Abstract
World War II and its subsequent GI Bill have been widely credited with playing a transformative role in American society, but there have been few quantitative analyses of these historical events’ broad social effects. We exploit between-cohort variation in the probability of military service to investigate how WWII and the GI Bill altered the structure of marriage, and find that it had important spillover effects beyond its direct effect on men’s educational attainment. Our results suggest that the additional education received by returning veterans caused them to “sort” into wives with significantly higher levels of education. This suggests an important mechanism by which socioeconomic status may be passed on to the next generation.
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Notes
See, for example, Mare and Maralani’s (2006) model of intergenerational mobility, in which the positive relationship between parental education and the education of one’s offspring is enhanced by the impact of education on marital sorting and mitigated by the impact of education on fertility.
In a related study, Lemieux and Card (2001) estimated the effect of the Canadian GI Bill on education and earnings.
Recent studies have documented that the Vietnam War draft lottery had an impact on nonwage outcomes such as marital status, migration, and health. See, for example, Angrist and Chen (2011), Conley and Heerwig (2011), McCarthy (2012, 2013), and Malamud and Wozniak (2012). Similarly, Galiani et al. (2011) estimated the impact of military service on crime using the random assignment of men to military service in Argentina.
Bedard and Deschenes (2006) found that cohorts with higher rates of WWII participation were more likely to die prematurely (excluding deaths attributed to combat) and that higher death rates among these cohorts are associated with higher rates of military-induced smoking. Yamashita (2008) and Fetter (2013) found evidence of a fading relationship between GI eligibility and homeownership, and Page (2007) showed that the children of affected cohorts had lower probabilities of repeating a grade.
Seminar participants have proposed two alternative identification strategies that we feel are less compelling than cohort-level variation in benefit eligibility. One suggestion has been to follow the approach used by Stanley (2003), who identified the impact of GI benefits using variation in take-up rates across eligible cohorts. The drawback to this approach is that we do not have a solid understanding of why take-up rates varied. Whatever underlies the variation might also have affected marital sorting. The second suggestion is to use cross-state variation in mobilization rates, similar to Acemoglu et al. (2004). However, that study also documents correlations between state mobilization rates and other state characteristics, and those characteristics may be correlated with marital outcomes. In previous work, Page (2007) found that estimates of the impact of GI benefits that used state-level mobilization rates as an instrument for eligibility were sensitive to the inclusion of state-level control variables.
If the treatment and control groups were exactly the same size, and were pulling from exactly the same pool of women, then a reasonable approximation of the partial equilibrium effect would be one-half of the estimated difference between the treatment and control groups. As more cohorts are added to the sample, however, the assumption that both groups are pulling wives from the same pool of women becomes increasingly tenuous, and more assumptions need to be made to estimate the magnitude of the partial equilibrium effect.
For the sake of completeness, we also estimated equations in which we replace %WWII and %Korea with a variable that measures the fraction of the cohort who served in either war. For the reasons described earlier, this specification does not seem ideal. Nevertheless, it produces estimates that follow the same pattern as our main estimates. Like our main estimates, they are positive and often statistically different from zero, but they are generally smaller in magnitude than the estimates produced by Eqs. (1a)–(3a).
The exception is for individuals born in very poor southern states. Our results are robust to the exclusion of these states.
Family background variables include father’s education (PSID), and whether the individual lived with both parents at age 16, his father’s occupation at age 16, and his parents’ educational attainment (OCG). The OCG data also include retrospective reports on parents’ income when the individual was age 16. The parental income data are reported in bins. It is unclear whether respondents are reporting nominal or real dollars. This makes it difficult to interpret statistical analyses using this variable because different cohorts turned 16 in different years. In a few specifications, we find that the fraction of individuals coming from high-income families is larger among the younger cohorts in our sample, which would be consistent with estimates of GI Bill effects that are biased downward. Because the OCG data do not include quarter of birth, these analyses are based on, at most, 15 data points.
This figure comes from authors’ calculations based on the 1980 census.
This figure is from authors’ calculations based on Army enlistment records available online through the National Archives Access to Archival Database (AAD) (http://aad.archives.gov/aad/). Estimates are not expected to differ for other branches of the Armed Forces.
Cohorts born in the early part of 1923 may have been 19 at the time they were drafted because the draft age was lowered from 21 to 18 in November 1942.
All our estimates exactly match Bound and Turner’s except for our estimate based on the 1923–1932 cohorts: 0.42, versus Bound and Turner’s published estimate of 0.30. The comparable estimate in the working paper version of their study (Bound and Turner 1999) is 0.42. Because the two sets of estimates are based on exactly the same specification, and all the estimates generated by the other samples match, we believe that the difference between the estimates for the 1923–1932 cohorts is likely due to a typographical error.
As would be expected from Fig. 1, the estimates in columns 1–4 barely change.
For example, Mettler (2005:10) stated, “their deservingness for the generous benefits was considered to be beyond question, given that through their military service they had put themselves in harm’s way for the sake of the nation.”
Of course, there are many differences between the WWI and WWII eras, which might lead to different estimates. For example, U.S. troop involvement in WWI was more concentrated over time and not as broad as in WWII. The troops’ warfront experiences also differed across the two wars, women played a larger role in WWII, and there were small increases in median education between the two periods. These factors might lead to different responses even without differences in GI benefits. Additionally, there is no guarantee that the true effects of education on marital outcomes were necessarily stable across this period. Although this exercise should therefore be considered cautiously, we believe that evidence of a discontinuity around the WWI cutoff would call into question the likelihood that GI benefits play a substantive role. The absence of such a discontinuity, while only suggestive, is nevertheless reassuring.
We obtain the same qualitative result when we replace the %WWI variable with a dummy variable indicating that the cohort was born after 1896.
Results are virtually identical if we restrict our definition of homeownership to include only heads of households.
Unlike Yamishita and Fetter, we do not find evidence that GI benefit–eligible cohorts were more likely to own a home in 1960 than their ineligible counterparts. The discrepancy appears to emanate from differences in the way the Korean War is incorporated into the different analyses. Yamishita did not control for the effects of the Korean War at all. Fetter’s analysis assumed that the impact of participating in WWII and participating in Korea would be the same for a given cohort. Our specification provides more flexibility on this front.
In contrast, Korean War participation rates were much lower (especially for our cohorts) and resulted in only 36,500 deaths.
For example, we calculated the sex ratio using only men and women who belong to the same birth cohort.
Fig. 2 
Sex ratio (male/female) by birth cohort. Estimates are based on white men and white women born in the contiguous United States. We define the sex ratio as the number of men born in a year-quarter divided by the average number of women born in the previous and subsequent 8 quarters. Source: 1960 Integrated Public Use Microdata Series (IPUMS, 1 % sample)
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Acknowledgments
We would like to thank Rachana Bhatt, Daniel Fetter, and Christine Schwartz for their helpful comments. We would also like to thank seminar participants at the University of California San Diego; University of Essex; University of Kentucky; London School of Economics; Texas A & M University; University of Texas-Austin; and participants in the All UC Labor Economics Workshop, American Education Finance and Policy Annual Meeting, the Bergen-Stavanger Workshop, University of Michigan Conference on the Long-Run Impacts of Early Life Events, and Society of Labor Economics annual meeting. We gratefully acknowledge financial support from the National Science Foundation grant #SES-0350988.
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Appendix
Estimated returns to education. Calculations are based on white men born in the contiguous United States. Estimates are derived from a regression of the log wage on educational attainment, birth year-quarter fixed effects, and the interaction between birth year and educational attainment. Source: 1970 Integrated Public Use Microdata Series (IPUMS, three 1% samples)
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Larsen, M.F., McCarthy, T.J., Moulton, J.G. et al. War and Marriage: Assortative Mating and the World War II GI Bill. Demography 52, 1431–1461 (2015). https://doi.org/10.1007/s13524-015-0426-x
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DOI: https://doi.org/10.1007/s13524-015-0426-x