Abstract
We investigate the impact of fertility and demographic factors on the Great Mexico–USA immigration by assessing the causal effects of sibship size and structure on migration decisions within the household. We use a rich demographic survey on the population of Mexico and exploit presumably exogenous variation in family size induced by biological fertility and infertility shocks. We further exploit cross-sibling differences to identify the effects of birth order, siblings’ sex, and siblings’ ages on migration. We find that large families per se do not boost offspring’s emigration. However, the likelihood of migrating is not equally distributed within a household. It is higher for sons and decreases sharply with birth order. The female migration disadvantage also varies with sibling composition by age and gender.
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Notes
To date, the household-level literature has mainly focused on the determinants of family migration investigating network effects (Winters et al. 2001; Stöhr 2015), the effect of the number of children on parental migration (Lindstrom and Saucedo 2007; Sarma and Parinduri 2015), and the effect of migration on fertility (Mayer and Riphahn 2000; Lindstrom and Saucedo 2002).
A well-established theoretical literature in economics rationalizes a causal link between children’s economic resources and their lifetime opportunities and adult outcomes (Becker and Tomes 1976; Thomas 1990). A related stream of empirical studies has investigated the role of family size, birth order, and sibling composition (by age and gender) on household investments in other forms of children’s human capital, such as health and education (see Black et al. 2005; Jayachandran and Kuziemko 2011; Jayachandran and Pande 2017, among others). In general, findings point to the little role of family size on children’s outcomes, while sibling structure and composition have more significant effects on offspring human capital investment.
To put the Great Mexican migration in historical perspective, it is worth noting that “as a share of Mexico’s national population, the number of Mexican immigrants living in the USA remained at 1.5% from 1960 to 1970, before rising to 3.3% in 1980, 5.2% in 1990, and 10.2% in 2005” (see Hanson and McIntosh 2010, p.1). In terms of absolute numbers, it is estimated that about 7 million Mexican immigrants entered the USA in the 1990s, 2.2 million did it legally while 4.8 million entered illegally (see Borjas and Katz 2007; Card and Lewis 2007). As a result, the Mexican-born population residing in the USA in 2000 was nearly 9.2 million, accounting for one-third of the US foreign-born population. Hence, the Mexican-born population of the late twentieth century appears historically unprecedented, being both numerically and proportionately larger than any other immigrant influx in the former and following century (Passel et al. 2012).
Using population censuses, Hanson and McIntosh (2010) report (in Fig. 2) that a significant proportion of men in Mexico start migrating around age 15, with emigration increasing sharply until approximately age 30 and decreasing thereafter, presumably as a result of return migration. By contrast, there is less youth migration among Mexican women and migration rates are relatively stable over the course of their lives.
Costs and benefits of migration may be unevenly distributed across both families and siblings within family, and hence bias the results. Moreover, unobservable parental preferences for children and old-age support through migration may positively co-vary. Stark (1981) and Williamson (1990), for instance, postulate that heterogeneity in parental preferences for childbearing and for migration are systematically related, and in a context such as Mexico where migration cum remittances is an essential lifeline to households of origin, they are generally positively related.
We check the robustness of our results to this sample selection, though, by also including the children of sterilized women and those using contraception in our sample. We use miscarriage at first birth as a source of fertility variation in this sample and results (reported in Table 10 Appendix A.1) appear to be unaffected.
We check the robustness of our findings to the inclusion of tied-migrants in the sample (about 13 percent of the sample) or those for which parents had migration experiences, adding parents’ migration status among the controls, in the analysis in Appendix A.4. The results in Table 13 are unaffected.
It is worth recalling that ENADID also collects information on migration episodes for temporarily absent household members, as long as migration occurred in the five years before the survey. Thus, ENADID only lacks information on permanent or long-term migration for non-household members.
This is the reason for the gender imbalance observed in our estimation sample (see Table 1).
Our computation for migrants of all ages in ENADID.
Our sample does not include children whose mothers are older than 54 years of age (9 percent of the total population aged 15–25) since fertility information was not collected from them.
Since our models estimated at the individual level include household fixed effects, we can only focus on children coming from households with two or more children. Household-level estimates, including households with single children, are reported in Appendix E.
We can include a control for both age and birth cohort because we use two cross-sectional surveys.
Another way to disentangle birth order and family size effects has been suggested by Booth and Kee (2009). They build a new birth order continuous index that purges family size from birth order and use this to test if siblings are assigned equal shares in the family’s educational resources. Since we prefer to estimate birth order effects using dichotomous indicators, we follow the approach described in Bagger et al. (2013).
Coefficients of all birth order indicators (including firstborns) are recovered using the method described in Suits (1984), whereby the coefficients on the dummy variables show the extent to which the behavior of each birth order deviates from the average behavior (of all birth orders).
This is to say that our identification strategy is able to isolate the within-family dimension of the impact of fertility on migration from the general equilibrium effect of population size. In some more data-demanding specifications reported in Appendix B we also control for municipality-year fixed effects.
See, for instance, Lewis and Linzer (2005). We also run estimates using White robust standard errors and the results of the analysis are unaffected.
Miscarriages or spontaneous abortions typically refer to any loss of pregnancy that occurs before the 20th week of pregnancy.
Other studies have considered different instruments such as twin births (e.g., Rosenzweig and Wolpin 1980; Angrist and Evans 1998; Càceres-Delpiano 2006) and sibling-sex composition (e.g., Angrist and Evans 1998; Fitzsimons and Malde 2014). Those instruments, however, are not suitable either for our data or for the Mexican context. Twin births cannot be used because we do not have administrative data, and although we make use of a large survey, we observe twin births only in 1.3 percent of families in our estimation sample. Sibling-sex composition is not suitable to the Mexican context because, for its very nature, it is likely to affect the fertility of parents who desire a small number of children. The idea behind the instrument is indeed that parents have an extra child just because they are not happy with the gender of those they already have (i.e., the group of compliers). This typically happens in Mexico when early parities are all females because parents have a son bias. However, average family size in Mexico is very large in our estimation period, the probability of having at least one son is also high, hence the instrument is unlikely to be relevant for a large share of the population.
More precisely, our unit of analysis are biological children in the same household.
Thus, in these estimates we also include individuals who do not have siblings, and look at whether they are more (less) likely to migrate than individuals with siblings.
Casterline (1989) stresses that in most societies pregnancy losses produce a reduction of fertility of 5–10% from the levels expected in the absence of miscarriages.
Other behavioral factors mentioned in Garcìa-Enguìanos et al. (2002) are caffeine, drug consumption, and induced abortions.
That is those for which we have parents’ characteristics.
Alternatively, the literature has been using (rare) long-spanning longitudinal data, which allow to link the childhood (background) family characteristics to grown-up children’s outcomes (Joffe and Barnes 2000).
Standard errors are clustered by municipality. Only children with mothers living in municipalities for which there are at least ten women in our baseline estimation sample are included in these regressions.
We test for the potential direct effects of miscarriage on child migration, via the emotional distress that a traumatic event such as miscarriage can cause to the mother, drawing on the work of van den Berg et al. (2017). The authors show that a child’s death represents one of the largest losses that an individual can face and has adverse effects on parents’ labor income, employment status, marital status and hospitalization. Similarly, we include child death and the duration of the pregnancy that ended in a miscarriage or a stillbirth as controls in the child migration equation, but we do not find ‘grief’ effects on migration. This analysis is reported in Appendix D (Table 20).
In this case, however, the effect on completed fertility is probably negligible.
In case the instrument is substantially contaminated by voluntary abortions, we would expect IV estimates to be biased in the same direction as OLS. Indeed, omitting subscripts and in the models without controls, if we define as M = β0 + β1S + v the migration equation, where M and S are child migration status and sibship size, respectively, and S = γ0 + γ1Z + u the sibship size equation (the first stage) and Z the instrument (abortion), β1,OLS = β1 + Cov(S,v)/Var(S) while β1,IV = β1 + Cov(Z,v)/Cov(Z,S), where Cov(Z,S) < 0 and sign(Cov(S,v)) = −sign(Cov(Z,v)). In case, for instance, unobserved mother’s total desired fertility is positively correlated with children’s migration and a substantial share of abortions are voluntary, both OLS and IV will be similarly upward biased.
By including child age and cohort dummies, with household fixed effects we are also de facto controlling for birth spacing between siblings.
The inverse of the standard errors of “netted migration” are used as weights.
Those currently deceased are excluded from our definition of siblings. This is done for two reasons: (i) 70 percent of deceased children in our sample died before the first year of life, 90% of them before the second one; (ii) the focus of our analysis is not on very young children so that we need to take into account siblings who actually “had enough time” to compete over household resources, and exclude accordingly infant deaths. In Appendix C (Tables 16–19) we report robustness checks related to concerns about the endogeneity of our definition of sibship size and birth order and estimate models based on ever-born children, i.e., currently alive or deceased, and the results do not change.
We are de facto also controlling for mother’s age at delivery, which is a linear combination of child’s age and mother’s age. As far as parental controls are concerned, we have more missing information for fathers than it is the case for mothers. As to keep the sample size constant, we further include a dummy variable for missing paternal information.
The Hansen J-statistic does not reject the “validity” of the instruments (i.e., orthogonality to the error term and correct exclusion from the main equation) in the overidentified model.
The interaction effect sibship size×female is instrumented using the interaction instrument×female, where the instrument is infertility or miscarriage depending on the specification.
As our two-step procedure relies on household fixed effects, when estimating separate regressions by gender only families with at least two sons and at least two daughters can be included in the estimates for males and females, respectively. In order to avoid such a sample selection, we rather adopt a pooled estimation including interaction effects with gender.
A similar empirical strategy is employed by Vogl (2013) to study sibling rivalry over arranged marriages in South Asia.
In line with the medical definition, stillbirth episodes are different from miscarriages: the former refer to a loss between the sixth and the ninth month, while the latter to a loss during the first five months of pregnancy.
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Acknowledgments
This paper benefited from helpful comments at various stages from the Journal Editor Klaus F. Zimmermann, two anonymous reviewers, Michael Clemens, Pascaline Dupas, Margherita Fort, Ilyana Kuzmenko, Luca Nunziata, Giovanni Peri, Maria Perrotta, Anna Piil Damm, Erik Plug, Nicole Schneeweis, Jenny Simon, Giancarlo Spagnolo, Alessandro Tarozzi, Shqiponja Telhaj, Daniela Vuri, Alan Winters and seminar participants at GREQAM Aix-Marseille, SITE-Stockholm School of Economics, Nova School of Business and Economics (Lisbon), University of Sussex, University of Bologna, University of Turin, University of Rome “Tor Vergata,” the 13th IZA Annual Migration Meeting (Bonn), the Royal Economic Society Conference (Brighton), the ESPE Conference (Izmir) and the AIEL Conference (Trento). All errors are our own.
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Appendices
Appendix A: Robustness checks
As described in Section 2, we restrict our sample to children of mothers for whom we have information on arguably exogenous variation in fertility (i.e., miscarriage and infertility shocks). Here, we run the same analysis on the full sample of women, including children of sterilized women and of women using contraceptives, in order to address potential concerns related to sample selection. Moreover, ENADID provides information on the migration status only for children cohabiting with their parents and for those temporarily absent but still considered as household members. In order to lessen the concerns with the potential selection bias this may introduce, we make a number of further sensitivity checks by changing the composition of the estimation sample.
First, Section A reports both WLS and IV estimates on the full sample, the one including children of sterilized women and of women using contraceptives, by using miscarriage at first birth as instrument. Table 10 shows that the estimated effect of sibship size is − 0.024 (s.d. = 0.017) very close to our baseline estimate of − 0.018 (s.d. = 0.023) in Table 6.
In Section A, we run a sample sensitivity check by focusing on the male (sons) subsample, since according to the data boys tend to marry and hence leave their parents’ household later compared to girls. In Section A, we focus on a sample of individuals aged 15 to 20 as a further robustness check: only few individuals are expected to be out of their origin household in this age group. Moreover, since we are able to recover migration patterns of all individuals who left in the five years prior to the survey, our measure of migration is very precise (very few individuals leave alone before age 15 and can be considered as permanent migrants) at the cost of a smaller sample size. In both cases, the estimation results are very similar to those commented in the main text, although some coefficients are less precisely estimated.
Finally, Section A addresses the biases potentially generated by the exclusion from the estimation sample of parents migrated in the past and episodes of children’s tied migration. We include in the estimation sample children with parents who ever migrated abroad, adding in the regressions an extra control (in the form of a dichotomous indicator) for parental migration. Table 13 confirms the statistically insignificant effect of sibship size on child migration when endogeneity is addressed.
1.1 A.1 Sample including sterilized women and those using contraceptives
1.2 A.2 Sons
1.3 A.3 Age group 15–20
1.4 A.4 Tied and parents’ migration
Appendix B: Poverty and further identification threats
In developing countries women’s infertility conditions may partly depend on material poverty, which affects women’s health. Failing to control for economic conditions may represent a threat to our IV estimates because poverty is also likely to affect children’s migration status. In the baseline estimates of Section 4.2, we took into account this potential threat by including some strong correlates of individual or household poverty, such as parents’ educational levels, age and municipality fixed effects. In this section, we run supplementary checks by estimating models including municipality by (ENADID) wave fixed effects and municipality by parent’s education fixed effects (years of education of the most educated parent, either the mother of the father, are interacted with municipality indicators). We report both OLS and 2SLS estimates.
Table 14 shows that the OLS estimates are not sensitive to the inclusion of additional proxies for poverty and family wealth, suggesting that the income and wealth channels are unlikely to be the main sources of the OLS upward bias.
2SLS results are reported in columns 1 and 2 of Table 15, respectively. They also serve as checks of potential concerns related to the miscarriage at first pregnancy instrument, which may also be affected by women’s living standards. The results confirm the robustness of our 2SLS estimates of family size effects to including alternative proxies of household poverty.
Appendix C: Sibship size including deceased children
Appendix D: Pyschological effects of miscarriage
As already mentioned in Section 3.2, miscarriage may be a traumatic event, creating a special bond between a mother and her children or a higher need for care, which may reduce the likelihood of offspring migration. Although we do not have measures of mother’s mental health, in this section we seek to shed light on this issue.
In a recent paper, van den Berg et al. (2017) show that a child’s death represents one the largest losses that an individual can face and has adverse effects on parents’ labor income, employment status, marital status and hospitalization. Based on that paper, we assume that a child death should produce more negative psychological effects on mothers than a miscarriage. We also assume that a miscarriage later in the pregnancy should produce more emotional distress than an early miscarriage (i.e., the intensity of the child-mother bond depends on the duration of the interrupted pregnancy). We test for “grief” effects by including in the 2SLS regressions an indicator variable for child death and, alternatively, the duration of the interrupted pregnancy because of stillbirth as control variables.Footnote 42 The coefficients on both variables, which are reported in columns 1, 2, and 4 to 7 of Table 20, respectively, are not statistically significant. Finally, in column 3 of Table 20, we leverage on the fact that we have two excluded instruments and run an overidentification test, which is based on the validity of the infertility instrument. In particular, we include the miscarriage indicator only in the second stage of a just-identified model. The coefficient on miscarriage is not statistically significant in the second stage, and suggests that it does not have a direct effect on child migration over and above the effect on family size, identified by infertility shocks. All these checks suggest that the direct effect of miscarriage on child migration is not a major issue in our analysis.
Appendix E: Household-level estimates
Results of the household level estimates are reported in Table 21. Column 1 shows that a unit increase in the number of children is associated with an average increase in the number of migrants of 0.02 (t = 12.3).
Column 2 reports the 2SLS estimate using the infertility instrument. The first stage shows a reduction of − 0.753 (t =-12.1) in the total number of children per woman who experienced an infertility shock, with an F-statistic of 145.4. The first-stage coefficient is a bit higher in magnitude than the one obtained in the child-level estimates (− 0.5), probably because of the inclusion of one-child households in the estimation. Indeed, women with only one child are those who may have suffered from more severe sub-fertility conditions and for whom the instrument is likely to be stronger (see Table 2 in the main text). In spite of the higher strength of the instrument, the second stage does not show any evidence of a statistically significant effect of fertility on migration. Column 3 reports the 2SLS results using the variation in the number of children generated by miscarriage. Also in this case the first-stage coefficient is highly statistically significant and negative, with an F-statistic of about 45. The negative impact of miscarriage on total fertility is smaller than the one exerted by infertility, yet it is quite large and precisely estimated, i.e., − 0.476 (t = − 6.7). Like for the previous instrument, also in this case no significant effect is detected in the second stage. The same happens in the overidentified model in column 4. In Table 22, we report the estimates of the same model as above while using an indicator for the household having at least one migrant child as dependent variable and results do not change.
These findings are consistent with those reported in Section 4.2, pointing to a positive correlation between family size and migration, but excluding a causal effect of the former on the latter. Also in this case, as with individual-level estimates, the larger magnitude of OLS estimates relative to the IV ones points to an upward biased estimate because of endogeneity, suggesting that families more likely to send young migrants abroad tend to also have more children.
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Bratti, M., Fiore, S. & Mendola, M. The impact of family size and sibling structure on the great Mexico–USA migration. J Popul Econ 33, 483–529 (2020). https://doi.org/10.1007/s00148-019-00754-5
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DOI: https://doi.org/10.1007/s00148-019-00754-5