Childhood Migration and Educational Attainment

Childhood Migration and Educational Attainment: Evidence from Indonesia Abstract Millions of families migrate every year in search of better opportunities. Whether these opportunities materialize for the children brought with them depends on the quality of the destination that their parents selected. Using Indonesian Census data, I find that average differences in educational outcomes are small between children who moved domestically and those who did not. However, conditional on having migrated, destination turns out to be very important. Exploiting variation in the age of migration, I show that children who spend more time growing up in better districts have higher graduation rates and more years of completed schooling. These effects are persistent and carry over to better labor market outcomes. Overall, my findings suggest substantial heterogeneity of returns to childhood migration with respect to destination. 1 1 Introduction Internal migration is an important strategy of individuals seeking better opportunities. In making the migration decision, families not only take into account potential gains for the working generation. Whether better opportunities materialize for the children brought with them depends on the quality of the destination that their parents selected. Children who move to environments more favorable to learning benefit from migration while those who move to adverse environments may experience negative effects from migration. Existing research implies positive effects of rural to urban migration. However, despite increasing urbanization rates, most destinations of internal migrants are rural, in particular in developing countries. It is therefore crucial to study heterogeneous returns to migration with respect to destination, going beyond the rural-urban distinction. Using data from Indonesia, I show that destination quality, measured as average educational attainment among permanent residents, is a key determinant for the returns to childhood migration. Small observational differences in education outcomes between migrant and non-migrant children motivate the question of whether differences in destination quality could account for the small average effect. Destination quality can vary substantially in Indonesia, which is characterized by a rapidly growing economy and increasing urbanization rates. Similarly, educational attainment has increased tremendously with illiteracy rates now in the low single digits and nearly universal primary school education (Suharti, 2013), thanks to one of the world’s largest school construction programs in history and a large and vibrant religious education sector that caters to poorer and conservative families often left out of formal education markets in the Muslim world (Bazzi et al., 2020). The country and its highly internally mobile population therefore provides a well-suited context to investigate the importance of migration destination. 1 1 Education is a relevant metric to assess the effect on long-run economic standing: Duflo (2001) estimates the economic returns to a year of education in Indonesia to be between 6.8 and 10.6 percent. 2 To explore the role of destination, I apply Chetty and Hendren’s (2018) age-at-migration research design. By exploiting differences in the timing of migration, the design can identify the causal effect of location on education, even in the presence of sorting into destination. I compare the effect of destination quality between children who migrated at different ages and who were, therefore, exposed to the destination for different amounts of time - to estimate the causal location exposure effect on education. For my analysis, I draw on Census micro data covering the entire Indonesian population in 2000 and 2010. To motivate the exposure effects analysis, I first provide descriptive evidence of the relationship between internal migration and education. I find that internal migrants are more likely to graduate from any given level of school. For example, children aged 15 to 20 who lived outside their birth district in 2000 were 6.9 percentage points more likely to have completed at least junior secondary school (nine years of education) and 9 percentage points more likely to have graduated from senior secondary school. However, controlling for parental education reduces these differences to just 1.1 and 1.8 percentage points, respectively. While remaining selection effects prevent the causal interpretation of these estimates, they suggest that average returns to childhood migration might be small. I propose that the small average effect could mask heterogeneous returns across destinations. In line with my argument, I find that the correlation between district quality and graduation rates of migrants is high. For migrants, relocation to a district with a ten percentage point higher junior secondary school graduation rate among permanent residents is associated with a 6.1 percentage point higher likelihood to graduate from junior secondary school. However, part of this difference likely reflects unobserved family characteristics that are both correlated with destination choice and the underlying education potential of the child. In order to circumvent potential confounders and understand whether a causal relationship exists, I 3 exploit the timing of migration. I find that children who migrate earlier to a better district2 are more likely to have completed primary school and have higher graduation rates from junior and senior secondary school. My findings show that educational outcomes of migrants converge to those of permanent residents at a yearly rate of 1.8 to 1.9 percent. This implies a 16-year-old’s likelihood to graduate from junior secondary school increases by about one percentage point every year that she migrates earlier from an origin at the 10th percentile to a destination district at the 90th percentile. Children with less educated parents benefit more from additional exposure than children of parents with at least a junior secondary school degree, underlining the importance of internal migration as a channel for upward intergenerational mobility. The identifying assumption of the age-at-migration design is that unobservable family characteristics are orthogonal to the timing of migration. I relax this assumption by identifying the exposure effect from children who belong to the same household and show that the addition of household fixed effects does not qualitatively change the findings. To show that exposure effects from childhood migration have a persistent effect on economically meaningful outcomes, I complement the analysis with a sample of adults from the Intercensal Population Surveys (SUPAS). I find a positive destination exposure effect on completed education, and provide evidence for reduced form effects on labor market outcomes. For example, more time spent in a favorable environment during childhood increases increases the likelihood that an adult works in the formal sector. This paper contributes to two strands of research. First, my paper adds to the literature on the returns of internal migration (Bryan et al., 2014; Beegle et al., 2011; Hamory et al., 2020; Ferrone and Claudia Giannelli, 2020; Bryan and Morten (2019)), but with a focus on children instead of the working generation. Recent work points at positive effects of internal migration for children which predominantly benefits those who leave rural areas and move to cities (Cockx, 2 I will refer to districts with better educational outcomes among non-migrant children as “better” districts without judgment about other district characteristics. 4 2021; Hamory et al., 2020; Nakamura et al., 2020). My paper takes the question about heterogeneous returns to migration further by constructing destination- and cohort-specific quality measures. In addition, previous work relies on small longitudinal surveys, while I am able to identify causal destination exposure effects from cross-sectional Census data. Cockx (2021) attempts to control for selection into migration by comparing the children of migrants to the children of their non-migrant siblings. While this strategy partially controls for shared genetic and family background factors of the parental generation, it does not necessarily alleviate the concern of selection bias: It is likely that the sibling who decided to migrate to a city did so due to unobservable characteristics related to their willingness and ability to invest in their children’s education. Acknowledging the challenge of controlling for selection, I focus on the returns to different destinations among internal migrants instead. Second, I complement the literature on location exposure effects by studying the role of destination in a large developing economy. Experimental studies focus on evaluating relocation experiments in developed countries, such as the Moving to Opportunity for Fair Housing (MTO) project in the US (Katz et al., 2001; Ludwig et al., 2013; Chetty et al. (2016)) and other experiments or quasi-experiments like housing demolition (Chyn, 2018; Oreopoulos, 2003). Those studies find positive effects on health outcomes, but evidence regarding economics effects are contradictory. A recent paper by Chetty and Hendren (2018) introduces a method to identify causal location exposure effects in observational data. The paper studies intergenerational mobility in the United States and shows that outcomes, such as income and college graduation rates of individuals who migrated to better neighborhoods during childhood, improve linearly in proportion to the number of years they were exposed to the destination. Deutscher (2020) replicates the analysis with Australian data and finds that exposure during teenage years is particularly important. In their comprehensive study on intergenerational education mobility in Africa, Alesina et al. (2021) show exposure to place also matters in developing countries. I add to this growing body of literature by exploring location exposure effects on education in Indonesia. I study the effect on several age-specific educational outcomes from primary and 5 secondary school completion of children to the number of years of educational attainment of adults. In addition, I provide evidence for the persistence of childhood exposure effects and their relevance for labor market outcomes later in life. This paper is organized as follows. The next section gives an introduction to the educational system in Indonesia. Section 3 explains the empirical strategy and describes the data. Section 4 first shows that differences in education outcomes are small between migrant and non-migrant children. Then it presents estimates of the destination exposure effect of childhood migration on education and reduced form evidence of positive effects on labor market outcomes. The section finishes with a discussion of the identifying assumption and robustness checks. Section 5 concludes. 2 Education in Indonesia In Indonesia, children start school at the age of six or seven3 and go to primary school for six years. Subsequently, junior secondary school (Sekolah Menengah Pertama, or JUNSEC) takes three years and senior secondary school another three years (Sekolah Menengah Atas, or SENSEC)4 . In 1973, the Indonesian government started a massive school construction program using revenues from the early 1970s oil boom. Under the program, 61,807 new schools were constructed between the school years 1973–1974 and 1978–1979, which approximately doubled the number of schools Duflo (2001). The goal was to put a primary school in every village. The program increased primary school enrollment considerably and also allowed overage students to obtain elementary education. From 1994 onwards, the government has required nine years of compulsory education. However, while junior secondary school enrollment rates 3 The official school starting age is seven, but parents are allowed to enroll their children at the age of six since 2003 (Suharti, 2013). However, even as early as 1995 about half of the six-year-olds were reported going to school in the Intercensal Population Survey (1995 SUPAS). 4 After junior secondary school, students can also attend vocational high school (Sekolah Menengah Kejuruan, or SMK) which in the Census will be recorded as “senior secondary school”. 6 have increased over time, even in 2010 only 68 percent of the eligible cohorts attended junior secondary school (Suharti, 2013). Geographic differences in education are substantial, and the availability and quality of junior secondary schools is particularly problematic in isolated rural areas (Suryadarma and Jones (2013)). In 2010, the adult population (age 15 and older) had an average 10.9 years of education in the province of Jakarta, but only 6.7 years of education in the province of Papua. The share of junior secondary school teachers holding the minimum qualification (a four-year degree) ranged from 38 percent (Maluku) to 89 percent (East Java) during the school year 2009/2010 (Suharti, 2013). While socioeconomic background is an important determinant of educational attainment for children, gender is not. Net enrollment rates are higher for girls than for boys in junior secondary school, and similar in senior secondary school. While in the 1990s there were considerably more male students pursuing tertiary education, women have overtaken men during the 2000s and now have higher enrollment rates (Suharti, 2013) in universities. 3 Empirical Strategy This section first introduces my main data source, the 2000 and 2010 complete count Census samples, and additional data which comes from the 1985, 1995, and 2005 waves of the Intercensal Population Survey (SUPAS). It then goes on to describe the estimation strategy. 7 3.1 3.1.1 Data 2000 and 2010 Complete-Count Population Census My main data is drawn from the 2000 and 2010 complete-count Population Census micro data samples.5 It covers the entire Indonesian population of about 195 million individuals in 2000 and 234 million in 2010. I restrict my sample to children and young adults between the age of 12 and 20 who live with their parents6 . The lower bound coincides with the age of primary school graduation and the upper bound is chosen to minimize cohabitation bias. This bias might arise if children who cohabitate with their parents are systematically different from those who do not. Given that cohabitation rates decrease with children’s age, I expect the potential bias to be stronger for older children. In Section 4.6 I show that the baseline results remain unchanged after restricting the sample to children under the age of 15 who have cohabitation rates above 95 percent. From the data I can directly construct a simple measure of (past) migration: Migrated indicates whether an individual lives in a district7 which is different to their birth district. In 2000, the share of young migrants under this definition was 9.7 percent, and 10.3 percent in 2010. The age-at-migration design requires identifying families who migrated exactly once, and both knowledge of the origin and destination as well as the ages of the children in the household at the time of migration. Like most Censuses globally, the Indonesian Censuses that I use here cover migration history in a rather sparse way. The only information is birth district and the location of residence 5 years prior. Collins and Zimran (2019) suggest exploiting differences in the place and year of birth among siblings. To identify families who migrated exactly once, I therefore select those families who have at least one child being born in the current district, 5 The 2000 Census data was obtained from Samuel Bazzi through Data Sharing Agreement with SMERU Research Institute. I use a version of the 2010 Census that is available at the Harvard Library Goverment Documents Group. 6 In both years, about 30 million children between 12 and 20 can be found to live with their parents. 7 Sometimes translated as ”regency”, the Indonesian terms are kabupaten (rural) and kota (urban). Districts are comparable to commuting zones in the US. 8 and at least one child born in a different district. Families with more than two different birth districts are not considered, as well as families who moved back and forth more than once between two districts. In most families, all children were born in one district; in fact, this is the case for 93 percent of all households with children in 2000 and 94 percent of all households with children in 2010. About five percent of households with children have migrated exactly once according to this definition, and only about one percent of the households have migrated more than once. The birth years of the two adjacent children - ordered by age - who are born in different districts determine the upper and lower bound of the year of migration. I construct an estimate as the midpoint of both birth years.8 From this I can infer an estimate of the age at migration for each child born in the origin district. I show that the magnitude of my baseline results remain unaffected after placing restrictions on the maximum difference of the two adjacent birth years (Section 4.6). The baseline restriction is a maximum error of four years. Educational attainment is captured in the Census by a categorical variable taking the values ”No education/less than primary school”, ”primary school completed”, ”junior secondary school completed”, ”senior secondary school completed”, and several distinctions for tertiary education. Unfortunately, the variable only shows completed levels of schooling. Hence a student who went to senior secondary school but did not graduate will be reported as a junior secondary school graduate. I construct several binary variables: 1. Primary12+ = 1 if an individual aged 12-20 has at least primary school completed. 2. JUNSEC15+ = 1 if an individual aged 15-20 has at least completed junior secondary school. 3. SENSEC18+ = 1 if an individual aged 18-20 has at least completed senior secondary school. 8 If the midpoint is not a round number, the estimate will be assigned the ”earlier” year, i.e. if one sibling was born in 1996 and one in 1999, the mean is 1997.5 and the migration year estimate will be 1997. 9 4. GFA = 1 if an individual aged 12-20 has completed the appropriate grade (primary, junior or senior secondary school) for their age. The measures of district quality ypoc and ypdc are, therefore, defined as the share of ”permanent resident”9 children who graduated from primary school (Primary12+), junior secondary school (JUNSEC15+) or senior secondary school (SENSEC18+) in the relevant age group. The shares are separately calculated for each cell defined by parent education group p10 , origin o, destination d, and birth cohort c11 . ∆podc based on GFA shows the share of children who have graduated from the appropriate level of schooling given their age. Grade for age allows me to include all children between 12 and 20, while taking into account that younger children have most likely not completed schooling yet. 3.1.2 Intercensal Population Surveys (SUPAS) My second, supplementary, sample is drawn from the 1985, 1995, and 2005 waves of the Intercensal Population Survey (SUPAS). These data offer a detailed education measure and several questions on migration, which allows me to both identify one-time migrants as well as derive the age at migration for adults. While the sample size is limited12 , the SUPAS allows me to analyze the effect of childhood neighborhoods on completed education without introducing a cohabitation bias13 . The SUPAS are household surveys with a small set of questions on the individual level, including years of education. They are carried out in the mid-period between two population censuses, for the first time in 1976. Due to data availability14 , I am using the 1985, 1995 and 2005 waves15 . Since the borders of Indonesian districts have been altered 9 Permanent residents are those individuals who have not moved at all during childhood. Here, I select those children who have been born in their current district and who have no siblings being born in another district. 10 I divide parents into two education groups, where the lower group includes parents without junior secondary degree whereas in the high education group at least one parent has at least junior secondary school completed. 11 For precision, I only include observations where both ȳpdc and ȳpoc are based on at least 30 permanent residents per cell. Section 4.6 shows the robustness of my baseline results relative to variations of this restriction. 12 SUPAS interviews up to 0.5 percent of the Indonesian population. The sample of respondents is representative at the district level, but not necessarily representative of the migrant population. 13 A sample consisting of adults who are still living with their parents and siblings is potentially very selective. 14 In 1976, only a smaller set of migration questions was included. 15 I downloaded the 1985 and 2005 waves from IPUMS international (Minnesota Population Center, 2020), the data excludes the province of Aceh in 2005. I use a version of SUPAS 1995 provided to researchers by BPS (Central 10 over time, in particular through district splitting, I fix districts to the 1985 borders to obtain harmonized neighborhoods. This results in 281 districts for the years 1985 and 1995, and 265 districts for the year 200516 . Besides data on the individuals’ education levels, the empirical design requires information to identify migration during childhood. The aforementioned waves of the survey contain a person’s district (kabupaten) of birth, the previous district, and the current district of residence. This information allows me to identify individuals who have moved exactly once in their life. If the previous district is different to the current district but the previous district equals the birth district, I assume that a person only moved once17 . Using a variable measuring years in current residence, I calculate age at migration for one-time migrants. Taking into account the trade-off between power and comparability, I restrict the data to the birth cohorts 1960 to 1984. In this sample, 74 percent of individuals never moved, 18 percent moved once, and 8 percent moved more than once.18 I restrict the sample to all individuals who migrated exactly once before their 21st birthday. To allow completion of their education, the individuals have to be at least 21 years old at the time of the survey. The focus on adults in this data comes with a limitation, which is the lack of parental information: most adults do co-reside with their parents, and SUPAS does not record information on parents who live in other households. Therefore, the measure of district quality change ∆odc Bureau of Statistics) in Indonesia. 16 The districts of the province Aceh are missing in the 2005 data. Districts vary in size and grow over time. The average district in my sample has 430,000 inhabitants in 1985, 570,000 in 1995, and 680,000 in 2005. They range between about 17,000 and 4,450,000 inhabitants. 17 This classification is imperfect as it will over count the number of individuals who moved once. It might be the case that someone moved several times, then moved back to their birth district, and then moved away from it to their current district. The information in the Supas does not allow identifying those earlier moves unless they are recorded in the variable measuring district five years prior. 18 The rate of one-time migrants is higher in this sample than in the Census data. The reason is that the SUPAS allows to infer migration during the entire life time, while in the Census I only measure migration that occurred between the birth of the oldest and the youngest child in the family. 11 is defined as the difference in average years of schooling of permanent residents19 , separately calculated for each cell defined by origin o, destination d, and birth cohort c. 3.2 Estimation Equations To study the effect of childhood migration on education, I first explore the relationship of migration and educational outcomes of children who live with their parents. I estimate a simple regression of the form yi = α + β M igrated + λo + λd + λc + X0p ξ + vi (1) where yi is an education outcome of child i. I control for birth district λo , current district λd and birth cohort fixed effects λc . The coefficient of interest β is likely upward biased, since we expect parents with high education to be both more likely to migrate but also invest more in their children’s education. To account for this endogeneity, I additionally control education of the household head and their spouse20 , interacted with gender of household head and spouse, respectively (denoted by Xp ). While parental education is an important determinant of both destination choice and children’s education, other omitted variables likely bias this estimate. However, it provides some sense of the potential magnitude of the causal effect and is therefore informative nonetheless. To identify the effect of migrating to a better destination, a naive approach would be to regress an individual’s educational attainment on some measure of destination quality. If destinations were assigned randomly, one could estimate yi = φ + βϑd + ei 19 (2) Permanent residents in this sample are those individuals who have not left their birth district before the age of 21. 20 Education is recorded as five dummy variables denoting the highest completed degree. 12 where yi is individual education and ϑd a measure of destination quality. Several issues arise. First, the effect of a destination might depend on how much time an individual has spent there. That is, spending more time in a favorable environment might have a stronger effect than spending little time. Second, it is likely that ϑd and the residual ei are correlated in observational data, because families with higher ability or willingness to invest in their children’s education could be more likely to move to better places. Finally, what is relevant for a counter-factual is not only the quality of the destination but whether and how much better it is than the origin. I address each of these three empirical challenges by using the age-at-migration approach developed by Chetty and Hendren (2018). First, I could estimate Equation (2) by each age at migration m separately, giving me a total of M equations of the form yi = φm + βm ϑd + ei (3) Second, due to selection into destination, β̂m might be a biased estimate. However, I will assume that this bias is unrelated to the timing of migration21 . That is, while higher ability families might be more likely to migrate to better areas, they do not do so when their children are younger. Under this assumption it is possible to identify a type of location quality effect with observational data: the location exposure effect. If there is a causal effect of location on the migrant child, then the effect should be stronger the longer a child was exposed to the location. I simply take the difference of two adjacent coefficients and define the location exposure effect at age m as γm = βm − βm+1 . Since the bias differences out, γ̂m will be an unbiased estimate of γm . γ̂m estimates the effect of spending an additional year at the destination. Third, let me define a quality measure that takes into account the quality of the origin and the destination for each birth cohort separately. The environment for a child could be very 21 I show in Section 4.5 that my results are not driven by a violation of this identifying assumption. 13 different in the same place depending on when they grew up there. I will measure the change in location quality as ∆Spodc = ȳpdc − ȳpoc , where ȳpdc and ȳpoc are educational attainment of category S 22 of permanent residents in destination district d and origin district o, respectively, of birth cohort c. The measure also distinguishes between children of parents p with low and high education.23 Stacking all M equations from (3) into one, I model the impact of childhood migration on educational attainment in Indonesia similar to Chetty and Hendren’s (2018) semi-parametric specification: yi = M X βm 1(mi = m)∆Spodc +αoc + φpm + X0p ξ + i (4) m=1 | {z location effects } β̂m are the M coefficients of interest which measure the location effect at age of migration m. From these coefficients I can construct the location exposure effects γ̂m . By including origin × birth-cohorts fixed effects αoc , each β̂m is identified from comparing children at different destinations who were born in the same year and grew up in the same district. Age-at-migration × parent-education group fixed effects φpm account for interruption effects of migration and other age- and parent-education specific unobserved factors.24 The vector Xp controls for parental education in the most flexible way possible: highest completed degree of the household head interacted with gender of household head, and highest completed degree of their spouse interacted with the spouse’s gender. I two-way cluster standard errors at the origin and the destination level. The identifying assumption of Equation (4) is that unobservable family characteristics are orthogonal to the timing of migration. To relax this assumption, I additionally estimate a 22 Depending on the outcome of interest, this will be the share of junior secondary school graduates or similar measures of educational attainment. 23 In high education families, the highest degree of schooling of at least one parent is at least junior secondary school. 24 Chetty and Hendren (2018) additionally include an interaction of location quality and birth cohort, because their ability to measure location varies systematically across children’s birth cohorts. This is not the case in my paper. 14 specification including household fixed effects.25 This allows us to control for all time-invariant household characteristics which might affect both migration choices and the investment in the child’s education. In the sample of adults (from SUPAS), parental education is not available. Therefore, I define location quality change as ∆YodcR = ȳdc −ȳoc , which is equivalent to ∆Spodc , with the exception that it does not distinguish between the two groups of parental education. In this sample, education is always measured in terms of years of schooling, denoted by the superscript Y R. Additionally, origin × birth-cohorts fixed effects would be too demanding in this sample, which, depending on the outcome variable, includes at most 50,000 observations. I control for origin by linearly including origin quality interacted with birth cohort fixed effects: yi = α + M X βm 1(mi = m)∆YodcR + |c=1 m=1 | 4 {z location effects C X } 1(ci = c) θc1 + θc2 ȳoc +φm + νi
{z control for origin quality (5) } Results In this section I first introduce descriptive evidence on the relationship between migration and education in Indonesia. Then, I estimate destination exposure effects on contemporaneous and completed education, and I show suggestive evidence for effects on labor market outcomes. Finally, I address threats to causal identification. 4.1 Descriptive Evidence on Migration and Education To study the effect of childhood migration on education, I first explore the relationship of district-to-district migration and school graduation rates of children between the ages of 12 and 20 who live with their parents in the years 2000 and 2010. This cross-sectional data is from the complete count Population Census and, therefore, covers the entire Indonesian population. 25 Results of this estimation are reported in Section 4.5 15 I estimate Equation (1) with yi indicating whether an individual has completed primary school, junior secondary school, senior secondary school or some tertiary education, respectively. Table 1 shows the results for the year 2000 in Panel (a) and for 2010 in Panel (b). The odd columns report the estimates β̂ from Equation (1), the even columns report the estimates after additionally controlling for parental education. As expected, the coefficients on migration are all positive in the odd columns. For example, Column (3) in Panel (a) shows, that 15 to 20 year old migrants were 6.9 percentage points more likely to have graduated from junior secondary school relative to non-migrants in 2000. This is a meaningful difference given the average graduation rate of 56 percent in this age range. However, the comparison with Column (4), which additionally controls for parental education, reveals that the high coefficient reflects positive selection into migration: Conditional on parental education, migrants are only 1.1 percentage points more likely to have completed junior secondary school. This pattern is similar for primary school completion and senior secondary school degrees, both in 2000 and 2010. Is internal migration not beneficial for children because negative disruption effects almost eliminate the gains from better education opportunities? Or does the small average effect mask heterogeneity in returns to migration? In the following subsection I explore the role of migration destination. 4.2 The Role of Migration Destination Which role does the destination play for education gains from internal migration? For adult migrants, productivity depends on how well their skills are transferable to the destination (Bazzi et al., 2016). As Suharti (2013) documents, there is substantial variation both across and within provinces in terms of average years of schooling26 , as well as in the qualification 26 According to Suharti (2013), average schooling by district ranged from two years in the lowest performing district to twelve years in the highest performing district in 2010. 16 of teachers. If these differences are reflective of factors influencing the ability of acquiring education (through the supply and quality of schools, through peer effects, or other factors), then it might be crucial for children where a family migrates to. Let me, therefore, turn to the effects of migrating to a better destination during childhood. N SEC Figure 1 shows the distribution of ∆JU for all children aged 15 to 20 who don’t live in their podc N SEC birth district, where ∆JU is the difference in average junior secondary school graduation podc rates among the permanent residents of the destination and the origin district, by birth cohort and parental education group. The distribution is almost perfectly centered around zero N SEC (average ∆JU = −0.01) indicating that migration flows both ways and about half of the podc children migrated to a district with higher quality, while the other half migrated to a district with lower quality. Do children benefit from migrating to better places? To explore the effect of district quality, I start by estimating Equation (2) which regresses education indicators of migrant children on the quality of the destination district. Quality is defined as the share of permanent residents in the destination district that have at least primary school, junior secondary or senior secondary completed, or have the appropriate degree for their given age (GFA)27 . Additionally, I control for origin district and birth cohort fixed effects as well as fixed effects for the education of the household head interacted with their gender. Table 2 reports the results and shows a strong relationship of education and destination quality. Children who migrated to a district with ten percent more primary school graduates among the permanent residents of their birth cohort are on average 6.8 percentage points more likely to have finished primary school themselves (Column 1). The association of junior secondary school completion and senior secondary school completion is of similar magnitude 27 Refer to Section 3.1.1 for more details. 17 with 6.0 and 6.1 percentage points, respectively. Given the average graduation means of my sample, this implies that a child who migrated to a district with 10 percent more junior secondary school graduates in their cohort is 8.1 percent more likely to have finished junior secondary school. A child who migrated to a district with 10 percent more senior secondary school graduates is 11.3 percent more likely to have graduated from senior secondary school. The last column summarizes the effect on GFA (grade for age). These results indicate that location matters. However, while controlling for origin fixed effects as well as parental education should partially capture selection into destination, there could be unobserved factors that draws families of children with a high education potential to better places. In that case, the results in Table (2) would overestimate the effect of destination quality. Therefore, I now turn to the results from the age-at-migration approach which causally identifies location exposure effects for migrants. 4.3 Exposure Effects on Graduation Rates Is there a causal location effect for childhood migrants? To answer this question, I will exploit differences in timing of migration of children who were born in the same year, grew up in the same district, and migrated to similar locations. The child who migrated earlier will be exposed to the destination for longer. If there is a causal location effect on education, it should be stronger the longer a child was exposed to the new environment. Recall that the Census data does not include precise migration histories. Therefore, I estimate year of migration based on differences in birth district and birth year among siblings. First, I estimate the effect of migration at different ages during childhood on the likelihood of having junior secondary school completed. Figure 2 Panel (a) shows the regression coefficients of Equation (4) with JUNSEC15+ (indicator for having junior secondary school completed) as the outcome. Every single coefficient β̂m shows the location effect at age m and 18 can be interpreted as a counter-factual. This means β̂m measures how much moving to a better district increases the likelihood that a child has graduated from junior secondary school. β̂4 = 0.45 implies that moving to a district with ten percent more junior secondary school graduates among permanent residents at the age of four increased a child’s likelihood for a junior secondary school degree by 4.5 percentage points relative to the counter-factual where the child had never left the birth district. β̂4 is identified by variation of different values of N SEC district quality change measures ∆JU among all children who migrated at the age of four. podc It is possible that there is selection into destination, i.e. parents with higher propensity to invest in their children’s education could be more likely to select high-quality destinations. All β̂m are therefore possibly upward biased. However, as stated in Section 3, the extent of selectivity should not vary depending on the age of the child. Calculating the differences in magnitude of β̂m for different ages at migration m produces a causal estimate of the yearly destination effect for the migrant child. Inspecting Panel (a) of Figure 2 reveals a clear downward pattern of β̂m . The declining pattern of the coefficients is consistent with positive location exposure effects from childhood migration. Children who are younger when they move gain more from migrating than children who migrate later and, therefore, have less exposure to the new environment. Panel (b) of Figure 2 shows the linear fit of all β̂m coefficients. The slope of the fitted line is -0.017, implying that each year of migrating earlier to a one standard deviation better district increases the migrant child’s likelihood to graduate from junior secondary school by 0.22 percentage points per year28 . To improve power, I can impose a linear structure on the exposure effect instead of estimating slopes for each age at migration separately. Equation (6) replaces the age at migration dummies by estimating the linear effect of age at migration interacted with ∆Spodc . This regres28 N SEC The standard deviation of ∆JU is 0.13. podc 19 sion still controls for disruption effects and origin quality. yi = β 0 ∆Spodc + β lin mi × ∆Spodc +αoc + φpm + Xp ζ + i | {z } (6) location exposure effect β lin captures the effect of migrating a year later to a destination of different quality (as measured by ∆Spodc ) and is equivalent to the slope of the fitted values of β̂m . Table 3 shows regression results for Equation (6). Besides the effect on junior secondary school graduation, I show the effect on primary school completion, senior secondary school graduation and grade-for-age (GFA). All coefficients imply that, in terms of educational outcomes, migrants converge to permanent residents at a yearly rate of 1.8 to 1.9 percent. Thinking about intergenerational mobility, do children of low educated parents benefit more from better destinations? I split the sample by parental education group, and estimate the destination effect on junior secondary school completion of the migrant child. Table 4 reports the results in the second and third column. I find that exposure to a better destination matters more for children of low educated parents (Column 2). This regression can be interpreted as estimating upward mobility: Spending an additional year in a one standard deviation better district increases the likelihood of a junior secondary school degree by 0.31 percentage points29 or 0.58 percent, given that in my sample 53 percent of children of parents without junior secondary school degree complete junior secondary school. Exposure effects on intergenerational education mobility are found to be of similar magnitude in Africa: Alesina et al. (2021) find that an additional year in a one standard deviation better region between the age of one to eleven increases the likelihood of primary school completion of a child of illiterate parents by 0.47 percentage points. Figure 1 shows that migration from lower to higher education districts are as common 29 N SEC Looking at the distribution of ∆JU for children of low-educated parents only, a standard deviation equals podc 0.18. 20 N SEC as migration from higher to lower education districts, i.e. ∆JU is both positive and podc negative. Does the direction of migration matter? I find that the effect is very symmetrical, moving to a worse district hurts about as much as moving to a better districts benefits a child’s graduation probability (Table 4, Column 4 and 5). If anything, the effect is somewhat stronger N SEC < 0 migrations. While a lot of research shows that education interventions for ∆JU podc have particularly high returns for young children, in this context, the environment before and around (potential) junior secondary school graduation might matter a lot. 4.4 Exposure Effects on Completed Education and Labor Market Outcomes So far, I have documented positive location exposure effects on education for childhood migrants. These effects are measured for young adults, just a few years after migration. How persistent are these effects and are they relevant later in life? I complement the analysis by constructing a second sample of one-time childhood migrants, based on the Intercensal Population Survey (SUPAS). This sample consists of adults who migrated exactly once before the age of 21. In this data I observe both completed education measured in years of schooling as well as several labor market outcomes. Unfortunately, parent characteristics are not available, and the sample size is by an order of magnitude smaller than the Census sample. I begin the analysis by estimating Equation (5). Figure 3 Panel (a) shows β̂m at every age at migration m, and the 95% confidence interval. The outcome here are years of schooling, which likely reflects completed education since individuals in my sample are at least 21 years old. The coefficients β̂m decline with age at migration, confirming positive destination exposure effects from childhood migration. Panel (b) implies that migrating a year earlier to a destination where permanent residents of the same cohort have on average a year more schooling compared to the origin is associated with 0.008 more years of education for the migrant. Migrating to a one standard deviation better district yields 0.017 more years of school. 21 Compared to my findings on graduation probabilities in Section 4.3, the effects are attenuated. However, the two analyses are not directly comparable since individuals in the SUPAS sample obtained education in earlier decades30 , when the supply of schools was much lower. The individuals in the SUPAS sample were born in 1960-1984, so that about 18 percent of the sample was twelve or older when the first primary school under the school expansion program INPRES was constructed in 1974. Only about 10 percent were born in or after 1978, so that they would enter school after the majority of primary schools had been constructed (Suharti, 2013).31 The lack of schools for those early born cohorts could limit the scope for positive location effects. Figure 4 plots β̂m for individuals who migrated not only during childhood, but until the age of 40.32 While migration during childhood has a causal effect on education, migration later in life is unlikely to have such an effect, since most individuals complete education in their late teens or early twenties.33 The figure therefore reveals the extent of selection into migration: the average value of β̂m for m ≥ 21 is δ = 0.23. By assumption, selection does not vary with age at migration. Do these positive location effects on education translate into better labor market outcomes? Unfortunately, data availability is a limiting factor as salary/wages are only included in the 1995 sample. All waves, however, contain information on the ”status” of a worker with the alternatives ”self-employed” ”wage/salary worker” and ”unpaid worker”34 . To obtain insights on labor market effects, I will again estimate the linear specification from Equation (6) with ∆YodcR defined as before, but yi being a binary variable which takes the value 1 if a person is 30 Only the birth cohorts 1980 to 1985 overlap in both samples. Individuals in the Census samples were born in 1980-1988 and 1990-1998, and entered primary school after the vast majority of schools under the INPRES program had been constructed. 32 Very few individuals in my sample migrated between the ages of 41 and 45, which is why I omit them from this figure. 33 In rare cases an individual might attend college at a higher age, therefore it is not entirely impossible for migration to have an effect later in life. 34 Additionally, there is ”unknown/missing” and ”not in universe”. The latter is an important category, since the variable is only identified on individuals 10+ who are working or are employed. The majority of inactive individuals are women. 31 22 employed in the formal sector (i.e. reports being a wage/salary worker) and 0 if she is working in the informal sector (i.e. reports being self-employed or an unpaid worker). About half of the individuals in my sample are employed in the formal sector. Additionally, I estimate the effect on log monthly income for the 1995 sample. The reduced form results (reported in Table 5) provide suggestive evidence for positive destination exposure effects in the labor market. The coefficient on formal employment is significant, but very small in magnitude (Column 2). It implies that migrating a year earlier to a one standard deviation better destinations increases the likelihood of being employed in the formal sector by about 0.2 percentage points or 0.4 percent. The effect on log monthly income is small and not significant. However, the sign is consistent with positive exposure effects. 4.5 Threats to Identification The main identifying assumption of the age-at-migration design is that unobservable family characteristics are orthogonal to age at migration of the child - implying that the bias on β̂m is constant across age at migration m. A violation of this assumption would arise if families who are more able or willing to invest in their children’s education migrate to better places when the children are younger. In that case, the upward bias would be higher for β̂1 compared to β̂6 or β̂11 , and this could diminish the effect of ∆Spodc by age at migration (i.e. the downward slopes in Figures 2 and 3 and the negative coefficient in Tables 3 and 4). I have two strategies to test this assumption using my baseline sample with Census data. First, I draw on Oster (2019) to estimate the extent of potential selection on unobservable characteristics into migration at certain ages necessary to entirely explain my results. Second, I control for unobserved family characteristics by adding household fixed effects to the estimation equation. Any unobservable factor such as the motivation to invest in the child’s education should be highly related to parental education. Therefore, it is instructive to observe coefficient stability 23 between the full model and one that omits all parent related covariates. In Table 6, the first column reproduces the baseline estimate of the full model (according to Equation (6)), while the second column estimates a model that omits all variables related to parental education and gender of the household head and their spouse. Relative to the full model, the coefficient in the restricted model has a higher magnitude (-0.018 vs. -0.027). Following Oster (2019), I use those coefficients and R2 values of the respective regressions to obtain a selection coefficient of proportionality of δ = 2.2235 . This implies that selection on unobservables would have to be more than twice as much as selection on observables in order to entirely undo my findings. Oster suggests a cutoff of δ = 1 for robust results. Alternatively, I can account for any type of unobservable family characteristics by adding household fixed effects to Equation (6). In doing so, I identify the exposure effect from children who belong to the same household, therefore relaxing the orthogonality assumption. In Table 6, Column (3) shows results from adding household fixed effects. Relative to the full sample, the number of observations in this analysis drops, because it restricts the sample to families with at least two migrants who are between 15 and 20 years old. For comparison, Column (4) repeats the baseline analysis on that smaller sample. If differential selection into destination was driving the exposure effects estimates, I would expect the magnitude of coefficient in Column (3) to be considerable smaller than the baseline result. It is, in fact, somewhat bigger in magnitude, but the coefficient is estimated with less precision. 4.6 Robustness Cohabitation bias. My sample of 12 to 20 year old children is restricted to those who live with their parents at the time that the Census is taken. However, the older the children, the more likely it is that they live outside of their parents’ households. In 2010, about 93 percent 35 As Oster (2019) suggests, I assume Rmax = 1.3 ∗ R̃ where R̃ is the R2 of the regression with full controls. 24 of children aged 12 lived with at least one parent, but that share falls to 88 percent among 15-year-olds and to 63 percent among 20-year-olds. Cohabitation bias arises if children who stay with their parents are systematically different from children who moved out. Since cohabitation rates fall as children get older, I expect the potential bias to be more severe for older children. Therefore, I successively exclude older children from the analysis to observe from Equation (6) with primary coefficient stability. Table 7 reports coefficients on ∆primary podc school completion as the outcome. Column 1 shows the baseline estimate of -0.019 with the full sample of 12 to 20 year old children. I then restrict to children age 12 to 18 (Column 2), age 12 to 16 (Column 3), and finally age 12 to 14 (Column 4). The coefficient is remarkably stable across all specifications with a high overlap of all 95 percent confidence intervals. I repeat the analysis for the outcome of junior secondary school degree and successively restrict the analysis to children age 15 to 19, 15 to 18, and finally 15 to 17 (Table A.1 in the Appendix). Coefficients are equally stable in this specification, confirming that cohabitation bias is not a concern for the location exposure estimates. Year of migration estimate. Due to the lack of detailed migration history in the Censuses, I have to construct the year of migration based on the birth years of siblings who were born in different districts (see Section 3.1.1). In the baseline regressions, I include all migrations which are based on siblings who are born at most eight years apart. In that case, my year of migration estimate could be up to four years earlier or later than the actual year of migration. To decrease this type of measurement error, I can place tighter restrictions on the difference between the two birth years that the year of migration is constructed from. Relative to the baseline with N SEC a maximum error of four years, the coefficient on ∆JU remains remarkably stable in a podc sample with a maximum error of three, two, or one year (Table A.2). Number of children in the household. Due to the construction of the age at migration, households in my sample have at least two children. The average number of children present 25 is 3.6.36 Families with many children might be systematically different from families with few children. To test the robustness of my estimate, I repeat the analysis for two different subsamples. Table A.3 shows estimates for families with four or more children, and for families with two or three children. The coefficients are statistically indistinguishable from each other across the different samples. Migration within and across province. If children migrate to an adjacent district, it is possible that they still have access to the same schools. To test whether the exposure effect is different for farther away migration, I repeat the analysis for a sample of children who moved across province borders (Table A.3, Column 4) and within a province (Column 5), respectively. Indeed, the latter coefficient is somewhat attenuated relative to the one from across-province migration, but they are statistically indistinguishable from each other. Precision of ∆Spodc . The measure of district quality change ∆Spodc is based on the average educational outcomes of children in parental education group × birth cohort × district cells. In the baseline results of Section 4.3, I exclude all observations where either the parental education group × birth cohort × district cell of the origin or the destination includes less than 30 permanent residents. To improve precision, I increase this size cut-off to 100, 200, and 300 permanent residents for each cell. Both the point estimates and the confidence intervals remain unchanged (Table A.4). 5 Conclusion In this paper, I study the effect of internal migration during childhood on education in Indonesia. Families migrate for various reasons, for example as a coping strategy after a negative shock such as a natural disaster or for better prospects in the future (Kleemans, 2015). Expected income in the destination is a major economic influence on the migration decision (Kennan and Walker, 2011). But what is the effect of internal migration on children? For them, 36 Children are defined by their relationship to the household head, not by their age. 26 migration can come at the cost of (temporary) disruption of school attendance, but with the chance of better education opportunities in the destination. In two cross-sections of the Indonesian population, I find a strong link between internal migration and children’s education, but most of it is explained by parental education. After accounting for this endogeneity, observational differences are small between migrant and nonmigrant children. I suggest that the low average effect masks heterogeneity with respect to destination. I find that half of children migrated to areas with better education outcomes among permanent residents, while the other half moved to districts with worse education outcomes relative to the origin. District quality - measured as the average education among non-migrant children - is highly correlated with education outcomes of migrant children in the destination. Exploiting the timing of migration, I show that the relationship is causal. I find that spending an additional year in a one standard deviation better district increases the migrant child’s likelihood to graduate from junior secondary school by 0.22 percentage points. Furthermore, I find positive reduced form effects on the likelihood of working in the formal sector as an adult. I show that my findings are robust towards the inclusion of household fixed effects, and that selection on unobservables would have to be twice as much than selection on observables to entirely explain my findings. Future research should try to understand which factors are decisive to make a district “high quality”. Potential factors include the number and quality of schools, peer effects or local (perceived) returns to schooling. While the human capital literature points out the particular importance of early childhood (Almond and Currie, 2011; Cunha and Heckman (2007); Heckman et al. (2013); Case et al., 2005), Deutscher (2020) finds that in Australia, exposure effects are most important during teenage years. For Indonesia, I find that all childhood years matter equally. In addition, starting out in a worse district and moving to a better one has 27 approximately the same effect than moving the other direction. This implies that moving to a worse district can “undo” the positive effect from a better district during early childhood. One mechanism that could be specific to the Indonesian context is the access to and the quality and cost of secondary schools. Remote rural areas are still underserved in terms of public secondary schools. In some areas, private schools meet the demands for secondary education, but at a lower quality. In addition, while officially only private schools can charge fees, the collection of alternative revenue is widespread (Bangay, 2010). Such fees might be prohibitive, since financial constraints are the predominant reason for children to drop out of school early (Suharti, 2013). The elimination of financial barriers could improve educational attainment overall, and in particular among children of poorer households. 28