Education and Political Participation: Exploring the Causal Link

Though Dee (2004) and Milligan et al. (2004) come to common conclusions concerning the effect of education on turnout, the independent variables do differ across the studies. Milligan et al. (2004) use an indicator variable measuring completion of high school, while Dee uses college attendance (for the proximity instrument) and the highest grade of schooling completed (for the compulsory education instrument).

Two of these studies were randomized studies and one was quasi-experimental.

This information is drawn from the Selective Services website (http://​www.​sss.​gov/​, accessed August 11, 2008) and Card and Lemieux (2001).

This last cohort was never called to service as the draft ended in February 1973.

Card and Lemieux (2001) explore the possibility that the increased educational attainment of this cohort is attributable to post-service GI Bill benefits. They reject this alternative explanation. First, they find that most of the excess college enrollment was attributable to men who had not yet served in the military. Second, they find that, if anything, the rate of post-service degree attainment was lower for Vietnam-era veterans than for earlier cohorts. Using a similar model, with data from the National Health Interview Survey, MacInnis (2006) finds that the pre-lottery Vietnam draft caused approximately a 3.7% increase in college completion.

Moreover, educational deferments were eliminated just over a year after the lottery was introduced, resulting in relatively few individuals who were eligible for both the lottery and educational deferments. An additional problem is that the draft lottery must be used as an instrument for both education and veteran status. Identification therefore must proceed via assumptions concerning the functional form of these relationships (Angrist and Krueger 1992).

We did not include the 1976 CPS because the survey did not record state of residence. It should be noted that the results presented below hold if each individual study is excluded and the analysis rerun. Also, we exclude respondents who fail to finish high school because they would not be eligible to receive the treatment of a college education.

The CPS sampling frame excludes active members of military. Thus, no respondents in our sample are active members of the military.

The basic results are similar when we use either college degree or the approximate total number of years in college as our measure of educational attainment (see Table 5).

By including this interaction, we also control for the downward trends in male veteran rates, which fall from a high of 59% in the 1935 cohort to a low of 11% in the 1959 cohort, the last one we examine. To render coefficients more interpretable, we rescale Birth Year to vary between zero and one.

We include a variable for married because it strongly influences turnout. However, the results with the “married” variable should be interpreted with caution because this variable may introduce post-treatment bias. We did not include income because it could be an intervening variable (i.e., the draft leads to more education, which leads to higher incomes, which fosters political participation). Previous research has shown that veteran status negatively affects future earnings among Vietnam-era males (Angirst 1990). However, as a robustness check, we included income quintiles as a series of dummy variables in our regressions and the results did not change.

We use an indicator of veteran status. Theoretically, respondents could have served in the armed forces, but not in Vietnam. For our treatment group, however, veteran status indicates service during the Vietnam era, as defined by the CPS codebook.

Fixed effects for CPS study year are included but not shown in all models. Following the convention of applications of this instrumental variable approach in economics (Angrist and Pischke 2009; Grimard and Parent 2007; MacInnis 2006), we use linear probability models in both stages of the regression.

This model therefore assumes that the relative schooling choices of men and women would follow the same path in the absence of sex-specific factors, notably the draft (Card and Lemieux 2001).

For instrumental variables estimates to be consistent, however, the first stage need not be correctly specified (Angrist and Pischke 2009, p. 191). It must only predict exogenous variation in the variable being instrumented.

Including the married indicator variable slightly changes the coefficient, but this result should be interpreted with caution because this variable may introduce post-treatment bias.

The total number of years in college was not available for the full CPS sample. To approximate the number of years in college variable, we use estimates from the 2000 National Annenberg Election Study. Based on these estimates, we code some college in the CPS to 13.8 years, college degree to 16 years, and more than a college degree to 18.3 years. We then re-scale this variable to vary between 0 and 1.

We also checked to see if the results differed according to their proximity to the Vietnam War. One reviewer argued that if some other factor influenced the educational attainment and voting propensity of men born between 1946 and 1948, a violation of the exclusion restriction, the effect of the treatment might vary by time. In particular it might be largest in the elections most proximate to the Vietnam War. To explore this possibility, the reviewer suggested that we exclude the 1972–1980 period and see if the results hold up. We performed this analysis and our results did not change.

Specifically, we combined data from: the Cumulative National Election Study (NES), the General Social Survey (GSS), the 2000 Annenberg Election Study, and the 2004 Annenberg Election Study. These data are less ideal because each study asks about different elections and different numbers of elections. In addition, we have no consistent indicator of veteran status. However, even given these differences we find a surprisingly consistent set of results, also suggesting that education may fail to increase turnout. These results are available from the authors upon request.

These findings also may shed some light on the effect of Vietnam-era service on the propensity to vote. As noted above, research on this war finds a reduced propensity to vote among Vietnam era veterans, a finding we replicate in Table 1. This negative finding could arise, however, not because serving suppresses voting, but because of a selection effect. The kinds of people who served may be predisposed not to vote for other reasons. The IV estimates provide may some support for this alternative, as instrumenting veteran status flips the sign on the veteran coefficient (see Table 4). However, this effect is not statistically significant.

The imprecision of the IV estimate here is similar to that found in Grimard and Parent (2007).

In addition, when we use the same IV estimation replacing turnout with income quartiles as the dependent variable, we find that the instrumented education measure has a positive and significant relationship with the respondents’ income, as expected.

It is, of course, important to note two caveats that generally apply to instrumental variable analysis. Our estimates only describe the effect of education among those induced to attend college because of the draft. This effect may be different from the effect of college among individuals who attend college voluntarily. Researchers refer to this aspect of instrumental variables estimates as a Local Average Treatment Effect (LATE). In our case, it is hard to say a priori whether the treatment group would be more or less predisposed to vote. They might be less likely to vote than other educated people because of mistrust of government. Alternatively, they might be more “activist” and so more likely to vote. The second caveat is that, with instrumental variables analysis, bias from an exclusion restriction violation always remains a possibility.