The schooling repayment hypothesis for private transfers: evidence from the PROGRESA/Oportunidades experiment

Abstract

The schooling repayment hypothesis for private transfers predicts a positive relationship between the amount of parental investment in children’s education and the amount that adult children transfer to their parents. We provide evidence on the repayment motive using data from the Mexican conditional cash transfer program PROGRESA/Oportunidades (PO). PO pays a transfer to parents for sending their children to school. Thus, if private transfers from adult children to parents are in part repayment for parental schooling investments made in the past, then PO should decrease these transfers—parents were already exogenously compensated by the government for sending their kids to school and not to work. Exploiting the exogenous variation in the amount of cash transfers a household receives from PO for sending its children to school, we compare the private transfers received in 2007 by parental households who had children 0–16 in 1997 and started receiving the programs’ benefits in 1998 with the transfers received by similar parental households who started receiving benefits in 1999. Results suggest a repayment motive exists. That is, PO is causing adult children to transfer less resources to their parents.

1 Introduction

Are transfers from adult children to their parents partly repayment for schooling investments made by parents in the past? In the theoretical literature, in addition to the altruistic and exchange motives for private transfers, some authors model the relationship between parents and children as an implicit intergenerational contract: parents invest in their children’s education, when children are young, and receive a repayment from them when they become adults (Becker 1993; Cigno 1993; Cox and Stark 1994; Ehrlich and Lui 1991; Guttman 2001). These models predict a positive relationship between the amount of parental investment in children’s human capital and the private transfers that adult children give to their parents. We provide evidence of the repayment motive for these transfers using data from Mexico’s PROGRESA/Oportunidades program (PO hereafter).

Addressing the school repayment hypothesis empirically is challenging because the expenditures are generally endogenous to the ability of each child. Additionally, unobserved family characteristics affecting the transfers received from children might also be correlated with the human capital investment in children. For example, the altruism of the parents (reflected in high investments into children) might be transmitted to the children explaining large transfers on their part. As a result, for both developed and developing countries, previous empirical work examines the determinants of the transfers that adult children give to their parents and vice versa.¹ The specific evidence on the schooling repayment hypothesis is scarce and mostly based on estimating the effect of the educational attainment of adult children on the transfers that parents receive from them, but without controlling for the endogeneity of education.²

To provide evidence on the repayment motive, we exploit the features and randomized design of PO, a Mexican antipoverty program that pays a cash transfer to rural parents for sending their children to school. The schooling transfer from the program—the largest fraction of total program benefits for most households—is conditioned on children’s enrollment and substantial attendance to school. By design, when PO was first implemented in 1997, 320 rural localities were randomly chosen to participate in the evaluation sample of the program, and 186 rural localities were kept as controls. Households classified as poor by the program administration in treatment localities started receiving benefits in May 1998, whereas poor households in control localities were not incorporated into the program until December 1999. Nonpoor households did not qualify for program benefits regardless of their locality of residence. Both poor and nonpoor households in these localities have been followed over time. Thus, the conditionality of the schooling grant and the randomized design of the program provide a unique opportunity to look at the repayment motive and overcome the limitations of previous work. If private transfers from adult children to parents are in part repayment for parental schooling investments made in the past, then children exposed to PO should transfer less to their parents as adults, because their parents were already exogenously compensated by the government for sending them to school and not to work.

We use data from the 1997 baseline survey and the 2007 round of the PO rural evaluation sample. We focus on poor parental households that had children 0–16 years old in 1997. Any parent with at least one child older than 16 in 1997 is dropped from our sample.³ Nonpoor households are excluded from the main analysis, but are used to perform a falsification test.

There are two important aspects of our data that may complicate finding an effect. First, both parents and children are still relatively young in 2007 to be receiving and giving important amounts of private transfers, so it might be too early to detect any significant program effects. Second, it has been documented that PO increases children’s education (Behrman et al. 2005, 2011; Schultz 2004) and improves their health (Gertler 2000; Behrman and Hoddinott 2001). These improvements should lead to an increase in children’s earnings which—under relatively weak assumptions—should generally lead to an increase in transfers to parents. That is, the combination of more schooling and better health works against finding evidence of the repayment hypothesis. Nevertheless, despite this, as discussed later, we do find some evidence consistent with the repayment motive.

Our identification strategy exploits the exogenous variation in the amount of cash transfers a parental household receives from PO for sending its children to school. This variation is induced by the age of the child in 1997, before the start of the program, and the year the household was incorporated into the program. Using the child’s age in 1997 and the year of treatment, we calculate the child’s potential years of exposure to the program by 2007 assuming that a given child enters first grade at age 6, and abstracting from any grade repetition. Thus, our exposure measure is exogenous because it does not depend on actual participation in the program or school enrollment.

The ideal dataset would allow us to observe the private transfers that parents receive from each child in 2007, so we can link these transfers with our measure of the individual child’s exposure to the program. Our data have information on the total amount of private transfers received by the parent from his children and from other sources in the previous year, but we do not observe the transfers given by each individual child. In addition, our data has only information on private transfers from donors who do not belong to the household, so we do not observe any transfers from children who still live in the parental household in 2007. As a result, we estimate the effect of the number of children in different age groups that a parental household had in 1997, who are absent in 2007, interacted with a dummy for early treatment, on the amount of private transfers the parental household and the head receive from children in 2007.

Despite the limitations of our data, we find that longer exposure to PO decreases the transfers coming from children potentially exposed to the program, and not those coming from children who left the household before the start of the program, or from other friends and relatives. Hence, we interpret our results as suggestive evidence in favor of the repayment hypothesis.

We conduct a number of robustness and additional empirical checks to further support our findings. For example, we perform a falsification test by re-estimating our transfer equations using the sample of nonpoor households and find no significant effects of our key interactions, which is reassuring. In addition, we use the information of poor individual children in our sample to estimate the effect of early treatment by age on the probability and motives of migrating, and find no significant effects. So, our main results cannot be attributed to the effect of the program on the migration of children with longer exposure either.

2 Empirical strategy and descriptive statistics

Our identification strategy exploits the exogenous variation in the amount of cash transfers a household receives from PO for sending its children to school. This variation is induced by the age of children in 1997 and the starting date of treatment of each household. Table 1 shows in column 6 the potential years of differential exposure to PO by 2007 for a given child, depending on her age in 1997 and the moment her locality was incorporated to the program (May 1998 or December 1999). For calculating the years of exposure, we assume the age-grade relationship shown in columns 1 and 2.⁴ The actual transfers from the program are conditioned on the school grade and not on the age of the child, thus in Table 1 we are abstracting from any grade repetition or from re-entry of older children to school after the program was implemented in their localities. Our measure is a proxy for the schooling costs that parents were compensated for by the program and it is not correlated with unobserved characteristics of the household or children that affect schooling choices or the actual years of exposure to the program.

Table 1 Children’s exposure to PROGRESA/Oportunidades based on age and year of treatment

Table 1 shows that depending on the age of the child in 1997, the additional years of schooling compensation received from into PO varies between 0, 1 and 2 years. Note that given our assumptions about the age-grade relationship and grade progression, children who were 14–16 years old in 1997 had no exposure to PO educational grants, regardless of the community they lived in. However, grade repetition seems to be an issue in our sample.⁵ Thus, a number of children who were 14–16 years old in 1997 might actually have received the benefits of the program. Hence, we will consider this to be the case from now on.

Table 1 also shows the educational level—primary or secondary—financed by those additional years of program support. For children 6–10 years old in 1997, the early treatment financed part of their primary education, whereas for children 11–13 years old in 1997, it financed their secondary one. Finally, in column 3, it can be seen that these (adult) children are still quite young by 2007.

The data allow us to create parent–child pairs for each child the head of the parental household had in 1997. We also observe sociodemographic characteristics of both heads and children. Ideally, we would like to observe the private transfers each individual child gave to the head and link this information with the individual characteristics of the head and child. But, as mentioned above, this information cannot be disaggregated by child. We only observe whether the parental household, and who within the household, received a private transfer from another household, the amount, and whether the donor was a child who left the parental household before 1997, a child who left the parental household after 1997, or someone else (a relative, friend, neighbor or other).⁶ Due to these data limitations, our unit of observation is the parental household head and our outcome variable is the total private transfers the head receives from his children and other types of donors.

To provide evidence on the repayment motive, we estimate the following equation by OLS:

$$T_{hl} = \alpha + \beta_{1} X_{hl} + \beta_{2} D98_{l} + \mathop \sum \limits_{g}^{{}} \gamma_{g} C_{ghl} + \mathop \sum \limits_{g}^{{}} \delta_{g} \left( {D98_{l} \times C_{ghl} } \right) + \mathop \sum \limits_{g}^{{}} \rho_{g} A_{ghl} + \mathop \sum \limits_{g}^{{}} \pi_{g} \left( {D98_{l} \times A_{ghl} } \right) + \phi_{l} + \varepsilon_{hl}$$

where $T_{hl}$ are the private transfers received by the head of parental household h in locality l; $X_{hl}$ are characteristics of the head;⁷ $D98_{l}$ is a dummy equal to 1 if the parental household is in a PO locality that started treatment in 1998, and 0 otherwise; $C_{ghl}$ and $A_{ghl}$ are the number of children in age group g the head of parental household h had in 1997 and those who are absent from the parental household in 2007, respectively; $\phi_{l}$ is a locality fixed effect intended to capture any shock at the locality level that could affect the amount of transfers sent to the parental household;⁸ and $\varepsilon_{hl}$ is an idiosyncratic error term. Following the exposure differentials shown in Table 1, the four age groups we consider are: 0–5, 6–9, 10–13 and 14–16 years old in 1997, before the start of PO.⁹

The coefficients of interest are $\pi_{g}$, because they measure the effect of having an additional child in age group g in 1997, who is absent from the parental household in 2007, and who potentially had more exposure to the program because it started in 1998 in her locality. We interpret these coefficients as the effect of PO on the private transfers due to a repayment motive, because we are already controlling for $C_{ghl}$, $D98_{l} \times C_{ghl}$, and $A_{ghl}$. If the repayment hypothesis holds, we expect an insignificant coefficient for our key interaction ($D98_{l} \times A_{ghl}$) of the 0–5 age group, and negative and significant coefficients for the older age groups because, as shown in Table 1, only children age 6 and older in 1997 in early treated localities had a longer exposure to the program’s schooling grants. The income effect of receiving the PO cash benefits for a longer time on private transfers is appropriately controlled for with the interaction of the number of children in different age groups in 1997 and the early treatment dummy ($D98_{l} \times C_{ghl}$).¹⁰

Table 2 presents the descriptive statistics of parental household heads and their households by the date their treatment started (May 1998 or December 1999). The last column shows the difference in means between these two groups. The mean private transfers received individually by the parental household head during the previous year to the 2007 survey are small: 92 pesos for those receiving treatment early and 58 pesos for those receiving treatment later. About 84 % of the private transfers received by the head come from his children and, of those, 74 % come from children who left the household after 1997. On average, we find no statistically significant difference for the transfers received by the heads receiving treatment early or later. However, simple means do not allow us to observe the variation caused by the ages of children and absent children, neither do they allow us to separate the effect of the program on the income of the parental household. For parental households, private transfers received in 2007 are larger. For both groups, about 54 % of the private transfers come from the head’s children and, of these, 77 % come from children who left the parental household after 1997. For both groups, about 46 % of private transfers come from other donors, whereas for heads alone only 4–16 % do.

Table 2 Descriptive statistics by year of treatment start

The mean differences between those receiving treatment early and later are very small and never statistically significant for almost all of the characteristics reported in Table 2. Particularly relevant is the fact that the years of schooling of the head and the number of children he had in 1997 are balanced, since these variables can be taken as proxies of the relative (lifetime) resources available to parents in the future. Expenditures per capita and the total value of households’ assets in 1997 are balanced as well. So, the PO assignment still looks random, even if we are selecting a particular subsample of the evaluation data, which is reassuring. The only statistically significant mean differences between parental households receiving treatment early and later are those in the children’s average years of PO exposure. For the average parental household treated early, the program financed between 1.6 and 2 years more the education of its children.

In our reported estimations, we only control for the individual characteristics of the head of the parental household, because those are more likely unaffected by the program. We do not control for parental household size and its composition, the total value of its assets and the number of members who are absent in 2007, because PO could potentially affect these outcomes.¹¹

3 Results

Table 3 shows the results from OLS regressions on the amount of private transfers received by the parental head (Panel A) and household (Panel B) in 2007. Only the coefficients on the early treatment dummy and the key interactions with the number of children in different age groups in 1997, who are absent in 2007, are shown. In all estimations, the standard errors are clustered at the locality level.

Table 3 OLS regressions for private transfers received in 2007 by poor parental households and heads

Column 1 shows the results for the transfers received from children. For both parental heads and households, the key interactions for children older than 6 in 1997, absent in 2007, are negative, but not statistically significant. We interpret these results as the first piece of suggestive evidence supporting the repayment hypothesis, because absent children with longer program exposure, seem to transfer less to their parents. Further, the effect increases in absolute value as we consider older children. Pre-intervention data from 1997 show that at age 11, children start dropping out of school and start participating in the labor market. Thus, when children turn 11 years old, the school-work trade-off becomes important for parents. Hence, children of that age who continue to go to school are more likely to feel more indebted to their parents in the absence of the program. The trade-off would be even more important for children age 14–16 in 1997, who have the largest negative effect on the private transfers received by early treated heads. They have even better labor market opportunities and a greater probability of being absent from the parental household.¹²

In column 2, for the transfers received from children who left the household after 1997, who might have been exposed to PO, the key effects are similar to those in column 1. Interestingly, some become larger and statistically significant. In particular, in Panel A the coefficient for the oldest group becomes significantly different from zero at 5 %. If instead of a two-tailed t test, for each coefficient we test the null hypothesis that they are nonnegative versus the alternative that they are strictly negative, we reject the null for the estimate for children 10–13 years old in 1997 (−66.9 pesos) at 10 % and the one for children age 14–16 (−185.2 pesos) at 2 %. This reinforces our interpretation of these coefficients as evidence of repayment, because these transfers are coming precisely from children potentially exposed to the program. In Panel B, a similar pattern is observed for the transfers received by the parental household. An additional child age 14–16 years old decreases the transfers received by the household by 215 pesos per year, effect statistically different from zero at 10 %. For a one-sided test, we are able to reject the null that this coefficient is nonnegative versus the alternative that it is strictly negative at 5 %.

In column 3, in both Panels A and B, the same key interactions for the transfers received from children who left the household before the start of the program are positive and mostly smaller in magnitude than those in column 2. So, the negative effects of the number of absent children exposed longer to PO on the transfers received from children are mostly due to the negative effects on the transfers from children who left the household after the program (column 2), and not before.

Finally, column 4 shows the results for the private transfers received by the parental head and household from other donors (friends, neighbors and relatives other than children). The key interactions are relatively small for these transfers and are not statistically significant as would be expected if the differential exposure of absent children to PO affected only the transfers from children, due to the repayment hypothesis, and not those from other donors.

4 Confounders, robustness checks and falsification test

Even after controlling for relevant covariates, some confounders could potentially undermine our results. PO is intended to increase its beneficiaries’ health and their children’s education, and has been found to be effective in doing so (Gertler 2000; Behrman and Hoddinott 2001; Behrman et al. 2005, 2011; Schultz 2004). Precisely because of this, we do not control for health and education outcomes in our estimations. Still, an improvement in these factors can potentially increase adult productivity and earnings, and also the transfers paid to parents as a result. However, note that in such case, our results would be attenuated.

Regarding health, the program could make early treated parental households healthier on average than later treated ones, which could contaminate our results if adult children transfer money to their parents not only due to a repayment motive, but as a response to a health shock affecting them. However, Bautista Arredondo et al. (2008) find that seniority as a beneficiary of the program, measured by the year of enrollment, is not correlated with differences in the health level of beneficiaries or their utilization of medical services in 2007.

In turn, more education could have additional negative effects on the transfers given to the parents for at least two reasons. First, in order to continue studying, adult children may leave the parental household, delay their entry into the labor market (Behrman et al. 2011; Skoufias and Parker 2001), and thus also their transfers to parents.¹³ Second, education may make the adult children less reliant on social networks in their localities of origin, and so less concerned about any social punishment for decreasing their support to their parents.

Another potential confounder is the migration of children. If PO induces treated children to leave the parental household for work, it would be more likely to observe transfers from them to their parents. This behavior would work against our results. The opposite would hold if such effect is negative and our results could not be entirely attributed to the effect of lower repayment. Similarly, as we mention above, if treated children migrate in order to acquire more education, their entry into the labor market may get delayed causing them to have less resources to transfer.

Table 4 presents the results from OLS regressions on the probability that the adult child is absent in 2007, and—conditional on being absent and having completed a migrant questionnaire—the motive for migrating.¹⁴ All estimations control for an early treatment dummy; characteristics of the child;¹⁵ a female dummy; the number of siblings, and the number of male siblings; characteristics of the parent;¹⁶ and locality fixed effects. The key independent variables in these regressions, i.e. those measuring the effect of additional exposure to PO are the interactions between the early treatment dummy and the dummies for the 1997 age of the child. In all estimations, the standard errors are clustered at the locality level.

Table 4 OLS regressions for the child’s migration probability and motives

Column 1 shows that the effect of the early treatment dummy on the probability of being absent in 2007, and the interactions of this dummy with the age of the child, are small and not statistically significant (the omitted category are children age 0–5).¹⁷ Thus, our main results in Table 3 cannot be explained by the effect of PO on the children’s decision to leave the parental household.

Columns 2–5 show the results of OLS regressions on the motive for migrating for the sample that did migrate. The early treatment dummy by itself has no statistically significant effect on any motive for migrating, except for the negative effect of 17 % on the probability of migrating for marriage. For studies and work, none of the interactions of the early treatment dummy with the age dummies are statistically significant after controlling for the main age effects (not shown). This confirms that children with longer PO exposure in our sample are not decreasing their transfers to their parents because they are more likely to leave the parental household to continue studying rather than for work. For marriage, the key interactions are positive and significant, especially those for children who were 10–16 years old in 1997. However, given the magnitude of the negative effect of the early treatment dummy alone (−0.17), the positive interactions suggest that the effect of being in an early treated locality on the probability of migrating for marriage for children age 10–16 years old, compared to children who were their same age in 1997 in control localities, is close to zero.¹⁸ Overall, the results in Table 4 favor our interpretation of the results in Table 3 as evidence of the schooling repayment hypothesis for private transfers.

Finally, to further check the validity of our results, we perform a falsification test. We run the same regressions presented in Table 3, but using data for nonpoor parental households, i.e. those ineligible for PO.¹⁹ Some studies show that the program has had a positive effect on the education of noneligible children in treatment localities (Bobonis and Finan 2009; Lalive and Cattaneo 2009). Hence, if children transfer money to their parents partly because of repayment, the program has changed the education of noneligible children, but not this motive.

Table 5 shows that, as expected, the effect of early exposure to the program captured by the interaction of the number of children in different age groups in 1997 who are absent in 2007 with the early treatment dummy is never statistically different from zero. If we perform one-sided tests for the null that each of these key interactions is nonnegative versus the alternative that it is strictly negative, we are not able to reject the null at any conventional level for any of them. These results further suggest that our findings are a consequence of the additional exposure to PO, and not of some other circumstance that occurred in the localities treated early, or to education making the adult children less reliant or concerned about the social networks in their localities of origin.

Table 5 OLS regressions for private transfers received in 2007 by nonpoor parental household and heads

5 Additional empirical checks

Lastly, we check for any effects on parental assets and current per capita consumption in the parental household in 2007 to provide some indirect evidence on whether parents of children treated in 1998 anticipated lower transfers from them as adults. Table 6 presents OLS regressions for the logarithms of the value of parental household assets and consumption per capita in 2007.²⁰ In both estimations, we include the early treatment dummy and the number of children of different ages in 1997. We do not include variables for the number of children who are absent in 2007. The interactions of interest are those of the number of children in different age groups in 1997 with the early treatment dummy, which capture whether the parent anticipated that the PO schooling subsidy could lower the transfers he would receive from his children in the future, before any of them actually decided to leave the household. If he did, we might observe a higher asset accumulation and no effect on current consumption.²¹ In both estimations in Table 6, we control for the same characteristics of the parent as in Table 3.

Table 6 OLS regressions for parental household assets and consumption in 2007

In column 1 of Table 6, neither the effect of the early treatment dummy nor those of the relevant interactions are statistically significant for the log of household assets. We take this as rough evidence of parents not increasing their asset accumulation, despite the fact that the effect of the PO subsidy received would tend to increase asset accumulation.

In column 2, for the log of total expenditure per capita in 2007, the early treatment dummy and the key interactions with age have mostly small and not statistically significant coefficients. Only the interaction for the number of children age 14–16 in 1997 is negative, the largest in absolute value, and marginally significant at 10 %. So, having an additional child age 14–16 in 1997, who started treatment early, decreases consumption per capita in the parental household in 2007 by 9.1 %. This result is consistent with the interpretation we have been giving to our main results, because the largest reductions in transfers, and the only ones that are significant, are due to the number of early treated children in this same age group. Taken together, the results in Table 6 suggest that parents did not expect the reduction in transfers potentially due to lower repayment. However, this evidence is not conclusive.

6 Conclusions

In this paper, we provide suggestive evidence of a repayment motive for the private transfers that adult children give to their parents by exploiting the features and experimental design of PO, a Mexican antipoverty program that pays a cash transfer to rural parents for sending their children to school. Even though in our data both parents and their (adult) children are still relatively young to be receiving and giving important amounts of transfers, we find that that the number of absent children who were 14–16 years old in 1997 and had longer exposure to the program reduces the amount of private transfers that parents receive from children in 2007.

Our paper contributes to the literature on the motives for private transfers from adult children to parents by providing suggestive evidence on schooling repayment, and to the evidence on the medium-term unintended effects of PO. To our knowledge, this is the first paper that looks at the effect of a conditional schooling subsidy on the transfers that parents receive from their adult children who were exposed to the program, i.e. the first to study the intergenerational effects of the program. These effects are of utmost importance given that the design and stated goal of PO is precisely to break the intergenerational transmission of poverty. Our results suggest that the effect on intergenerational transfers from children to parents is negative.

Given the relevance of this result, we further provide crude evidence that parents—at the start of PO—did not expect to be receiving less transfers from their children in the future. As a result, they do not seem to have set aside resources via savings or the accumulation of assets in order to use them for consumption purposes once their children started to transfer less money to them. Thus, the first generation of PO parental households might be worse-off in the future, especially because the largest part of the program transfer, which is the schooling subsidy, is temporary. From a distributional point of view, for the first generation of beneficiary children, the program could become a positive net transfer from society, because it allowed them to get more education, and to earn more and transfer less to their parents as adults. Whether these children repay the government for their schooling through taxes depends crucially on whether they get jobs in the formal sector, where tax compliance is usually higher, after graduating from the program. However, more research seems due given that we are not able to observe other forms of non-monetary support, like caregiving time, and given the other limitations of our data already mentioned.