Abstract
Democratic theory and prior empirical work support the view that political participation, by promoting social integration and pro-social attitudes, reduces one’s propensity for anti-social behavior, such as committing crimes. Previous investigations examine observational data, which are vulnerable to bias if omitted factors affect both propensity to participate and risk of criminality or their reports. A field experiment encouraging 552,525 subjects aged 18–20 to register and vote confirms previous observational findings of the negative association between participation and subsequent criminality. However, comparing randomly formed treatment and control groups reveals that the intervention increased participation but did not reduce subsequent criminality. Our results suggest that while participation is correlated with criminality, it exerts no causal effect on subsequent criminal behavior.
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Notes
For example, Vavreck (2007) finds that more educated and more politically engaged individuals are more likely to overreport turnout.
See http://www.voterparticipation.org/about-us/, retrieved May 2016.
According to researchers who conducted the initial outreach program for the VPC, race was coded by the vendor’s proprietary method that used linguistic characteristics of each name and Census demographics for the address to predict individual race.
86% of cases are single-address records.
Tests reported in the supplemental appendix reveal no imbalances across voter file covariates (race/ethnicity, gender, and state of residence) in the treatment and control groups.
An example of the mailing appears in the supplemental appendix.
For records with only a month and year of birth, day of birth was often recorded by the original research team as the 1st of the month. For this reason, we exclude all cases with birthdays on the first of the month. These exclusions are implemented using pre-treatment measures.
Although the process of matching voter file records to state supervision records is imperfect, the error rate should be the same in both the treatment and control groups.
Records were considered successfully geocoded if the ArcGIS match score was greater than 85 (out of 100) and there was a unique street address for the highest match score.
There are no covariate imbalances between the treatment and control groups for this final sample (see tests in the supplemental appendix).
According to 2015 Census estimates, there are a little over 21.8 million 18–22 year olds in the U.S. The coefficient estimate is −0.48 percentage points. If all voted rather than none, the reduction in the number incarcerated is 104,785 individuals.
This predicted risk score was obtained by estimating a logistic regression using records in the control group (those not sent a treatment letter in the field experiment) to predict the probability each individual in our dataset was under state supervision. That model, estimated separately for gender groups (male, female, or unknown, as reported by the list vendor), includes indicators for whether an individual is Black or Hispanic (an exclusive coding, with all other races making up the excluded category), state fixed effects, and the various ACS survey measures in Table 2. Using the coefficient estimates from that model, we predict the risk measure for the entire sample using each individual’s observed (pre-treatment) characteristics. See the supplemental appendix for additional analysis and the underlying coefficient estimates.
In the supplemental appendix, we show these results are robust to limiting the analysis to states where it is less likely that individuals were incarcerated for a crime they had committed prior to the 2010 election. In Ohio and Washington we observe when incarceration began and do not code as incarcerated individuals whose admission date is before June 1, 2011, while in Texas we observe date of offense and do not code as incarcerated individuals whose offense dates precede the 2010 election. In the supplemental appendix, we also show similar results in states where our records of supervision include more low-level punishments and assess the relationship between registration and the likelihood of coming under state supervision.
We assume the effect of participation occurs via voting, rather than registration, since the prior theoretical literature stresses how deliberative and participatory activities—like voting—are transformative. In the supplemental appendix we present parallel analyses assuming that registration is the relevant participatory act. Note that our, or any other, experiment that perturbs both registration and voting, cannot be used to assess through which causal pathway these effects manifest—one reason that an explicit statement of the exclusion restriction must build on theory.
Our technical framework is equivalent to an experiment with two-way non-compliance. Treatment is voting and some assigned to the treatment group do not vote (are untreated) while some assigned to the control group are treated (do vote). For a discussion of identification and estimation of causal effects in such circumstances, see Gerber and Green (2012), chapter 6.
Our notation assumes that the consequential factor for a subject’s treatment and outcome is her own treatment assignment and voting, and not that of the other subjects. This approach follows the assumptions in prior empirical and theoretical investigations, which articulate mechanisms for a direct effect of participation on an individual’s mindset and habits.
Note that random assignment means that, in expectation, the proportion of each type of subject is the same across the treatment and control groups.
In the supplemental appendix, we present parallel analyses without covariates.
For all experimental analysis, we report standard errors clustered at the household level, the level at which randomization took place.
Parallel estimates using probit, presented in the supplemental appendix, yield similar results.
A potential concern is that one must vote multiple times to reduce the propensity for criminal behavior. Despite this possibility (discussed in the conclusion), our single election test is justified because prior work has operationalized and provided evidence for the relationship in this manner. In addition, because criminal behavior for those who engage in it generally begins around when they obtain the right to vote (i.e., turn 18), a single election must be sufficient time for the relationship to work if participation is to be an effective means to avert an initial turn to criminal behavior.
For example, Wantchekon (2012) reports the effect on turnout of a large-scale deliberation experiment in Benin.
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Acknowledgements
We thank Chris Mann for sharing the VPC experimental data. We thank seminar participants at UCLA and UCSD, Traci Burch, Kevin Arceneaux, Anthony Fowler, Alec Ewald, the three anonymous reviewers, and the editor for their helpful comments and feedback. All errors are our own.
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Data and supporting materials are available at http://huber.research.yale.edu.
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Gerber, A.S., Huber, G.A., Biggers, D.R. et al. Can Political Participation Prevent Crime? Results from a Field Experiment About Citizenship, Participation, and Criminality. Polit Behav 39, 909–934 (2017). https://doi.org/10.1007/s11109-016-9385-1
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DOI: https://doi.org/10.1007/s11109-016-9385-1