Exploiting Case Timing

A simple bivariate regression of 2012 voting onto “saw household member arrested/convicted/jailed” suggests that proximal contact has substantial demobilizing effects (results in Online Appendix Section 4). But people who are sentenced to jail (and their families) are likely different from those who are not Indeed, adding in available covariates shrinks the effect estimates dramatically, suggesting that a simple comparison of jailed to unjailed yields biased results (Gerber et al. Reference Gerber, Huber, Meredith, Biggers and Hendry2017).

Rather than simply comparing registered voters who see a household member arrested to those who do not, I exploit the timing of criminal cases to get better estimates of proximal contact’s effect on voting. The intuition here is that people who see a loved one sent to jail in October are not substantially different from people who see their loved one sent to jail in December, except that the October cases fall before the election and can impact people’s decision to vote. If we believe that arrest, charge, and sentencing behavior are fairly consistent across time (particularly around the election), we should be able to compare people who experience a given type of proximal contact before the election to those who experience it afterward to obtain a causal effect of contact on voter turnout. This is similar to approaches used by Weaver and Lerman (Reference Weaver and Lerman2010) and Testa (Reference Testa2016) to estimate the individual effects of contact and by Burch (Reference Burch2013a) to estimate neighborhood effects of incarceration, and shares intuition with the approaches described in Elwert and Pfeffer (Reference Elwert and Pfeffer2016).

As a first check of the assumption that cases from before and after the election are fairly similar and affect similar households, Figure 1 plots binned means for a number of pretreatment covariates for the weeks before and after the November 2012 presidential election. These background characteristics look fairly consistent over time, both for characteristics of the voters (age, gender, prior turnout in the 2008 election) and the matched defendants (gender, race, and charge severity). Similarly, Figure 1 in the Online Appendix explores voting in the four prior elections rather than just 2008. If we saw large trends or discontinuities in these pretreatment variables, we would worry that comparing across time would introduce bias, as we would be comparing voters with different underlying turnout propensities (and the differences on observable covariates might also suggest differences on unobservable characteristics). It does not appear that arrests shortly before the election affected different types of households than those shortly after.

FIGURE 1.

Pretreatment Covariates During the Pre-/Post-Election Periods, Demonstrating Balance and No Large Discontinuities

I begin with cases from one month around the election. Table 2 presents OLS regression results from a model that regresses a voter’s 2012 turnout onto an indicator variable for whether their household member’s case fell before or after the election, and a factor variable indicating how extreme their level of proximal contact was (charge but no conviction, conviction but no jail, or a jail term) as well as the interaction between the two. These results suggest that seeing a household member charged but not convicted of a misdemeanor before the 2012 election had little impact on voter turnout (estimate of +3 percentage points) compared to having that experience after the election. Seeing a household member convicted of a misdemeanor crime (but not jailed) before the election rather than after appears to have a larger demobilizing effect (−6 percentage points), as does seeing a household member sent to jail (−12 percentage points).^{Footnote 5}

TABLE 2.

Proximal Contact on Voting (Using Case Timing)

Note: *p < 0.05.

These results from the 30 days immediately before and after the election suggest that proximal contact can demobilize voters. But do these effects persist, or are they limited to the relatively small number of people who are dealing with the immediate aftermath of cases when election day comes around?

Figure 2 expands the time frame for Table 2’s analysis, looking at windows ranging from two weeks around the election to forty weeks. The top panel presents estimates of the effect of seeing a household member charged with a misdemeanor (but not convicted) before the election, the middle panel estimates of the effect of conviction (but not jail), and the bottom panel estimates of pre-election jail sentencing’s effect on household member voting. These plots suggest that Table 2’s estimates, of large negative effects on voting from proximal contact, are more the exception than the rule. As the window broadens to include cases that fell months rather than weeks before the election, the estimated effects of proximal contact approach zero. It does not appear that the types of proximal contact measured here (misdemeanor charges, conviction, or jail time) have lasting effects on household members’ voter turnout beyond a few weeks. It may appear that conviction (middle panel of Figure 2) still exercises some negative influence on turnout as we look at cases months from the election: the estimates are negative and suggest a 2–4 point drop in turnout, although they cannot be statistically distinguished from zero. But recall that these estimates are based on a dataset that combines voters who experienced conviction very near the election with those who experienced it earlier. If we drop the month (30 days) immediately around the election and generate the same estimates, we reach a different conclusion, as shown in Figure 3. Once we omit voters who could have a very short-term effect from proximal contact (because their household member is charged and convicted in the few weeks immediately before the election), the pattern of null results becomes even clearer. People who see their household member convicted of a misdemeanor two or three or eight months before the election do not seem less likely to vote than people who do not see their family member convicted until afterward.

FIGURE 2.

Estimates of the Effect of Proximal Contact (Charge, Conviction, Jail) on Turnout Using Cases That Fall Before and After the Election, Varying the Time Window Used

FIGURE 3.

Estimated Effects of Household Member Misdemeanor Conviction on 2012 Voting, as in the Center Panel of Figure 2, Dropping Cases From the 30 Days Immediately Around the Election

The introduction to this paper highlighted two broad types of mechanisms by which proximal contact could demobilize: roughly, “resource” mechanisms and “social” ones. These results are consistent with only the resource story. Having a household member convicted or jailed in the weeks before an election can send a household into chaos, as household members scramble to pay legal costs or fines, to find childcare, and to keep the household financially afloat during one member’s absence (Howell Reference Howell2009). Further, that household member’s return from jail or lockup can bring additional turmoil (Comfort Reference Comfort2016). These experiences are serious, but many of them are short term, consistent with the pattern of demobilization seen here.

But many of the social mechanisms by which proximal contact has been hypothesized to reduce turnout occur on a longer time frame. Social stigma or embarrassment at a loved one’s arrest and conviction would be expected to cause families to withdraw from social and civic life for more than just a few weeks. Political socialization experienced by families of people incarcerated, such as that described by Weaver and Lerman (Reference Weaver and Lerman2014), is usually thought to persist for months or years after the initial experience. If such processes were happening in this case, we should continue to see effects for households whose cases fell months or even years away from Election Day. That we do not see such long-lasting effects casts doubt on whether these mechanisms are occurring here. As noted below, the absence of these long-run social effects is not likely due to this paper’s focus on misdemeanor cases; similar patterns appear in felony cases as well (Section SI5). Instead, it seems that processes like social withdrawal, while important in many realms of life, do not shape voting patterns among households with proximal contact. The concluding section considers why this is.

Robustness

Section 5 of the Online Appendix presents additional evidence to address several concerns: match quality (generally or over time), imbalance around the election, and the generalizability of these findings. A placebo test using only 2013 cases rules out certain types of bias due to seasonal patterns. I also estimate the effects of household members’ felony cases (these results, like the main results for misdemeanor cases, do not suggest a lasting demobilization effect).

I also check whether the apparent null effects shown here are masking effect heterogeneity: some household members being demobilized by proximal contact while others are mobilized, with these effects obscuring each other (Maltby Reference Maltby2017). In the Online Appendix, I explore the possibility of effect heterogeneity on several dimensions: race, neighborhood, wealth, family relationships, and past voting. Across many different subsets of the population, I find very little evidence of persistent demobilization (or mobilization). Similarly, Section 2.3 of the Online Appendix discusses what underlying differences between Harris County and the rest of the USA could mean for generalizability. I consider characteristics such as court processes, local demographics, and voter turnout and conclude that it is unlikely that a similar study run elsewhere would find substantially larger or longer-lasting effects.