Education and Agriculture

Education and Agriculture PRELIMINARY DRAFT: DO NOT CITE Naureen Karachiwalla Giordano Palloni October 27, 2017 Abstract We provide causal evidence on the effect of educational attainment on participation in agriculture. Using the largest school investment program to date (the Sekolah Dasar IN- PRES program in Indonesia in the 1970 s) we show with differences in differences between treated and untreated cohorts and higher and lower program intensity districts, that individuals with higher educational attainment move out of agriculture. However, those who remain in agriculture own more agricultural land. Educational attainment may thus benefit both the agricultural and non-agricultural sectors. We also show that the parallel trends assumption, required for our results to be interpreted as causal, does indeed hold. Finally, we show that these results are not driven by selective migration. These results suggest that large investments in human capital can have profound effects on the rural economy and can lead to structural transformation. JEL Codes: I25, I28, O13, J43 Key words: education, agriculture, general equilibrium, Indonesia This paper has substantially benefited from excellent research assistance from Natasha Ledlie, as well as feedback from Valerie Mueller. Esther Duflo kindly provided the data. The authors gratefully acknowledge funding from the Policies, Institutions, and Markets Research Program of the CGIAR, as well as SNV Netherlands. International Food Policy Research Institute (IFPRI), 1201 Eye Street NW, Washington DC, 2005 USA (N.Karachiwalla@cgiar.org). International Food Policy Research Institute (IFPRI), 1201 Eye Street NW, Washington DC, 2005 USA (G.Palloni@cgiar.org). 1

1 Introduction This paper is motivated by two important global trends. First, governments invest a substantial share of their budgets in education. Second, educational attainment has been increasing (Glewwe and Muralidharan, 2015). These trends will have important consequences for rural labour markets, and in particular, on individuals choice to stay in or move out of agriculture. Governments thus need to anticipate what effects their investments will have. Should they then increase their investments in agriculture? In other sectors? Both? Additionally, understanding how increased education levels will affect occupational choice can help governments adapt infrastructure and modify policies in expectation of these downstream changes. The question of whether education moves people into or out of agriculture is one that is long studied. On the one hand, education could increase the returns to agriculture (for example, by enabling people to read instructions for agricultural inputs and learn about new practices) and thus increase the flow of people into agriculture (see, for example, Foster and Rosenzweig (1995); Goldin and Katz (2000); Schultz et al. (1965); Hayami et al. (1971); Reimers and Klasen (2013); Taylor and Yunez-Naude (2000). On the other hand, education could increase the returns to non-agricultural occupations (for example, by enabling people to take up other jobs that require certification) and thus decrease the proportion of people engaged in agriculture (see, for example, Huffman (2001); Gollin et al. (2014); Bezu and Barrett (2012); Mundlak (2001); Mussa (2015); Gardner (2005); Orazem and Mattila (1991). Relatedly, education could indirectly increase the net returns to non-agricultural occupations by decreasing migration costs (for example, better educated individuals may be able to adapt more quickly to new areas, have larger existing social networks, or an increased ability to form new networks). The literature that has tried to address this question previously is not based on experimental methods, but mostly on cross-country regressions and panel data (with a few exceptions, see Taylor and Yunez-Naude (2000)). However, selection into higher levels of educational attainment is likely important and would bias coefficient estimates (Huffman, 2001). In this paper, we are able to exploit a rare, but oft-studied, policy experiment to answer this question causally. We use the method of Duflo (2001), and study the large Indonesian school building program that took place during the 1970 s, and was the fastest school construction program in the world. Our 2

identification strategy compares those in higher versus lower intensity school building areas and those exposed to and not exposed to the program based on age. We also test the parallel trends assumption, comparing higher versus lower intensity program districts with an older cohort in a control experiment. Other papers have also used this method to answer different questions (see Ashraf et al. (2016); Breierova and Duflo (2003); Hertz et al. (2007); Pettersson Gelander (2012)). We find that every school built per 1,000 children results in an increase in the likelihood of completing primary school of 1.6 percentage points, and an increase in the likelihood of being literate of 1.2 percentage points. It also increases the likelihood that the household s livelihood involves no agriculture by 2 percentage points. Every school built per 1,000 children decreases the likelihood that the household owns agricultural land by 1.4 percentage points, but increases the area of agricultural land owned by 1.4 hectares for those who do own land (Liu and Yamauchi (2014) also find a similar result). Thus, people are moving out of agriculture, but those who stay have more agricultural resources. Education may then benefit both sectors. The welfare effects for the uneducated who remain in agriculture (presumably positive) and the educated who would not have been in agriculture regardless of the intervention (presumably negative) are less clear. One may worry that these results are driven by selection of people who are educated migrating to cities or to areas with greater returns to education. We find that these results are not driven by selective migration; people are not moving either to cities or within rural areas. Agüero and Ramachandran (2010) also find that educational attainment alone does not determine migration in either Indonesia or in Kenya. Lastly, we find that the parallel trends assumption holds for all of our outcomes. This paper is among the first quasi-experimental causal estimates of education on agriculture and rural transformation, and thus contributes to our understanding of what types of potential effects may result from large investments in education. Additionally, there is no research on policies large enough to have potentially produced general equilibrium effects on the returns to education in agriculture and outside of agriculture. The Indonesian school building program affected education for enough people that it is likely to have had general equilibrium effects on the return to education in each sector; we therefore view our estimates as general equilibrium treatment effects. Further, we have access to data on a rich set of outcomes that can point to 3

potential mechanisms by which this is occurring, and in particular, can allay concerns based on selective migration. It is important to note that it is unlikely that such investments would be equally effective in all contexts. Indonesia s school expansion was also accompanied by parallel investments to ensure that some quality was maintained, as evidenced by the fact that literacy also improved substantially. It would be a stretch to recommend that the average lowincome country should pursue an ambitious school construction program in order to structurally transform their economy. However, as the literature finds new and refines existing important ways to improve learning, those investments may also lead to transformation. The rest of the paper is organized as follows. The next section describes the Indonesian school building program as well as the data. Section 3 presents the empirical specification. Section 4 presents the results, and Section 5 concludes. 2 Program and Data The Sekolah Dasar INPRES school building program began in 1973 and was part of a large push for development from the Indonesian government. By 1980, 61,807 schools had been constructed (approximately 2 schools per 1,000 children). The number of schools constructed in a district was proportional to the number of out of school children in that district 1971. Duflo (2001) shows that in general this rule of thumb was followed, but not completely. The government also made complementary investments and recruited the necessary teachers to staff the schools, as well as ensured that all the newly hired teachers received pre-service training. This investment was in sharp contrast to the years prior to 1973, when there was a freeze in both hiring and capital expenditure in the education sector. The program resulted in a large increase in enrolment, from 69% in 1973 to 83% in just five years. Readers are referred to Duflo (2001) for further details on the program. We use two sources of data in this paper. First, we use the same data obtained by Duflo on the INPRES program. We use district level data on the number of schools constructed between 1973-79, the number of school aged children in 1971, the number of children enrolled in school in 1971, and the allocation of a water and sanitation program that also took place during the same years as the INPRES program. 4

We also use the 1995 intercensal survey carried out by the Indonesian Central Bureau of Statistics the Intercensus population survey (SUPAS). As in Ashraf et al. (2016) we use a sub-sample of these data, whereas the entire sample is used in Duflo (2001). We focus on men (since multiple papers have shown that on average, it was men whose educational attainment was affected by the program) born between 1950 and 1972, and match on district of birth with the INPRES data. Table 1 displays summary statistics for three groups in our sample: the full sample, those born between 1957-1972 (the experiment of interest), and those born between 1950-1962 (the control experiment). As expected, the average age of those in the sample for the experiment of interest is lower (30 years) than the average age of those in the sample for the control experiment (39 years). A higher proportion of men (nine percentage points more) had completed primary education in the younger cohort, and were literate, as expected. There are not large differences between groups for the proportion of men whose households own land, the area of land owned, or the proportion of men whose households do not participate in any agricultural activity. More men in the older cohort are likely to be self-employed, and to have formed their own household. They are also more likely to have migrated in the past five years. However, there are not large differences between those who have ever migrated or who reside in a rural location. The next section will further compare these groups as well as compare men living in relatively higher intensity INPRES program areas versus relatively lower intensity INPRES program areas. 3 Empirical Specification Identification relies on differences in differences. The comparisons are between those who were born in years such that they were exposed to the program to those born in years such that they were too old to benefit from the program, and between those who were born in districts where relatively more schools were built versus those born in districts where relatively fewer schools were built. In other words, we compare the change in outcomes between younger cohorts (who were potentially exposed to the program) and older cohorts (who were not exposed) in districts that had a high level of primary school construction relative to in districts that had a low level of primary school construction. Children born prior to 1962 were already too old 5

to benefit from the program (children attend primary school between age 7-12). Duflo (2001) shows that delayed enrollment and repetition are negligible. She also shows that district of birth is almost always the district where primary education takes place, and it is also not more plausibly exogenous than is district of education. We estimate the following equation: Y idt = α d + α t + β 1 T t S d + k X d Ik t Γ k + ɛ idt (1) where Y is the outcome of interest, i is the individual, d is a district, and t is time (year of birth). α d are district of birth fixed effects and α t are year of birth fixed effects. T t is a dummy variable equal to one for those born between 1968-1972 (those aged 2-6 in 1974 - the treated cohort) and zero for those born 1957-1962 (aged 12 to 17 in 1974 - the control cohort). Those who were partially treated (those born between 1963 and 1967) are dropped from the analysis. S d is the number of INPRES schools built per 1,000 children in district d. k X d Ik t Γ k denotes year of birth fixed effects interacted with district-level control variables. We control for the school aged population (ages 5-14) as well as the enrollment rate in the district in 1971 as these are the basis for the number of schools that were to be built in each district. We further control for the allocation of a water and sanitation program in the district of birth to control for the possibility of other programs that could also affect education being implemented alongside INPRES. The water and sanitation program was the second largest program at the time. Standard errors are clustered at the level of the district of birth. The coefficient of interest is β 1. This coefficient can be interpreted as a causal estimate as long as, in the absence of the program, the educational attainment of men in the relatively higher versus lower intensity program districts would not have been different in the absence of the program. We can test this assumption by estimating (1) using men who were 12-17 in 1974 (born 1957-1962) as the treated sample and those who were 18-24 in 1974 (born 1950-1956) as the control sample for a control experiment. If the parallel trends assumption holds, there should be no differences between the higher and lower intensity program districts between the treated and untreated cohorts for this older sample. We look at several outcomes. We first confirm whether the INPRES program influenced 6

primary school completion (educational attainment). We use primary school completion rather than years of education because Duflo (2001) shows that the INPRES program increased years of schooling mainly by increasing primary schooling, which is sensible since it was primary schools that were built. Ashraf et al. (2016) also uses primary school completion as their measure of educational attainment. We also use literacy as an outcome to see whether the program induced skills formation rather than simply a higher number of years of schooling. This is important as it is skills that determine employment Hanushek and Woessmann (2011). Next, we examine whether men who were exposed to the program have higher or lower participation rates in agriculture. Our outcome measure is a dummy variable equal to one if the individual s household s main source of livelihood involves no agriculture. We then examine whether those exposed to the program have more land; we use the number of hectares of land owned by the individual s household. 1 These are all measures of involvement in the agricultural sector. We then explore some further measures that could be related to involvement in agriculture. Individuals who are self-employed are less likely to be engaged in agriculture; they more likely own a small or micro enterprise. We thus look at the impact of the program on whether an individual is self-employed. Further, given that families tend to own land, an individual who has moved out of their parents household is also less likely to be engaged in agriculture. We create a dummy variable equal to one if the individual has formed his own household. 2 Lastly, we check whether the results may be driven by selective migration. First, we create a dummy variable equal to one if the individual has ever migrated (the dummy variable is equal to one if the district of birth is different from the current district of residence). We also create a dummy variable equal to one if the individual has migrated within the past five years. Finally, we create a dummy variable equal to one if the individual s household is located in a rural area to check whether individuals may be moving from urban to rural areas (or vice-versa) or may be moving within districts. We also estimate specifications that estimate treatment effects by year of birth. We graph the coefficients from these to see whether, as we would expect, we see increasing effect sizes for those who were exposed to the program longer and zero effect sizes for those not exposed to the 1 Households with no land have this variable set to zero. 2 In the data, this is determined by whether the individual is the head of household or the spouse. 7

program. To address the potential issue of the endogeneity of educational attainment, as a robustness check, we also estimate instrumental variables specifications using the number of schools built per 1,000 children in the district of birth interacted with exposure to the program as an instrument for primary school completion. We then use the estimated likelihood of completing primary education in the second stage to estimate the impact of educational attainment on the above listed outcomes. The same controls are included in these specifications, and standard errors are also clustered at the level of the district of birth. The next section discusses the impact estimates. 4 Results This section presents the results of estimating our empirical specifications. Table 2 provides reduced form evidence on the impact of the INPRES school building program on educational attainment and participation in agriculture. Column (1) shows that each additional school built per 1,000 school-aged children results in an increase in the likelihood of completing primary school of 1.6 percentage points (significant at the 10% level), 3 and column (2) shows that it also results in an increase in the likelihood of being literate of 1.2 percentage points (significant at the 5% level). These results confirm the findings of Duflo (2001); Ashraf et al. (2016) and others that the INPRES program substantially increased educational attainment. Further, skills were gained in the process; in high intensity program districts, cohorts who benefitted from the program are significantly more literate. In column (3) we see that an additional school built per 1,000 children also increases the likelihood that a household s source livelihood involves no agriculture by 2 percentage points. This effect is statistically significant at the 5% level. This result provides evidence that improvements in educational attainment cause people to move out of agriculture. Additionally, every school built per 1,000 children decreases the likelihood that the household owns agricultural land by 1.4 percentage points (significant at the 10% level), providing further evidence of educated individuals moving out of agriculture. An additional school built per 1,000 children 3 This is almost exactly the same coefficient and standard error found by Ashraf et al. (2016). 8

however also increases the area of agricultural land owned by 1.4 hectares (significant at the 5% level). The program may also have benefited the agricultural sector by improving the returns for those who remained in agriculture. Those who remain in agriculture tend to have larger, and potentially more productive farms. All of the coefficients in the control experiment for the older cohort confirm that there are no pre-trends and that the parallel trends assumption holds. All but one coefficient is statistically insignificant, and the one marginally significant coefficient (dummy variable for the household s livelihood involving no agriculture) goes in the opposite direction as the sample for the main experiment. Further, given the number of tests being conducted (10), the finding of one significant pre-trend at the 10% level is exactly what we should expect to find by chance. In Table 3 we examine some other outcomes that could be correlated with participation in agriculture. In column (1) wee see that each additional school built per 1,000 school-aged children results in an increase in the likelihood that an individual is self-employed (significant at the 1% level). Individuals who are self-employed are less likely to be engaged in agriculture. Column (4) shows that an additional school built per 1,000 children increases the likelihood that an individual has moved out of his parents house by 4 percentage points (significant at the 1% level). These individuals are also less likely to be engaged in agriculture, given that agricultural land tends to be owned by the family. We then look at the issue of selection. One may worry that the results are driven by selective migration; that more educated individuals move to cities or to other areas with higher returns to education. However, there are no impacts on the likelihood of ever having migrated, having migrated in the past five years, or the location of the household being rural. For these outcomes, all the pre-trend coefficients are statistically insignificant. Figures 1-4 provide further evidence on the impacts of the program. In these figures, coefficients are plotted for impacts of the program separately by age. We consider those aged 2-23 in 1974, and we expect that for those aged 7 and below, impacts would be increasing (or decreasing in the case of negatively signed coefficients from Tables 2 and 3). We also expect the impacts to be zero for those aged 8 and above in 1974. We plot the impact of the INPRES program on primary school completion, whether the household s livelihood involves no agriculture, whether the household owns agricultural land, and the area of agricultural land owned. Figure 1 shows 9

that the effect of the program on primary school completion for those aged 8 and above in 1974 is indeed not statistically different from zero, but is increasing from age 7 and below. Figure 2 shows a similar pattern: zero impacts for those aged 8 and above and increasing impacts for those aged 7 and below in 1974. Figure 3 shows that the impact of the program on the likelihood of a household owning land is zero for those aged 8 and above and is decreasing for those aged 7 and below in 1974. Finally, figure 4 shows that the impact of the program on the area of land owned is zero for those aged 8 and above and is increasing for those aged 7 and below in 1974. These figures confirm the findings in Tables 2 and 3. In Table 4 we provide estimates from instrumental variables regressions where the likelihood of completing primary school is instrumented with the intensity of the INPRES program interacted with exposure to the program. The coefficients all have the same sign and pattern of the reduced form results with less precisely estimated coefficients, and much larger effect sizes due to the inflation from the first stage. We do not focus on these for interpreting effect sizes, as some probabilities lie above one. 5 Conclusion In this paper, we provide among the first quasi-experimental evidence regarding educational attainment and rural transformation. We are interested in general equilibrium effects, and we explore the effect of educational attainment (measured by primary school completion) on participation in agriculture. The Indonesian school building program (INPRES) that took place from 1973-1979 provides a unique opportunity to explore this question, as it is one of the largest education investment programs in history, and is thus likely to have had general equilibrium effects. We exploit difference in differences variation in the cohorts exposed to the INPRES program versus those who were too old to benefit from it, as well as those who were born in districts with relatively high program intensity versus those born in districts with relatively lower program intensity. We find that the program indeed increases educational attainment significantly. Each additional school built per 1,000 children increased the likelihood of completing primary education by 1.6 percentage points, and increases the likelihood of being literate by 1.2 percentage points. 10

The INPRES program thus did significantly improve educational attainment, and this was accompanied by marketable skills. We also find that the program decreased the likelihood of a household s livelihood involving any agriculture. Individuals thus tended to move out of agriculture and into the non-agricultural sector as a result of the program. Complementary to this, we also find that the likelihood of owning agricultural land decreases as a result of the program. However, for those who do own agricultural land, the area of land owned is greater. Thus, the program may also have benefited the agricultural sector by improving the returns for those who remained in agriculture. We also find that additional schools constructed lead to an increased likelihood of being self-employed and of moving out of one s parent s household. Those who are self-employed and who have formed their own households are less likely to be engaged in agriculture. Finally, we show that these results are not driven by selective migration. The program had no impact on migration or location in rural versus urban areas. These results suggest that large (and well implemented) investments in human capital can have profound effects on the rural economy and can lead to structural transformation. Studying the general equilibrium effects of such investments can help governments to plan future complementary investments, as well as help governments to respond to changes in occupational choices. References Agüero, J. M. and M. Ramachandran (2010). The intergenerational effects of increasing parental schooling: Evidence from Zimbabwe. University of California, mimeo. Ashraf, N., N. Bau, N. Nunn, and A. Voena (2016). Bride price and female education. Technical report, National Bureau of Economic Research. Bezu, S. and C. Barrett (2012). Employment dynamics in the rural nonfarm sector in Ethiopia: Do the poor have time on their side? Journal of Development Studies 48 (9), 1223 1240. Breierova, L. and E. Duflo (2003). The Impact of Education On Fertility and Child Mortality: Do Fathers Really Matter Less than Mothers? OECD Development Centre Working Paper, No. 217 (Formerly Webdoc No. 5). OECD Publishing (NJ1). 11

Duflo, E. (2001, September). Schooling and Labor Market Consequences of School Construction in Indonesia: Evidence from an Unusual Policy Experiment. American Economic Review 91 (4), 795 813. Foster, A. D. and M. R. Rosenzweig (1995). Learning by doing and learning from others: Human capital and technical change in agriculture. Journal of Political Economy 103 (6), 1176 1209. Gardner, B. L. (2005). Causes of rural economic development. Agricultural Economics 32 (s1), 21 41. Glewwe, P. and K. Muralidharan (2015). Improving school education outcomes in developing countries: evidence, knowledge gaps, and policy implications. University of Oxford, Research on Improving Systems of Education (RISE). Goldin, C. and L. F. Katz (2000). Education and income in the early twentieth century: Evidence from the prairies. The Journal of Economic History 60 (3), 782 818. Gollin, D., D. Lagakos, and M. E. Waugh (2014). The Agricultural Productivity Gap. The Quarterly Journal of Economics 129 (2), 939 993. Hanushek, E. A. and L. Woessmann (2011). How much do educational outcomes matter in oecd countries? Economic Policy 26 (67), 427 491. Hayami, Y., V. W. Ruttan, et al. (1971). Agricultural development: an international perspective. Baltimore, Md/London: The Johns Hopkins Press. Hertz, T., T. Jayasundera, P. Piraino, S. Selcuk, N. Smith, and A. Verashchagina (2007). The inheritance of educational inequality: International comparisons and fifty-year trends. The BE Journal of Economic Analysis & Policy 7 (2). Huffman, W. E. (2001). Human capital: Education and agriculture. Handbook of Agricultural Economics 1, 333 381. Liu, Y. and F. Yamauchi (2014). Population density, migration, and the returns to human capital and land: Insights from Indonesia. Food Policy 48, 182 193. 12

Mundlak, Y. (2001). Explaining economic growth. American Journal of Agricultural Economics 83 (5), 1154 1167. Mussa, R. (2015). The Effects of Educational Externalities on Maize Production in Rural Malawi. Oxford Development Studies 43 (4), 508 532. Orazem, P. F. and J. P. Mattila (1991). Human capital, uncertain wage distributions, and occupational and educational choices. International Economic Review, 103 122. Pettersson Gelander, G. (2012). Do Supply-Side Education Programmes Work? The Impact of Increased School Supply on Schooling and Wages in Indonesia Revisited. Reimers, M. and S. Klasen (2013). Revisiting the role of education for agricultural productivity. American Journal of Agricultural Economics 95 (1), 131 152. Schultz, T. W. et al. (1965). Economic crises in world agriculture. Ann Arbor: Univ. Michigan Press. Taylor, J. E. and A. Yunez-Naude (2000). The returns from schooling in a diversified rural economy. American Journal of Agricultural Economics 82 (2), 287 297. 13

Figures Figure 1: Treatment Effects by Age - Primary School Completion ATE: Primary School Completion For Males -.05 0.05 23 22 21 20 19 18 17 16 15 14 13 12 11 10 9 8 7 6 5 4 3 2 Age in 1974 Point Estimate 95% CI Figure 2: Treatment Effects by Age - Household is not involved in agriculture ATE: HH not engaged in agric. For Males -.1 -.05 0.05 23 22 21 20 19 18 17 16 15 14 13 12 11 10 9 8 7 6 5 4 3 2 Age in 1974 Point Estimate 95% CI 14

Figure 3: Treatement Effects by Age - Household owns agricultural land ATE: HH owns agric. land For Males -.02 0.02.04.06.08 23 22 21 20 19 18 17 16 15 14 13 12 11 10 9 8 7 6 5 4 3 2 Age in 1974 Point Estimate 95% CI Figure 4: Treatement Effects by Age - Area of agricultural land owned ATE: Area of land owned For Males -8-6 -4-2 0 2 23 22 21 20 19 18 17 16 15 14 13 12 11 10 9 8 7 6 5 4 3 2 Age in 1974 Point Estimate 95% CI 15

Tables Table 1: Summary statistics Full Sample Born 1957-1972 Born 1950-1962 mean/sd mean/sd mean/sd Age 34.19 30.34 38.52 (7.09) (5.45) (3.71) Completed primary school 0.75 0.79 0.70 (0.43) (0.40) (0.46) Literate 0.94 0.96 0.93 (0.23) (0.20) (0.26) HH not engaged in any agric. 0.50 0.51 0.50 (0.50) (0.50) (0.50) HH owns agric. land 0.42 0.41 0.42 (0.49) (0.49) (0.49) Area of agric. land owned 58.69 59.76 58.35 (48.79) (48.61) (48.85) Self-employed 0.48 0.43 0.55 (0.50) (0.50) (0.50) Moved out of parents HH 0.76 0.66 0.93 (0.43) (0.47) (0.26) Migrated since birth 0.29 0.29 0.30 (0.46) (0.45) (0.46) Migraded in past 5 years 0.08 0.10 0.05 (0.27) (0.30) (0.23) Rural location 0.61 0.61 0.62 (0.49) (0.49) (0.48) Observations 79329 52636 54106 16

Table 2: Education and Agriculture Outcomes (1) (2) (3) (4) (5) Completed Literate Livelihood involves HH owns Area of Primary no agric. agric. land agric. land Panel A - Experiment of Interest heightborn 1968-1972 * No. INPRES 0.0160 0.0122 0.0198-0.0144 1.4427 schools per 1,000 children (0.0083) (0.0052) (0.0079) (0.0073) (0.7274) Observations 52636 52636 52636 52636 52636 Panel B - Control Experiment heightborn 1957-1962 * No. INPRES -0.0009 0.0068-0.0134 0.0076-0.7627 schools per 1,000 children (0.0073) (0.0050) (0.0073) (0.0058) (0.5734) Observations 54106 54106 54106 54106 54106 Notes: Standard errors in parentheses. * p < 0.10, ** p < 0.05, *** p < 0.01. Panel A - Experiment of Interest: sample includes those aged 2-6 in 1974 (treated cohorts) and those aged 12-17 in 1974 (control cohorts). Panel B - Control Experiment: sample includes those aged 12-17 in 1974 ( treated cohorts) and those aged 18-24 in 1974 (control cohorts). All regressions include the following controls: year of birth fixed effects, district of birth fixed effects, year of birth interacted with school aged population in the district of birth in 1971, year of birth interacted with enrollment rate in the district of birth in 1971, year of birth interacted with allocation of water and sanitation program in district of birth. Standard errors clustered at the level of the district of birth. Table 3: Employment and Migration Outcomes (1) (2) (3) (4) (5) Self- Moved Migrant Migrant in Rural employed out since birth past 5 years location Panel A - Experiment of Interest heightborn 1968-1972 * No. INPRES 0.0197 0.0387-0.0021-0.0024-0.0050 schools per 1,000 children (0.0073) (0.0098) (0.0069) (0.0067) (0.0072) Observations 52636 52636 52636 52635 52636 Panel B - Control Experiment heightborn 1957-1962 * No. INPRES -0.0079-0.0017 0.0069 0.0028 0.0046 schools per 1,000 children (0.0057) (0.0044) (0.0062) (0.0038) (0.0069) Observations 54106 54106 54106 54105 54106 Notes: Standard errors in parentheses. * p < 0.10, ** p < 0.05, *** p < 0.01. Panel A - Experiment of Interest: sample includes those aged 2-6 in 1974 (treated cohorts) and those aged 12-17 in 1974 (control cohorts). Panel B - Control Experiment: sample includes those aged 12-17 in 1974 ( treated cohorts) and those aged 18-24 in 1974 (control cohorts). All regressions include the following controls: year of birth fixed effects, district of birth fixed effects, year of birth interacted with school aged population in the district of birth in 1971, year of birth interacted with enrollment rate in the district of birth in 1971, year of birth interacted with allocation of water and sanitation program in district of birth. Standard errors clustered at the level of the district of birth. 17

Table 4: IV Regressions heightcompleted primary school (1) (2) (3) (4) (5) (6) (7) (8) (9) Literate Livelihood involves HH owns Area of Self- Moved Migrant Migrant in Rural no agric. agric. land agric. land employed out since birth past 5 years location Panel A - Experiment of Interest 0.7597 1.2404-0.8989 90.1895 1.2346 2.4211-0.1319-0.1472-0.3098 (0.3715) (0.6451) (0.5900) (58.7955) (0.8293) (1.3470) (0.4396) (0.4134) (0.4110) Observations 52636 52636 52636 52636 52636 52636 52636 52635 52636 Panel B - Control Experiment heightcompleted primary -7.9822 15.7317-8.9016 896.0538 9.3377 2.0340-8.0771-3.3867-5.3623 (69.8008) (129.9489) (74.8532) (7.5e+03) (80.0005) (17.2765) (69.8513) (29.9889) (44.4043) school Observations 54106 54106 54106 54106 54106 54106 54106 54105 54106 Notes: Standard errors in parentheses. * p < 0.10, ** p < 0.05, *** p < 0.01. Panel A - Experiment of Interest: sample includes those aged 2-6 in 1974 (treated cohorts) and those aged 12-17 in 1974 (control cohorts). Panel B - Control Experiment: sample includes those aged 12-17 in 1974 ( treated cohorts) and those aged 18-24 in 1974 (control cohorts). Completion of primary schooling instrumented with interaction between dummy variable for being 2-6 in 1974 and the number of schools built per 1,000 children (experiment of interest) or with interaction between dummy variable for being 12-17 in 1974 and the number of schools built per 1,000 children (control experiment). All regressions include the following controls: year of birth fixed effects, district of birth fixed effects, year of birth interacted with school aged population in the district of birth in 1971, year of birth interacted with enrollment rate in the district of birth in 1971, year of birth interacted with allocation of water and sanitation program in district of birth. Standard errors clustered at the level of the district of birth. 18