significance at the 1% level, ** at the 5% level, and * at the 10% level. The regresssions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1, 2, 7 and 8 include the whole data set. Open in new tab Table 3 reports results for planned crimes that involve victims (pickpocketing and robbery). I first used year fixed effects reported in column 1 and then day by year fixed effects. In column 3, the observations are weighted by passengers. Columns 4 and 5 show results from regressions using the full sample. In column 5, station‐specific linear trends are also included. All evidence point to the fact that cameras reduce pickpocketing. Using the identical estimates from specifications reported in columns 1, 2 and 3, pickpocketing was reduced by approximately 23% compared to the average of 0.017 without cameras in the city. Specifications 6–10 report the effects on robbery. While robberies are usually very severe, they are also very rare crimes (there are 271 incidents in the city centre sample). This result should therefore be interpreted with considerable caution. When the city centre sample is used, cameras significantly reduced robbery (specifications 6 and 7; specification 8 is significant just below the 10% level). However, the result is not robust to using the interaction model (specifications 9 and 10). The size of the effects varies and amounts to, on average, reductions of approximately 60%. Table 3 Surveillance Cameras and Planned Crime with Victims Dependent variables: columns (1–5) pickpocketing/passenger, columns (6–10) robbery/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.004* −0.004 −0.004*** 0.001 0.002 −0.002* −0.003** −0.001 −0.001 −0.001 (0.002) 0.002 0.001 (0.002) (0.002) (0.001) (0.001) (0.001) (0.001) (0.001) Camera × city −0.007** −0.006*** 0.000 0.001 (0.003) (0.002) (0.001) (0.001) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 16.71 13.45 1.00 0.00 (0.00) (0.00) (0.32) (0.95) R 2 0.01 0.07 0.09 0.02 0.02 0.00 0.06 0.05 0.01 0.01 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Dependent variables: columns (1–5) pickpocketing/passenger, columns (6–10) robbery/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.004* −0.004 −0.004*** 0.001 0.002 −0.002* −0.003** −0.001 −0.001 −0.001 (0.002) 0.002 0.001 (0.002) (0.002) (0.001) (0.001) (0.001) (0.001) (0.001) Camera × city −0.007** −0.006*** 0.000 0.001 (0.003) (0.002) (0.001) (0.001) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 16.71 13.45 1.00 0.00 (0.00) (0.00) (0.32) (0.95) R 2 0.01 0.07 0.09 0.02 0.02 0.00 0.06 0.05 0.01 0.01 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Notes ***Indicates significance at the 1% level, ** at the 5% level, and * at the 10% level. The regressions include station fixed effects and standard errors are clustered at the level of the stations. The specifications in columns 1–3 and 6–8 include stations in the city and the specifications in columns 4, 5, 9 and 10 the whole data set. Open in new tab Table 3 Surveillance Cameras and Planned Crime with Victims Dependent variables: columns (1–5) pickpocketing/passenger, columns (6–10) robbery/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.004* −0.004 −0.004*** 0.001 0.002 −0.002* −0.003** −0.001 −0.001 −0.001 (0.002) 0.002 0.001 (0.002) (0.002) (0.001) (0.001) (0.001) (0.001) (0.001) Camera × city −0.007** −0.006*** 0.000 0.001 (0.003) (0.002) (0.001) (0.001) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 16.71 13.45 1.00 0.00 (0.00) (0.00) (0.32) (0.95) R 2 0.01 0.07 0.09 0.02 0.02 0.00 0.06 0.05 0.01 0.01 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Dependent variables: columns (1–5) pickpocketing/passenger, columns (6–10) robbery/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.004* −0.004 −0.004*** 0.001 0.002 −0.002* −0.003** −0.001 −0.001 −0.001 (0.002) 0.002 0.001 (0.002) (0.002) (0.001) (0.001) (0.001) (0.001) (0.001) Camera × city −0.007** −0.006*** 0.000 0.001 (0.003) (0.002) (0.001) (0.001) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 16.71 13.45 1.00 0.00 (0.00) (0.00) (0.32) (0.95) R 2 0.01 0.07 0.09 0.02 0.02 0.00 0.06 0.05 0.01 0.01 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Notes ***Indicates significance at the 1% level, ** at the 5% level, and * at the 10% level. The regressions include station fixed effects and standard errors are clustered at the level of the stations. The specifications in columns 1–3 and 6–8 include stations in the city and the specifications in columns 4, 5, 9 and 10 the whole data set. Open in new tab Table 4 reports regressions from drug‐related crime and assaults; apart from the regression reported in column 9, none of the ten specifications in this Table show deterrent effects of cameras. This is not surprising in the sense that potential criminals may be influenced by drugs and commit crimes in the heat of the moment, which is likely to reduce their awareness of camera signs. Moreover, in the case of drug dealing none of the parties will report the crime so that cameras can be used ex post. Table 4 Surveillance Cameras, Drug‐related Crime and Assaults Dependent variables: columns (1–5) drug related crime/passenger, columns (6–10) assault/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.003 0.001 0.004 0.004 0.005 −0.004 −0.004 −0.002 −0.001 −0.002 (0.005) (0.005) (0.004) (0.005) (0.006) (0.003) (0.003) (0.002) (0.003) (0.003) Camera × city −0.004 0.002 −0.003 0.000 (0.007) (0.006) (0.003) (0.003) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 0.00 0.41 3.61 0.84 (0.96) (0.52) (0.06) (0.36) R 2 0.01 0.07 0.07 0.02 0.02 0.00 0.07 0.07 0.02 0.02 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Dependent variables: columns (1–5) drug related crime/passenger, columns (6–10) assault/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.003 0.001 0.004 0.004 0.005 −0.004 −0.004 −0.002 −0.001 −0.002 (0.005) (0.005) (0.004) (0.005) (0.006) (0.003) (0.003) (0.002) (0.003) (0.003) Camera × city −0.004 0.002 −0.003 0.000 (0.007) (0.006) (0.003) (0.003) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 0.00 0.41 3.61 0.84 (0.96) (0.52) (0.06) (0.36) R 2 0.01 0.07 0.07 0.02 0.02 0.00 0.07 0.07 0.02 0.02 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Notes The regressions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1–3 and 6–8 include stations in the city and the specifications in columns 4,5,9 and 10 the whole data set. Open in new tab Table 4 Surveillance Cameras, Drug‐related Crime and Assaults Dependent variables: columns (1–5) drug related crime/passenger, columns (6–10) assault/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.003 0.001 0.004 0.004 0.005 −0.004 −0.004 −0.002 −0.001 −0.002 (0.005) (0.005) (0.004) (0.005) (0.006) (0.003) (0.003) (0.002) (0.003) (0.003) Camera × city −0.004 0.002 −0.003 0.000 (0.007) (0.006) (0.003) (0.003) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 0.00 0.41 3.61 0.84 (0.96) (0.52) (0.06) (0.36) R 2 0.01 0.07 0.07 0.02 0.02 0.00 0.07 0.07 0.02 0.02 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Dependent variables: columns (1–5) drug related crime/passenger, columns (6–10) assault/passenger . Sample . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . (10) . Camera −0.003 0.001 0.004 0.004 0.005 −0.004 −0.004 −0.002 −0.001 −0.002 (0.005) (0.005) (0.004) (0.005) (0.006) (0.003) (0.003) (0.002) (0.003) (0.003) Camera × city −0.004 0.002 −0.003 0.000 (0.007) (0.006) (0.003) (0.003) Station‐specific linear trends No No No No Yes No No No No Yes Year fixed effects Yes No No No No Yes No No No No Day by year fixed effects No Yes Yes Yes Yes No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 0.00 0.41 3.61 0.84 (0.96) (0.52) (0.06) (0.36) R 2 0.01 0.07 0.07 0.02 0.02 0.00 0.07 0.07 0.02 0.02 Observations 37,264 37,264 37,264 212,624 212,624 37,264 37,264 37,264 212,624 212,624 Notes The regressions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1–3 and 6–8 include stations in the city and the specifications in columns 4,5,9 and 10 the whole data set. Open in new tab To exclude the possibility that the results are not driven by trends, as well as to study the break at the time of introduction and possible dynamic effects, I also performed an event time analysis of the effect of cameras on crime in the city centre. Figure 5 plots month event time coefficients using station and year fixed effects. Event time zero corresponds to the month the policy is introduced in a station. The event time coefficients denote the average number of incidents per passenger in month τ relative to the number of incidents per passenger in the month preceding introduction of cameras. The bars show 95% confidence intervals and standard errors are clustered by station. Prior to the introduction of surveillance cameras, no single month is significantly different from zero. Following the introduction of cameras, there is a reduction in crime per passenger. All the subsequent coefficients lie below the reference group (t − 1) and several of the event months are significantly different from zero. Some of the coefficients of the last event months are markedly lower than before. The number of observations falls rapidly in the initial and final periods, which explains the large standard errors. A balanced panel would include 32 event‐time dummies in addition to the reference category prior to the introduction and 23 subsequent periods with 510 observations in each period. Such a window highlights the fact that there is an immediate and lasting reduction in crime where ten periods are significantly different from zero subsequent to the introduction. Fig. 5. Open in new tabDownload slide Surveillance Cameras and Crime, Monthly Event Time Analysis Fig. 5. Open in new tabDownload slide Surveillance Cameras and Crime, Monthly Event Time Analysis In a similar robustness test, Table 5 reports several placebo treatments for the time periods prior to introduction of the surveillance cameras. Column 1 reports 12 placebo month prior to the introduction of cameras and column 2 reports 18 placebo months. The placebos are both positive and negative and none of them are significant. The true camera dummy is highly significant in both specifications. This indicates that the introduction of cameras was exogenous to previous crime. Table 5 Placebo Treatments Dependent variable: crime/passenger . Sample . (1) . (2) . Camera −0.036** −0.036** (0.014) (0.014) Camera‐1 0.022 0.021 (0.020) (0.020) Camera‐2 −0.025 −0.024 (0.022) (0.023) Camera‐3 −0.029 0.030 (0.029) (0.030) Camera‐4 −0.051 −0.052 (0.033) (0.032) Camera‐5 0.027 0.026 (0.041) (0.041) Camera‐6 0.001 −0.000 (0.050) (0.050) Camera‐7 0.040 0.041 (0.053) (0.052) Camera‐8 −0.024 −0.025 (0.021) (0.021) Camera‐9 −0.032 −0.032 (0.022) (0.023) Camera‐10 0.010 0.011 (0.032) (0.032) Camera‐11 −0.029 −0.030 (0.038) (0.037) Camera‐12 0.030 0.036 (0.024) (0.048) Camera‐13 −0.021 (0.034) Camera‐14 0.007 (0.046) Camera‐15 0.036 (0.033) Camera‐16 −0.022 (0.025) Camera‐17 0.003 (0.025) Camera‐18 −0.015 (0.023) R 2 0.07 0.07 Observations 37,264 37,264 Dependent variable: crime/passenger . Sample . (1) . (2) . Camera −0.036** −0.036** (0.014) (0.014) Camera‐1 0.022 0.021 (0.020) (0.020) Camera‐2 −0.025 −0.024 (0.022) (0.023) Camera‐3 −0.029 0.030 (0.029) (0.030) Camera‐4 −0.051 −0.052 (0.033) (0.032) Camera‐5 0.027 0.026 (0.041) (0.041) Camera‐6 0.001 −0.000 (0.050) (0.050) Camera‐7 0.040 0.041 (0.053) (0.052) Camera‐8 −0.024 −0.025 (0.021) (0.021) Camera‐9 −0.032 −0.032 (0.022) (0.023) Camera‐10 0.010 0.011 (0.032) (0.032) Camera‐11 −0.029 −0.030 (0.038) (0.037) Camera‐12 0.030 0.036 (0.024) (0.048) Camera‐13 −0.021 (0.034) Camera‐14 0.007 (0.046) Camera‐15 0.036 (0.033) Camera‐16 −0.022 (0.025) Camera‐17 0.003 (0.025) Camera‐18 −0.015 (0.023) R 2 0.07 0.07 Observations 37,264 37,264 Notes *** denotes significance at the 1% level, ** at the 5% level and * at the 10% level. The regressions include day by year fixed effects and station fixed effects. The standard errors are clustered at the level of the stations. Open in new tab Table 5 Placebo Treatments Dependent variable: crime/passenger . Sample . (1) . (2) . Camera −0.036** −0.036** (0.014) (0.014) Camera‐1 0.022 0.021 (0.020) (0.020) Camera‐2 −0.025 −0.024 (0.022) (0.023) Camera‐3 −0.029 0.030 (0.029) (0.030) Camera‐4 −0.051 −0.052 (0.033) (0.032) Camera‐5 0.027 0.026 (0.041) (0.041) Camera‐6 0.001 −0.000 (0.050) (0.050) Camera‐7 0.040 0.041 (0.053) (0.052) Camera‐8 −0.024 −0.025 (0.021) (0.021) Camera‐9 −0.032 −0.032 (0.022) (0.023) Camera‐10 0.010 0.011 (0.032) (0.032) Camera‐11 −0.029 −0.030 (0.038) (0.037) Camera‐12 0.030 0.036 (0.024) (0.048) Camera‐13 −0.021 (0.034) Camera‐14 0.007 (0.046) Camera‐15 0.036 (0.033) Camera‐16 −0.022 (0.025) Camera‐17 0.003 (0.025) Camera‐18 −0.015 (0.023) R 2 0.07 0.07 Observations 37,264 37,264 Dependent variable: crime/passenger . Sample . (1) . (2) . Camera −0.036** −0.036** (0.014) (0.014) Camera‐1 0.022 0.021 (0.020) (0.020) Camera‐2 −0.025 −0.024 (0.022) (0.023) Camera‐3 −0.029 0.030 (0.029) (0.030) Camera‐4 −0.051 −0.052 (0.033) (0.032) Camera‐5 0.027 0.026 (0.041) (0.041) Camera‐6 0.001 −0.000 (0.050) (0.050) Camera‐7 0.040 0.041 (0.053) (0.052) Camera‐8 −0.024 −0.025 (0.021) (0.021) Camera‐9 −0.032 −0.032 (0.022) (0.023) Camera‐10 0.010 0.011 (0.032) (0.032) Camera‐11 −0.029 −0.030 (0.038) (0.037) Camera‐12 0.030 0.036 (0.024) (0.048) Camera‐13 −0.021 (0.034) Camera‐14 0.007 (0.046) Camera‐15 0.036 (0.033) Camera‐16 −0.022 (0.025) Camera‐17 0.003 (0.025) Camera‐18 −0.015 (0.023) R 2 0.07 0.07 Observations 37,264 37,264 Notes *** denotes significance at the 1% level, ** at the 5% level and * at the 10% level. The regressions include day by year fixed effects and station fixed effects. The standard errors are clustered at the level of the stations. Open in new tab In sum, the evidence indicates that surveillance cameras indeed reduce crime in stations in the city centre. The effects seem to be due to deterrence as opposed to incapacitation as crime was immediately reduced subsequent to the introduction of cameras. Moreover, pickpocketing is the most common crime to be reduced by cameras and since the penalties for this type of crime are often fines, this also suggests that the effects observed are in fact due to deterrence. 3. Displacement Effects The displacement effect may be addressed by using data on crime adjacent to the subway stations, that is, where camera surveillance is not permitted. I also had access to data on crimes that took place just outside the subway stations, which include bus stops, parking lots or parking stands for bicycles. According to the regressions weighted by the number of passengers in Table 6 (columns 3–5), some of the deterred pickpocketing incidents inside stations were displaced to the area outside the stations. Relative to the average before cameras were installed, pickpocketing adjacent to the stations increased by approximately 300%, or 12 incidents per year.11 Table 7 shows that when weighting the observations by the number of passengers, there is also a significant increase in crime per passenger just outside the stations in the central city following the introduction of cameras inside the stations. The increase was also very large, 130%. The average number of crimes just outside stations per station and year were approximately three. Based on the estimated 130% increase, the introduction of surveillance cameras leads to a displacement effect amounting to four crimes per station and year. Note that the coefficients in the weighted regressions in Tables 6 and 7 are somewhat larger and the precision is better than in the non‐weighted regressions. The unweighted regression on total crime in the city centre sample, for example, is not significant (column 2 in Table 7). On the other hand, the unweighted regression on pickpocketing reported in column 2 in Table 6 is significant at the 11% level.12 Table 6 Surveillance Cameras and Pickpocketing Outside the Subway Dependent variable: pickpocketing /passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.003 0.004 0.007*** 0.005*** 0.003* (0.003) (0.002) (0.002) (0.001) (0.002) Camera × city 0.000 0.002 (0.001) (0.003) Station‐specific trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 7.37 4.76 (0.01) (0.03) R 2 0.00 0.06 0.08 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Dependent variable: pickpocketing /passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.003 0.004 0.007*** 0.005*** 0.003* (0.003) (0.002) (0.002) (0.001) (0.002) Camera × city 0.000 0.002 (0.001) (0.003) Station‐specific trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 7.37 4.76 (0.01) (0.03) R 2 0.00 0.06 0.08 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Notes *** denotes significance at the 1% level, ** at the 5% level and * at the 10% level. The regressions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1–3 include stations in the city and the specifications in columns 4 and 5 the whole data set. Pickpocketing/passenger is multiplied by 100,000. Open in new tab Table 6 Surveillance Cameras and Pickpocketing Outside the Subway Dependent variable: pickpocketing /passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.003 0.004 0.007*** 0.005*** 0.003* (0.003) (0.002) (0.002) (0.001) (0.002) Camera × city 0.000 0.002 (0.001) (0.003) Station‐specific trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 7.37 4.76 (0.01) (0.03) R 2 0.00 0.06 0.08 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Dependent variable: pickpocketing /passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.003 0.004 0.007*** 0.005*** 0.003* (0.003) (0.002) (0.002) (0.001) (0.002) Camera × city 0.000 0.002 (0.001) (0.003) Station‐specific trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 7.37 4.76 (0.01) (0.03) R 2 0.00 0.06 0.08 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Notes *** denotes significance at the 1% level, ** at the 5% level and * at the 10% level. The regressions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1–3 include stations in the city and the specifications in columns 4 and 5 the whole data set. Pickpocketing/passenger is multiplied by 100,000. Open in new tab Table 7 Surveillance Cameras and Crime Outside the Subway Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.001 0.001 0.004** 0.000 −0.001 (0.001) (0.002) (0.001) (0.001) (0.002) Camera × city 0.002*** 0.005** (0.001) (0.002) Station‐specific linear trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 3.88 9.84 (0.05) (0.00) R 2 0.01 0.07 0.07 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.001 0.001 0.004** 0.000 −0.001 (0.001) (0.002) (0.001) (0.001) (0.002) Camera × city 0.002*** 0.005** (0.001) (0.002) Station‐specific linear trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 3.88 9.84 (0.05) (0.00) R 2 0.01 0.07 0.07 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Notes ***denotes significance at the 1% level, **at the 5% level and *at the 10% level. The regresssions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1–3 include stations in the city centre and the specifications in columns 4 and 5 include the whole data set. Open in new tab Table 7 Surveillance Cameras and Crime Outside the Subway Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.001 0.001 0.004** 0.000 −0.001 (0.001) (0.002) (0.001) (0.001) (0.002) Camera × city 0.002*** 0.005** (0.001) (0.002) Station‐specific linear trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 3.88 9.84 (0.05) (0.00) R 2 0.01 0.07 0.07 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Dependent variable: crime/passenger . Sample . (1) . (2) . (3) . (4) . (5) . Camera 0.001 0.001 0.004** 0.000 −0.001 (0.001) (0.002) (0.001) (0.001) (0.002) Camera × city 0.002*** 0.005** (0.001) (0.002) Station‐specific linear trends No No No No Yes Year fixed effects Yes No No No No Day by year fixed effects No Yes Yes Yes Yes Obervations weighted by passengers No No Yes Yes Yes F‐test of joint significance of camera and camera × city (p‐value in parantheses) 3.88 9.84 (0.05) (0.00) R 2 0.01 0.07 0.07 0.01 0.01 Observations 37,264 37,264 37,264 197,280 197,280 Notes ***denotes significance at the 1% level, **at the 5% level and *at the 10% level. The regresssions include station fixed effects and the standard errors are clustered at the level of the stations. The specifications in columns 1–3 include stations in the city centre and the specifications in columns 4 and 5 include the whole data set. Open in new tab However, since there are only 1,003 reported incidents in this data set, these results should be interpreted with considerable caution. Nevertheless, they indicate that some of the reduction in crime inside the stations in the city was displaced to the area adjacent to the stations. 4. Discussion Firms and governments in many countries increasingly use surveillance cameras in order to reduce crime. However, the potentially deterrent effects of such cameras are not yet well understood. In a natural experiment from the Stockholm subway system, surveillance cameras were found to reduce crime by approximately 25% at the stations in the city centre, 15% of which was displaced to the vicinity. In order to determine whether cameras should be used or not, it is also necessary to take the cost of the cameras into account. According to SL, the total costs of its cameras and the auxiliary equipment is SEK 33 million (approximately US$ 5 million), and the cameras have to be replaced every fifth year. SL’s call centre had the same number of employees (15) before and after introduction of the cameras, so employee costs have not changed. I have estimated that cameras deter approximately 575 crimes per year at the subway stations. On the other hand, approximately 75 crimes were displaced to non‐surveilled areas adjacent to the stations. Therefore, in total, assuming that there is no other displacement effect, there were 500 fewer crimes due to the cameras. Assuming also that there are no costs of intrusion on privacy, the cost of reducing one crime is just over SEK 13,000 (approximately US$ 2,000). It should be noted that this article deals with the deterrent effects of the cameras. However, surveillance cameras are sometimes used to gather evidence which, of course, is an additional benefit. It is difficult to estimate the value of a crime that did not take place. Obviously, an individual who is subject to a crime incurs substantial costs. More generally, reduced crime rates enhance a feeling of safety among passengers. SL carries out annual surveys where passengers are asked about their satisfaction with SL. One part of this survey pertains to passenger’ perception of their own safety. In the 2009 survey, it was reported that women travelling alone in the evening and at night felt 11% more safe in 2009 as compared to 2006 (AB SL Marknadsanalys, 2009). Of course, it is not clear whether this change is due to the introduction of cameras. Nevertheless, it may indicate that cameras increase passengers’ perception of safety which, after all, is the reason why they were installed in the first place. In sum, the benefit of surveillance cameras may therefore be higher than SEK 13,000. Under the assumption that crime is only displaced to areas adjacent to the subway stations, my policy conclusion is that the benefits of using cameras at subway stations in the city may outweigh the costs. This is in line with the few existing cost–benefit analyses in this area (Skinns, 1998; Gill and Spriggs, 2005). Finally, this analysis does not allow me to say what might have happened if cameras had been installed solely at the city stations. But since the cameras seem to be more efficient in the city centre, this could indicate that it is cost‐efficient to use cameras in the city centre only. Criminals who roam the subways in different countries are likely to be affected in similar ways by the presence of surveillance cameras. In fact, according to the Swedish police, pickpocketing is often committed by international gangs travelling around from one country to another.13 Thus, the results may also provide an indication of the effectiveness of cameras outside Sweden. Needless to say, more studies using exogenous variation and isolated policy intervention would certainly help policy makers when deciding whether surveillance cameras should be used or not. Footnotes 1 " For example, if surveillance cameras are installed due to an increased level of crime, then individuals potentially subject to crime may change their behaviour due to the elevated crime level rather than to the cameras. 2 " A notable example of an extensive study is Gill and Spriggs (2005) who analyse the effect of 13 camera projects in England in a wide range of environments where the introduction was not random. They conclude that ‘Even when changes /in crime/ have been noted, with the exception of those relating to car parks, very few are larger than could be due to chance alone and all could in fact represent either chance variation or confounding factors’ (Gill and Spriggs, 2005, p. 43). 3 " The article is also related to the recent economics literature, which addresses the causal relationship between policing and crime by using instruments (Levitt, 1997) or natural experiments (Di Tella and Schargrodsky, 2004; Klick and Tabarrok, 2005; Poutvaara and Priks, 2009; Machin and Marie, 2010; Draca et al., 2011). Moreover, for a discussion of the effect of surveillance cameras on terrorism, see Stutzer and Zehnder (2013) and references therein. 4 " There was, however, ongoing work to replace turnstiles. But according to Helena Nylén, the employee in charge of this project, to the extent new turnstiles were introduced during the time period under study, they were independent of the installation of surveillance cameras. 5 " The information is obtained from e‐mail correspondance with Lennart Argin in 2008 and telephone calls with Mats Lönn and Jan Ekström in February 2013. 6 " The stations Tekniska Högskolan and Stadion are relatively centrally located and also relatively large. They are nevertheless defined as non‐city stations because they are located outside the major junction Östermalmstorg. Defining these two stations as city stations does not affect the results qualitatively. 7 " A common type of vandalism, graffiti, is excluded from the data set. At the end of the time period under study, the police began to include it in a data base, which increased the number of reported crimes dramatically. 8 " I use crime divided by the average number of passengers per station to ensure that it is not changes in the number of passenger that drive the results. Dividing crime by passenger per year yields similar results. The results are also similar, albeit somewhat smaller, when crime is used as dependent variable. 9 " If the effect of surveillance cameras is homogeneous across stations, then the weighting should not matter for the coefficients. However, I also use weighted regressions, which measure the probability for a passenger to be a victim of crime, since it is possible that the effects differ across stations. 10 " Clustering on stations should alleviate the issue of serial correlation. However, as a further robustness check, I collapsed the data into months and weeks, which did not alter the results. 11 " Robberies per passenger also tend to increase significantly but there were only 15 incidents in the city centre before cameras. Analysing the effects on drug‐related crimes and assaults outside city centre stations provides a falsification test, as these types of crimes were not deterred by cameras. As expected, drug‐related crimes and assaults outside stations were not affected by the introduction of cameras. 12 " Moreover, the results of the interaction models without weights show significant results even though the size of the effects somewhat changes. 13 " http://www.polisen.se/Lagar-och-regler/Om-olika-brott/Stold-och-grov-stold/Fickstolder-och-bagagestolder References AB SL Marknadsanalys (Stockholm Public Transport Market Analysis) ( 2009 ). Upplevd kvalitetet i SL‐trafiken (Survey on the Quality of Public Transport), Stockholm. Associated Press . 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( 2009 ). ‘ Public areas CCTV and crime prevention: an updated systematic review and meta‐analysis ’, Justice Quarterly , vol. 26 ( 4 ), pp. 716 – 45 . Google Scholar Crossref Search ADS WorldCat Author notes " I thank Peter Fredriksson, Andreas Madestam, Peter Nilsson, Per Pettersson‐Lidbom, David Strömberg, Jakob Svensson, Jenny Säve‐Söderbergh, Anders Åkerman, Björn Öckert, conference participants at the EALE 2010 congress in London, Uppsala University, the referees and the editor for helpful comments. © 2015 Royal Economic Society