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The Effects of Education on Mortality: Evidence From Linked U.S. Census and Administrative Mortality Data

  • Published:
Demography

Abstract

Does education change people’s lives in a way that delays mortality? Or is education primarily a proxy for unobserved endowments that promote longevity? Most scholars conclude that the former is true, but recent evidence based on Danish twin data calls this conclusion into question. Unfortunately, these potentially field-changing findings—that obtaining additional schooling has no independent effect on survival net of other hard-to-observe characteristics—have not yet been subject to replication outside Scandinavia. In this article, we produce the first U.S.-based estimates of the effects of education on mortality using a representative panel of male twin pairs drawn from linked complete-count census and death records. For comparison purposes, and to shed additional light on the roles that neighborhood, family, and genetic factors play in confounding associations between education and mortality, we also produce parallel estimates of the education-mortality relationship using data on (1) unrelated males who lived in different neighborhoods during childhood, (2) unrelated males who shared the same neighborhood growing up, and (3) non-twin siblings who shared the same family environment but whose genetic endowments vary to a greater degree. We find robust associations between education and mortality across all four samples, although estimates are modestly attenuated among twins and non-twin siblings. These findings—coupled with several robustness checks and sensitivity analyses—support a causal interpretation of the association between education and mortality for cohorts of boys born in the United States in the first part of the twentieth century.

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Data Availability

The complete count 1920 and 1940 censuses are publicly available at https://www.ipums.org. The linked data files used in this project are available upon request.

Notes

  1. In ongoing work, we are exploring the feasibility of implementing similar machine-linking procedures for a subsample of female children (in female-female sibling and twin pairs and female-male sibling and twin pairs). Unfortunately, the technical challenges involved in obtaining reliable links for girls are much steeper because of more frequent name changes at marriage. We discuss this issue in more detail in our conclusion.

  2. The assumption regarding place of birth is probably not entirely accurate, but the implications thereof should not be important. Furthermore, the potential benefits of relaxing this assumption should be weighed against the obvious downside of increasing the population of potential matches and, thereby, also the risk of declaring false positives.

  3. We could not distinguish MZ from DZ twins in our analyses, but a publication from the period in question—which estimates that among same-sex twin pairs born between 1922 and 1930, 50% were MZ (Hamlett 1935)—provides a rough guide. It is possible that the actual percentage we end up with in our analytic sample is somewhat lower (because pairs have to be discordant on education to contribute to our preferred within-pair estimates and rates of discordancy are likely to be lower among MZ twins), but we do not expect the difference to be especially large. Supplementary analyses of data from the Virginia Twin Registry show that among male MZ twins born between 1910 and 1920 (and still alive in 1987), the rate of discordancy was 36%. The same figure for male-male DZ twins born during the same period was 45%. If we take these percentages at face value, they imply that roughly 45% of discordant pairs [(0.36 / (0.36 + 0.45) × 100% = 45%] in our twin sample are likely to be MZ.

  4. The primary determinant of successful linkage was name commonality (i.e., the number of people living in the same state with the same first and last name). In supplementary analyses, described in the online appendix, we show that name commonality is orthogonal to educational attainment net of basic sociodemographic and geographic controls.

  5. There is room for debate about whether such weighting adjustments are necessary in the first place (Amin et al. 2015b; Boardman and Fletcher 2015). Our within-pair models provide protection against differential selection during the linkage stage (and other related concerns about external validity) by adjusting for all characteristics (observed or otherwise) that are shared within pairs. We suspect that this is why weighted and unweighted estimates closely agree with one another.

  6. Fixed-effects models for pairs of unrelated individuals will produce point estimates (but not variance estimates) that are equivalent to an unpaired model with identical controls. We opted to use pairs for this subsample to ensure consistency with our treatment of the other subsamples.

  7. The intrapair correlations presented in Table 2 for twins and non-twin siblings can be used to back out a rough estimate of broad sense heritability. If we assume that the twin sample is approximately 50% MZ and 50% DZ—and if we invoke the usual assumptions regarding equal environments, minimal gene-environment interactions, and comparable shared environments within pairs—then Falconer’s (1960) formula suggests that the broad sense heritability of age at death for members of this cohort was approximately 1.5 × (rtwins – rsiblings) = 1.5 × (0.21 – 0.12) = 0.14. We reiterate that this is a rough estimate.

  8. The unweighted estimates (not shown) were substantively identical.

  9. In supplementary analyses, we pooled the non-twin sibling and twin subsamples and fit a model interacting an indicator of subsample membership and years of schooling. The results suggest that the sibling and twin estimates are not significantly different from each other (p = .82). The same is not true for a comparison of the sibling and neighbor estimates, which produces significant differences at the p < .01 level.

  10. We also experimented with a three-category measure of education, where education was coded as less than 12 years, 12 years, and more than 12 years of schooling. The three-category version produced a very similar (and statistically significant) educational gradient in age at death. We present results from the two-category version because cell sizes for some of the comparisons in the three-category version (e.g., more than 12 years vs. less than 12 years of education) are small in the twin subsample.

  11. The estimates presented in Tables 3 and 4 give at least some reason to think that unobserved differences in genetic endowments within twin pairs may be less consequential for our analyses. The within-twin pair estimates that we provide represent a weighted average of estimates for MZ and DZ twins (Conley et al. 2006). Prior research, as noted earlier, suggests that male-male twin pairs born during this period were approximately 50% MZ and 50% DZ (Hamlett 1935). If we set the DZ estimates equal to the age-adjusted estimates that we obtain for non-twin siblings (who, like DZ twins, share 50% of their genes), we can calculate the MZ contribution to our within-twin pair results using Weinberg’s (1901) method. For the within-pair model that uses a linear parameterization of education, we get a coefficient of [0.347 − 0.338 × (1 − 0.5)]/0.5 = 0.356. The fact that we do not see much of a difference between siblings and twins (and between the sibling estimates and our inferred estimates for MZ twins, who are genetically identical) does not imply that genes are somehow irrelevant to a person’s educational attainment or longevity. It simply suggests that the additional endowments we are differencing out as we move from a within-sibling to within-twin pair model are not predictive of educational outcomes and survival. Prior work in other contexts has reached similar conclusions (Lundborg et al. 2016).

  12. This setup is conceptually similar to the type of bounding analysis performed in Rosenbaum and Rubin (1983) and Rosenbaum (1995) except that we are deploying it within the context of a within–twin pair fixed-effects model.

  13. These results are available upon request.

  14. We used the occupational income score of the householder (Hauser and Warren 1997), which in most cases meant the focal individual’s father as opposed to mother.

  15. The p value on the interaction term is .03.

  16. If it is the case that education (and, in particular, higher levels of education) has become an increasingly important vehicle for obtaining valuable health-enhancing resources—as work by Hayward et al. (2015), Masters et al. (2012), Sasson (2016), and others clearly suggests—then we would expect to see larger and potentially more discontinuous education effects for later cohorts of adults (e.g., Baby Boomers).

  17. Rates of smoking could also contribute to cross-cohort differences. The 1910–1920 cohort shared with its predecessors and immediate successors high rates of smoking initiation and continuation (Preston and Wang 2006), with little variation by education (Escobedo and Peddicord 1996). If anything, this should suppress education effects relative to later cohorts, where educational gradients in smoking were more pronounced (Ho and Fenelon 2015).

  18. Another possible extension would be to link to the National Death Index (NDI), which provides information on cause of death. Based on the conceptual model presented in Fig. 1, we would expect to see a more robust relationship between education and deaths that were caused by chronic diseases linked to unhealthy lifestyles (Masters et al. 2015; Phelan et al. 2004), as opposed to deaths from less preventable causes where education (and the various personal and social resources it affords) should be of less benefit.

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Acknowledgments

This research was supported by a grant (1R21AG054824-01A1) from the Eunice Kennedy Shriver National Institute for Child Health and Human Development (NICHD). Research support was also provided by the Minnesota Population Center, which receives core funding (P2CHD041023) from NICHD. Thanks are due to participants at several conferences and seminars for their constructive feedback and comments, and to the anonymous reviewers. All errors and omissions, however, are the responsibility of the authors.

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Authors and Affiliations

  1. Department of Sociology, Indiana University, 1020 E. Kirkwood Avenue, Ballantine Hall 744, Bloomington, IN, 47405, USA

    Andrew Halpern-Manners

  2. Minnesota Population Center, University of Minnesota, 50 Willey Hall, 225 19th Avenue South, Minneapolis, MN, 55455, USA

    Jonas Helgertz, John Robert Warren & Evan Roberts

  3. Centre for Economic Demography and Department of Economic History, Lund University, P.O. Box 7080, SE-220 07, Lund, Sweden

    Jonas Helgertz

  4. Department of Sociology, University of Minnesota, 909 Social Sciences, 267 19th Avenue South, Minneapolis, MN, 55455, USA

    John Robert Warren & Evan Roberts

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Contributions

Halpern-Manners, Warren, Roberts, and Helgertz conceived of the project; Helgertz designed and implemented the record-linking procedure; and Halpern-Manners carried out the analyses and drafted the manuscript, with input and contributions from the other three authors. All authors read and approved the final manuscript.

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Correspondence to Andrew Halpern-Manners.

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Halpern-Manners, A., Helgertz, J., Warren, J.R. et al. The Effects of Education on Mortality: Evidence From Linked U.S. Census and Administrative Mortality Data. Demography 57, 1513–1541 (2020). https://doi.org/10.1007/s13524-020-00892-6

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  • DOI: https://doi.org/10.1007/s13524-020-00892-6

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