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Disenfranchisement Through Divorce? Estimating the Effect of Parental Absence on Voter Turnout

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Abstract

Does growing up without both parents decrease voter turnout? I extend and improve upon earlier answers to this question. First, I estimate the long-term effects on voter turnout via analysis of a nationally representative sample of adults. Second, I exploit the quasi-natural experiment of parental death to correct for non-random selection into parental absence. Contrary to previous research, I find no evidence that growing up in an absent-parent household effects white voter turnout. I also present evidence suggesting the negative effects are limited to black voters.

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Notes

  1. On the importance of material resources for socialization in general, see Verba et al. (2005).

  2. Only two of the studies reviewed above have attempted to deal with the selection problem. Sandell and Plutzer (2005) regress divorce on four pre-treatment covariates in an appendix, but the R-squared from this model suggests endogeneity could still be present. Kern (2010) constructs a propensity score using several pre-treatment measures of marital happiness and attitudes toward divorce. Unfortunately, even when such measures are available it is unclear how to correctly model the decision to separate, an issue sociologists have long struggled with (Ní Bhrolcháin 2001; Manski et al. 1992).

  3. Such an approach is common in applied econometrics (Angrist and Pischke 2009; Grimard and Parent 2007), and was used recently by Berinsky and Lenz (2011) to estimate the effect of education on turnout. I use robust standard errors in all specifications in order to account for LPM-induced heteroskedasticity (Wooldridge 2002, pp. 454–457). All specifications in this paper were also estimated using probit regressions, with no substantive differences in any of the results.

  4. I discuss possible alternative designs in the concluding section.

  5. I discuss possible failures of the exogeneity assumption, and present results from an alternative model, below.

  6. The exact question wording is, “Were you living with both your own mother and father around the time you were 16? IF NO: With whom were you living around that time?”

  7. I limit the analysis to these two subsamples because existing theory on political socialization does not offer clear predictions on how effects should vary across racial groups. Unfortunately, the only guidance is given by the observed differences that have appeared in the results of prior studies. Focusing on only black and white respondents facilitates comparison with earlier studies without demanding too much of the data.

  8. The key disadvantage of the GSS is that the independent variable of interest is partially unobserved, since the data only tell us that some change in family structure occurred between (and possibly before) birth and age 16, and nothing about family structure after that point. While not ideal, since this missing information could provide insight into the magnitude of the effect, it is reasonable to assume that any treatment effect heterogeneity of this form is orthogonal to the average effects we are interested in.

    Finally, although one other potentially useful feature of this data is the presence of a measure of parents’ educational background, missingness on these questions is understandably very high among respondents who were not living with both parents at age 16. For example, 25% of respondents who experienced a change in family structure could not recall their mother’s education, compared to 5% of those who lived with both parents. Thus, I will not use these questions in my analysis in order to avoid introducing bias.

  9. Since the GSS is conducted in the spring of the survey year, the most recent presidential election is about 18  months prior to the survey. For example, this means that a respondent surveyed in 2000 is coded as (1) on the dependent variable if they reported voting in the 1996 presidential election.

  10. I also include an age-squared term in the regressions, following standard practice in the behavior literature, dividing the variable by 100 so the coefficient is interpretable.

  11. It could be that family structure has a causal effect on education and income as well. Excluding these measures could lead to omitted variables bias, but including them could lead to post-treatment bias. While the former bias can only inflate estimates of the causal effect of childhood family structure on adult turnout, the direction of the latter bias is generally indeterminate (King and Zeng 2006; Angrist and Pischke 2009, pp. 64–68). Below I present estimates from models excluding these variables, as well as models with these variables as outcomes, as these are the only robustness checks available in such situations.

  12. A comparison of density plots for age (not shown) in both of these groups showed that while the means differ considerably, there is a good deal of common support on this variable.

  13. The first stage requirement is in fact trivially met, since, as in a randomized control trial with one-sided noncompliance, there are no units in our sample who received the instrument but did not also receive the treatment.

  14. To see this, note that the probability limit of the IV estimator can be written as \(Cov(Z_{i},Y_{i})/Cov(Z_{i},D_{i})=\delta+Cov(Z_{i},\epsilon_{i1})/Cov(Z_{i},D_{i}). \) The denominator in the second term is always positive, and the numerator will be negative under any of the violations discussed above.

    A different form of violation is that, as seen in Table 1, respondents who experienced a parental death are on average much older than the rest of the sample, while respondents who experienced parental absence for some other reason are on average younger than the full sample. Given that the densities for age still show considerable overlap, however, adjusting for age in both stages should account for this.

  15. Thanks to an anonymous reviewer for this suggestion.

  16. Estimates from this specification merit some caution, since the GSS changed the way it recorded respondents’ race starting in 2000. Before 2000, GSS interviewers would record respondents’ race based on observation; additionally, the GSS did not distinguish between Hispanics and other respondents until after 2000.

  17. This could indicate two things: there may be measurement error in the GSS coding of race prior to 2000; or, the effect seen in Table 2 could be limited to respondents in survey years 2000 and above.

  18. Out of a total of 121 respondents in this subsample, only 75 reported an absent parent and just 13 reported a parental death.

  19. These specifications include the same set of regressors as in the turnout equations, minus the age-squared term. Partisan attachment is measured using a “folded” partisanship scale, with, for example, independents coded (0) and strong Democrats and Republicans coded (3).

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Acknowledgments

I thank Adam Berinsky, Andrea Campbell, Anthony Fowler, Jens Hainmueller, Maia Hajj, Orit Kedar, Gabriel Lenz, Krista Loose, Michele Margolis, three anonymous reviewers, and the editors for helpful comments and discussion. I am responsible for any remaining errors.

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Correspondence to Michael W. Sances.

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Sances, M.W. Disenfranchisement Through Divorce? Estimating the Effect of Parental Absence on Voter Turnout. Polit Behav 35, 199–213 (2013). https://doi.org/10.1007/s11109-011-9188-3

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