In recent years, scholars have gained new insight into the American justice system by studying criminal justice officials, such as judges and prosecutors, as political agents motivated by the desire to remain in office. Focusing especially on the incentives of elected judges and prosecutors, scholars have shown that these officials may manipulate criminal charges and sentences in order to signal their ideological congruence or competence to voters (Gordon and Huber, Reference Gordon and Huber2002, Reference Gordon and Huber2007; Stuntz, Reference Stuntz2004; Dyke, Reference Dyke2007; Bandyopadhyay and McCannon, Reference Bandyopadhyay and McCannon2014; Gordon and Yntiso, Reference Gordon and Yntiso2022). These results are consistent with a vast formal and empirical literature on political accountability, in which political agents—whether bureaucrats accountable to elected officials (e.g.,Gailmard and Patty, Reference Gailmard and Patty2007, Reference Gailmard and Patty2012), or elected officials accountable to the public (e.g.,Canes-Wrone et al., Reference Canes-Wrone, Herron and Shotts2001; Alt et al., Reference Alt, Bueno de Mesquita and Rose2011)—make policy choices with an eye toward the principals who keep them in office.Footnote 1
In this paper, we contend that elected criminal justice officials are similar to other political actors not merely in having a principal–agent relationship with an electorate, but also in having powers, vis-à-vis their principals, which ordinary agents lack. A legislator, rather than choosing a set of policies her constituents approve, may try via gerrymandering or voting restrictions to choose a set of constituents who approve her policies (Bateman, Reference Bateman2018; Eubank and Fresh, Reference Eubank and Fresh2022; Helmke et al., Reference Helmke, Kroeger and Paine2022). We argue that in a similar fashion, in the many US states that restrict felon voting, elected criminal justice officials may try to shape the composition of the electorate to favor themselves and their copartisans through the selective imposition of disenfranchising felony sentences. The temptation to do this may be especially great for elected prosecutors, whose immense discretion gives them an outsize role in the administration of justice (Gordon and Huber, Reference Gordon and Huber2009; Stuntz, Reference Stuntz2011; Tonry, Reference Tonry2012).
To illustrate this argument, we construct a simple formal model featuring a prosecutor who may offer a felony defendant a plea deal, and a defendant who may accept the deal or reject it and go to trial. Trial is costly to both players, and the prosecutor wants to secure a conviction and as high a sentence as possible, while the defendant wants to minimize her expected loss. We show that when the prosecutor also stands to benefit from the outcome of an upcoming election, and there is a felon disenfranchisement law on the books, the prosecutor’s optimal plea offer depends on (1) whether he wants the defendant to vote, and (2) whether disenfranchisement is indefinite, or only for the duration of the felony sentence. If the prosecutor does not want the defendant to vote, we show that when disenfranchisement is indefinite, his offer is more lenient (to increase the probability that the defendant accepts), and when it is sentence-dependent, his offer is harsher (to increase the time the defendant spends disenfranchised). If the prosecutor does want the defendant to vote, the converse is true. In a “hybrid” regime where either disenfranchisement outcome may occur, any increase in the probability that disenfranchisement is sentence-dependent increases the harshness of the optimal plea when the prosecutor does not want the defendant to vote, and decreases it when he does.
We investigate the empirical validity of our argument by leveraging an unanticipated shock to the relationship between felony criminal sentencing and felon disenfranchisement in the state of Virginia: Governor Terry McAuliffe’s unexpected 2016 announcement of the automatic re-enfranchisement of all felons upon completion of their “sentences of [felony] incarceration” and “supervised release” (Order for the Restoration of Rights, 2016). This announcement heralded a substantial change from the previous regime, in which the length of disenfranchisement and the procedures for rights restoration varied across different types of felony convictions, approximating the “hybrid” regime in our model. It had at least three immediate consequences. First, it made the length of a felony prison or probation sentence the key determinant of (dis)enfranchisement going forward. Second, according to the Governor, it caused the immediate enfranchisement of 200,000 individuals (Horwitz and Portnoy, Reference Horwitz and Portnoy2016). Third, it motivated voter registration drives across the state, targeting the newly enfranchised felon population (Vogelsong, Reference Vogelsong2016). We hypothesize that, as a result, the announcement may have motivated Virginia’s elected felony prosecutors to attempt to mitigate changes to the partisan composition of the electorate by increasing charge and sentence severity for felony defendants they perceived as politically opposed, while decreasing them for defendants they perceived as politically aligned.
To test this hypothesis, we collected all criminal charges filed or sentenced in Virginia Circuit Courts between 2010 and 2020. Our raw data featured 896,824 felony and 333,354 misdemeanor charges, each with detailed accompanying information on the name, race, sex, and charging district of the defendant, and on the charge’s progress through the justice system from indictment to disposition and sentence. From these data, we constructed a case-level dataset by aggregating all charges filed or sentenced on the same day for the same defendant, and ordering multiple charges within a single case by the severity of their maximum sentences. This process yielded 386,992 felony cases filed or disposed of between 2010 and 2020, of which 56,023 were filed or disposed of in 2016.
We analyzed the effect of McAuliffe’s announcement on charging and sentencing behavior in our data using a nonparametric regression-discontinuity-in-time (RDiT) approach, then checked for robustness using both a local randomization approach and a simple series of pooled differences-in-means. Our main results disaggregate defendants by likely political alignment with their prosecutors, then compare the charging and sentencing outcomes experienced by each group immediately before the rule change to those immediately after it. Following Helmke et al. (Reference Helmke, Kroeger and Paine2022) and Eubank and Fresh (Reference Eubank and Fresh2022), we construct a likely-alignment indicator by assuming that racially polarized voting patterns render a defendant’s race informative—though not necessarily determinative—of her political affiliation.Footnote 2 Because defendant race is noted on every criminal case file, this information is immediately and costlessly available to prosecutors.
Our results are as follows. First, we find that immediately after the announcement, defendants who were likely-unaligned with their prosecutor experienced increases in felony charge severity and actual sentence length, while likely-aligned defendants experienced decreases. These findings persist across a range of different RDiT specifications and bandwidth choices, are broadly robust to pooled difference-in-means regression analyses and local randomization inference, and do not appear to depend on prosecutor office size. Providing further support for our theory, we show that the announcement had no effect on charging or sentencing for the subset of (non-disenfranchising) misdemeanor cases handled in Circuit Court over the same period.
Second, these effects appear to have occurred via a range of pathways. Shifts in sentence severity persist when we limit our analysis to cases charged prior to the announcement, suggesting that the announcement may have directly affected prosecutors’ sentencing decisions. But the announcement also appears to have affected prosecutors’ willingness to bargain—for example, by reducing or dismissing charges—as well as their initial charging decisions. Thus, to estimate the announcement’s total effect on sentence severity, we estimate the pre-announcement relationship between charge severity and sentence severity, use it to predict the indirect effect of post-announcement changes to charge severity on sentencing, and combine this result with the announcement’s direct effect on sentencing. We show that the total effect may have been an average sentence increase of four to seven months for unaligned defendants, and an average decrease of one to three months for aligned defendants.
Third, we find little evidence in favor of alternative explanations, such as electoral responsiveness or prosecutors’ personal attitudes toward felon disenfranchisement. Prosecutors never increase or decrease sentence severity against all defendants post-announcement, as would be consistent with simple electoral responsiveness arguments. Moreover, prosecutors of both parties exhibit increased punitiveness toward the unaligned and increased leniency toward the aligned. We also find no evidence that prosecutors’ personal attitudes toward felon disenfranchisement shaped their behavior: the effect is similar among prosecutors who opposed the Governor’s executive order and those who did not.
We next investigate possible prosecutor motives for strategic disenfranchisement. As with legislators, prosecutors arguably may attempt to manipulate voter status to improve their own chances of reelection, to improve the chances of their favored party, or both. Both motives are plausible: with regard to personal incentives, so long as prosecutors can readily infer defendants’ likely partisanship and are uncertain about their future margins of victory, manipulation may be worthwhile even when the total number of defendants affected is low. But the low cost of inferring defendant alignment may also tempt prosecutors to manipulate felon status for partisan reasons, to tip the scale in other, closer electoral contests. Moreover, McAuliffe’s announcement seems likely to have triggered partisan feeling: his changes to Virginia’s disenfranchisement law were described by Republicans as an attempt to guarantee Virginia for Democrats in the 2016 presidential election (Horwitz and Portnoy, Reference Horwitz and Portnoy2016).Footnote 3 Thus, it is possible that prosecutors were especially motivated to manipulate felon status due to the perceived salience of felon voting restrictions for the 2016 presidential election.
We conduct three series of tests to disentangle the personal from the partisan motivation, and find some evidence in favor of the partisan channel. We begin with the conjecture that prosecutors who wish to shape the outcome of an election may conclude cases pre-election for unaligned defendants, but post-election for aligned defendants. If we observe this behavior around prosecutors’ own elections, this suggests a personal motive; if prosecutors engage in this behavior more generally, it suggests partisan concerns. Accordingly, we examine patterns in criminal case outcomes in the weeks around state (odd-year) and federal (even-year) elections in Virginia from 2012 to 2019. We find little evidence of an effect in state election years, but do find some evidence of an effect in federal election years. This is consistent with broader partisan motives.
If partisan feeling motivates prosecutors to manipulate felon status, the announcement’s effect on charging and sentencing should be stronger among more enthusiastic partisans. We use prosecutors’ donor histories in the Database on Ideology, Money in Politics, and Elections (DIME) (Bonica, Reference Bonica2016) to examine how three measures of partisan political engagement—ideology, donation recency, and donation size—affected prosecutors’ responses to the announcement. We find that donors, especially more recent donors, are more responsive to the announcement than non-donors.
Finally, if prosecutors are motivated by their desire to stay in office, more politically vulnerable prosecutors might be expected to have responded more strongly to the announcement. Because vulnerability is endogenous to political aptitude, this possibility is difficult to test. Nevertheless, as a first cut, we code prosecutors as politically “threatened” if their last election featured a challenger who received at least 10% of the vote. We find that political threat, as measured, has no effect on charging and sentencing behavior post-announcement.
Our paper is relevant to the growing literature on justice officials as strategic political actors. Existing work has focused on the incentives for prosecutors and judges to manipulate (and often, maximize) charges, conviction rates, or sentences as a way of signaling their attributes to voters or political principals, with a view to being reelected or promoted (e.g., Gordon and Huber, Reference Gordon and Huber2002, Reference Gordon and Huber2007, Reference Gordon and Huber2009; Dyke, Reference Dyke2007; Bandyopadhyay and McCannon, Reference Bandyopadhyay and McCannon2014; Mungan, Reference Mungan2017). Our contribution is to show that elected justice officials may also manipulate charges, convictions, and sentences in order to shape the electoral environment directly.
Our paper is also relevant to scholarship on attempts by political actors to manipulate the composition of the electorate (Behrens et al., Reference Behrens, Uggen and Manza2003; Bateman, Reference Bateman2018; Eubank and Fresh, Reference Eubank and Fresh2022; Helmke et al., Reference Helmke, Kroeger and Paine2022). The literature in this area has focused primarily on the incentives of elected officials to shape the electorate in their favor. Thus, scholars have raised the possibility that felon disenfranchisement laws may have been strategically imposed by state officials (e.g., Eubank and Fresh, Reference Eubank and Fresh2022; Helmke et al., Reference Helmke, Kroeger and Paine2022). We contribute to this literature by arguing that such laws might also be strategically implemented, and demonstrating that the state-level imposition of such laws may motivate local-level officials to manipulate their application.
1. Elected prosecutors and felon voting laws
Consider an interaction between a felony defendant and a prosecutor. The prosecutor can offer a plea deal which the defendant can accept or reject. Consistent with prior work among political economists and legal scholars (Landes, Reference Landes1971; Grossman and Katz, Reference Grossman and Katz1983; Baker and Mezzetti, Reference Baker and Mezzetti2001; Gordon and Huber, Reference Gordon and Huber2009; Stuntz, Reference Stuntz2011), suppose the prosecutor has discretion to select the precise plea offer that maximizes his utility. If the defendant rejects the plea, the players go to trial, where with some probability the defendant is convicted and sentenced to prison, and with complementary probability she is acquitted. Trial comes at a privately known cost to the defendant, and her utility is decreasing in the length of her sentence. Trial is also costly to the prosecutor, but his utility is increasing in the length of the defendant’s sentence.
In this context, the prosecutor trades off a higher sentence in his plea offer against a higher likelihood of going to trial. In equilibrium, he offers the plea that optimally accounts for his own known cost of trial, the defendant’s unknown cost of trial, and the defendant’s expected sentence at trial. (In the Online Appendix, this argument is presented formally and the game is solved in full.)
Now suppose there is a felon disenfranchisement rule on the books, and the prosecutor is concerned about the outcome of an election. Under the rule, disenfranchisement may take one of two forms: it may be indefinite, or only for the length of a sentence. We show in the Online Appendix that if the prosecutor suspects the defendant will vote for the opposite party and the rule is indefinitely disenfranchising, then the prosecutor adjusts his plea offer downward to induce the defendant to accept and lose the right to vote. By contrast, if the rule disenfranchises the defendant only during her sentence, the prosecutor adjusts his plea offer upward to inflict a longer sentence. While in both cases the size of the adjustment depends on how much the prosecutor cares about preventing the defendant from voting, some shift is always optimal.
If the prosecutor instead suspects the defendant is a copartisan, then under indefinite disenfranchisement he adjusts the plea offer upward (to discourage the defendant from taking it) and in a sentence-dependent regime he adjusts it downward (to minimize her disenfranchised time). Finally, if the rule is a hybrid—with some probability a convicted felon is indefinitely disenfranchised, and with reciprocal probability she is disenfranchised only during her sentence—we show that an increase in the probability that disenfranchisement is sentence-dependent increases optimal plea offer severity if the defendant is politically unaligned, and decreases it if she is aligned.
So far, we have assumed that the defendant does not consider disenfranchisement in making her plea decision. This is empirically plausible for several reasons: defendants may not know about felony disenfranchisement rules, or may heavily discount the future loss of voting rights relative to their present concerns. Nevertheless, we extend the model to consider the case where the defendant dislikes disenfranchisement. We show that this case exacerbates some of the above effects while mitigating others, but that the prosecutor’s incentives to manipulate plea offers as described above are never fully counteracted unless the defendant’s disutility from disenfranchisement is very high relative to its benefit (cost) to the prosecutor.
Applying these theoretical findings to Virginia, we can make two conjectures. First, the Governor’s executive order effectively transformed felon disenfranchisement in Virginia from a hybrid regime in which multiple factors determined disenfranchisement status, to a fully sentence-dependent regime. Consequently, post-order, prosecutors should have assigned greater importance to manipulating felony sentence length to shape defendants’ probabilities of voting. Second, the executive order directly altered the composition of the electorate by immediately enfranchising a large number of formerly disenfranchised felons. If we expect that, pre-announcement, prosecutors were using a wider set of tools to disenfranchise unappealing defendants, this alteration should have resulted in a sudden increase in the share of unaligned voters in each district, which should have negatively shocked prosecutors’ own electoral viability and that of their copartisans. These shocks should have heightened the importance prosecutors assigned to manipulating defendants’ enfranchisement status. These two conjectures suggest the following hypothesis:
Hypothesis: The unexpected April 22, 2016, changes to felon disenfranchisement policy in Virginia caused the state’s elected prosecutors to increase the length of the felony sentences imposed on politically unaligned defendants, and decrease the length of the felony sentences imposed on politically aligned defendants.
Note that this hypothesis is independent of prosecutors’ precise reasons for shaping the electorate. These reasons might be personal and office-seeking, partisan and policy-seeking, or a mix. In a later section, we provide suggestive evidence that prosecutors’ attempts to manipulate the electorate are motivated at least in part by a desire to help copartisans.
2. Context: criminal justice in Virginia
On April 22, 2016, Virginia Governor Terry McAuliffe held a press conference in which he announced an executive order implementing sweeping changes to the state’s felon disenfranchisement rules. Before the order, the criteria for re-enfranchisement had depended on the offense, with some offenders eligible to be considered for rights restoration upon completion of their sentence provided they were not currently facing felony charges, and others required to complete a three year waiting period and submit a written application.Footnote 4 After the order, all felons who had completed their felony sentences of incarceration or supervised release could expect to have their right to vote immediately and automatically restored. According to the Governor, an immediate result of this change was the automatic enfranchisement of 200,000 felons who had already completed their sentences—a 3.3% expansion in the statewide voter pool.Footnote 5
For our purposes, the Governor’s announcement provides an excellent opportunity to test whether elected prosecutors attempt to shape the electorate by selectively imposing disenfranchising sentences. This is for three reasons. First, the policy change was unexpected, surprising all but a small group of close political advisors and allies. State legislators, bureaucratic officials, voter registrars, and prosecutors had been deliberately kept in the dark to prevent them from attempting to head off the changes before their announcement (Zullow and Moomaw, Reference Zullow and Moomaw2016).
Second, it sharply and clearly limited how a felony conviction could result in disenfranchisement. Post-announcement, all felons were to be automatically enfranchised after the length of their prison or probation sentence, and any individual convicted of a felony but not sentenced to prison or probation time kept her right to vote. This allows for a clear hypothesis: post-announcement, prosecutors concerned with shaping the local electorate should have shifted focus to manipulating the severity of the sentences imposed on criminal defendants.
Third, a unique feature of Virginia’s criminal justice system makes it an especially useful context in which to study the strategic incentives of elected prosecutors. While in many states, both prosecutors and judges are publicly elected, in Virginia, felony prosecutorsFootnote 6 (“Commonwealth’s Attorneys”) are chosen in district-level competitive elections every four years—but the Circuit Court judges who handle felony cases are appointed by the legislature to eight-year terms.Footnote 7 These judicial appointments occur in an almost consociational fashion, beginning with a judge’s nomination to the Courts Committee by the local Bar Association, proceeding to unanimous election by all state senators representing a given judicial circuit, and usually ending with unanimous confirmation by the Virginia Senate (A Legislator’s Guide to the Judicial Selection Process, n.d.). This suggests that Commonwealth’s Attorneys are likely, and Circuit Court judges unlikely, to respond to electoral or partisan considerations.
3. Data
Our raw data consists of all Circuit Court charges filed between 2010 and the first months of 2020 in 118 of Virginia’s 120 Circuit Courts.Footnote 8 The Office of the Executive Secretary at the Supreme Court of Virginia provided access to Circuit Court cases, which we complemented with additional sentencing data from Virginiacourtdata.org.Footnote 9 These data include, for each charge: the date of indictment; the geographic district in which the charge was brought; the defendant’s full name, race, gender, and date and month of birth; the eventual disposition of the charge; and any sentence imposed. Most charges also include information on charge reductions and hearings.
We aggregated criminal charges up to the case level by treating all charges filed or resolved on the same day, for the same individual, as belonging to the same case.Footnote 10 This yielded a dataset of 134,695 misdemeanor and 386,992 felony cases charged or sentenced between 2010 and 2020, of which 56,023 felony and 12,264 misdemeanor cases were, respectively, charged or sentenced in 2016.
Because misdemeanors do not result in disenfranchisement, we omit these cases from our main analysis, leveraging them instead to conduct a set of placebo tests.Footnote 11 We also exclude a small setFootnote 12 of cases coded in our data as probation violations leading to reinstatement of an underlying felony, for two reasons. First, active probationers were disenfranchised both before and after the announcement. Second, we were unable to consistently link these cases to the original case and sentence, meaning that we cannot determine the extent to which punishment is a function of the severity of the original conviction.Footnote 13
Finally, we merged our criminal case records with district-level vote shares in the 2012 and 2016 presidential elections and data on incumbent Commonwealth’s Attorneys’ party membership, election years, and election outcomes (including vote shares),Footnote 14 as well as the partisan identities of their challengers (fromHessick and Morse, Reference Hessick and Morse2019). We supplemented this information with data on Commonwealth’s Attorney office size from a 2018 Virginia Compensation Board survey.Footnote 15
3.1. Measurement
To test our theory, we constructed measures of prosecutor–defendant alignment and case-level charge and sentence severity. We operationalize these concepts as follows.
3.1.1. Defendant political alignment and race
As discussed above, race is indicated on every defendant’s case file, and is a common heuristic for partisan affiliation. This heuristic appears empirically plausible in Virginia, where 76% of African-Americans statewide (but only 27% of whites) described themselves as Democrats or leaning-Democrat in 2014 (Pew Research Center, 2014). This heuristic has also been shown to be accurate among felon populations: in North Carolina and Florida, for example, more than 80% of registered African-American felons, but only 33% of registered white felons, were Democrats (Burch, Reference Burch2012, 10). We therefore assume that Virginia prosecutors view African-American felony defendants as more likely to vote for Democrats, and white felony defendants as more likely to vote for Republicans. Admittedly, this assumption does not account for cross-district variation in the relationship between race and political preferences, e.g., in white support for Democrats. Nevertheless, we believe it is appropriate for two reasons.
First, there is methodological value in using a simple alignment rule applied equally to all prosecutors as our main specification. While it is possible that prosecutors make more nuanced inferences about defendants’ political preferences, these nuances are hard to account for in a principled manner, given data limitations. Second, to the extent that white support for Democrats varies across districts, we argue that even in districts where a randomly selected white person would be likelier than not to lean Democratic, this is not the case for a randomly selected white felony defendant, because white support for Democrats is tied to other demographic indicators which are sparse in the felony defendant population. Specifically, support for Democrats tends to be higher among white women, and to increase with education,Footnote 16 while white felony defendants are heavily male and tend to have low levels of formal education.Footnote 17 Moreover, there is evidence that Democratic Party operatives themselves view white felons as likely-Republican: during a close Governor’s race, Washington State’s Democratic Party chairman argued that illegal felon voting had tilted the race toward the Republican candidate, because the felon population was “nonunion, blue-collar, male [and] Caucasian ... the prime demographic Republicans target” (Postman, Reference Postman2005).
3.1.2. Prosecutor political party and alignment
Given this assumption on defendant alignment, when prosecutors campaign as Republicans or Democrats, we treat prosecutor–defendant pairs as politically aligned when their parties match: for example, a white defendant and Republican prosecutor would be politically aligned. However, approximately half of Virginia Commonwealth’s Attorneys run for election as Independents. Because Virginia does not have an Independent political party, and Independents are barred under state law from receiving endorsements or funding from the Republican and Democratic parties,Footnote 18 we cannot determine an Independent prosecutor’s voter base from party endorsements or donations. Moreover, Virginia voters who identify as Independent are evenly split between those who lean Democrat and those who lean Republican (Pew Research Center, 2014), suggesting that the label has no inherent partisan association.
Here, we begin with the premise that voters view a politician’s party membership as informative of her ideology and policy goals. If this is true, then because Independents are barred from entering into alliances with Virginia’s two recognized political parties, in a district with a partisan lean, an incumbent Independent should expect her partisan challengers to hail from the political party with greater voter support in the district. Figure 1, which presents challenges to incumbent prosecutors 2015–2017 by party affiliation (and for Independents, by district partisan lean), shows support for this premise. Independent incumbent prosecutors in blue-leaning districts were only challenged by Democrats and other Independents, while those in red-leaning districts were only challenged by Republicans and other Independents.
Challenger party by theorized alignment status.
If voters view party membership as informative, an Independent incumbent facing a partisan challenger should not expect the votes of citizens who are dedicated supporters of the challenger’s party. By the same logic, she should expect the votes of citizens who are dedicated members of the district’s minority party: they should prefer her to her opponent. This suggests that while in terms of policy, an Independent incumbent might position herself in the ideological center to build a majority coalition, in terms of electoral strategy, she should treat likely minority-party supporters as “aligned,” and likely majority-party supporters as “unaligned.”
Table 1 presents our overall operationalization of political alignment among prosecutor–defendant pairs.
Prosecutor–voter alignment
Table 1 Long description
Rows list prosecutor party as Republican, Democrat, Independent in a Republican county, and Independent in a Democratic county, with columns for white felon and black felon. Each cell reports either aligned or unaligned. Republican shows aligned for white felon and unaligned for black felon. Democrat shows unaligned for white felon and aligned for black felon. Independent, Republican county shows unaligned for white felon and aligned for black felon. Independent, Democratic county shows aligned for white felon and unaligned for black felon.
3.1.3. Charge and sentence severity
Because prosecutors may influence the length of a felony sentence directly, via the sentence they recommend, or indirectly, via the charges they file, we constructed measures of both charge and sentence severity. To measure charge severity, we used Virginia’s sentencing guidelines to determine the maximum permissible sentence for each charge in a case, then coded the case’s charge severity as the maximum sentence attached to the most severe (“top”) charge filed. This is a conservative measure of charge severity, because it does not account for the severity of all charges in a given case. Nearly all maximum felony sentences in our data take one of five values—5, 10, 20, or 40 years in prison, or life imprisonment—while a small number impose other values, such as 3, 30, or 50 years. Because a life sentence is indeterminate, we recode these sentences as 50-year sentences.
To measure sentence severity, we calculated the total felony prison sentence assigned after conviction in each case. Where multiple charges were sentenced in one case, and the sentences were set to run consecutively, we summed them. Where sentences were set to run concurrently, we used the longest sentence imposed. This measure is a conservative estimate of sentence severity, since it does not include supervised probation time. We exclude probation time for two reasons. First, many probation sentences in the data are “indefinite.” These sentences feature neither a maximum nor a minimum: they end when the court actors involved in the case decide they should. Second, even definite terms of probation can be indefinite in practice because infractions during the probation period can sometimes be used to reset the probation clock.Footnote 20
3.2. Empirical strategy
Treating Governor McAuliffe’s announcement as an unexpected shock to felon disenfranchisement rules in Virginia, we use several methods to test our daily, district-level case data for discontinuous, alignment-specific shifts in prosecutorial punitiveness in the weeks following the shock. First, we use a local-linear regression discontinuity in time (RDiT) approach to test for the effect of the Governor’s announcement on charge and sentencing outcomes, under the assumption that absent the announcement, potential outcomes would have been a smooth function of time. Our data are well-suited to this approach, which permits seasonality in criminal outcomes so long as these outcomes change smoothly in time.Footnote 21 However, to address any inferential shortcomings in the RDiT analysis, we also present results from a simple difference-in-means fixed-effects regression analysis, which relies on the assumption that the announcement was as-if random, and (in the Online Appendix) from a local randomization analysis, suggested by Cattaneo et al. (Reference Cattaneo, Idrobo and Titiunik2024) as a robustness check for data with discrete running variables.
The following local-linear regression model is our main RDiT specification throughout:
\begin{equation}
y_{ijt} = \beta_0 + \beta_1 \mathbb{1}(t \gt t_{ann.})+ f(t-t_{ann.}) + \alpha_j + X_{it} + \epsilon_{ijt}.
\end{equation} Here, 
$y_{ijt}$ is a measure of punishment severity, for example, the total prison sentence for case 
$i$ in district 
$j$ at time 
$t$; 
$t_{ann.}$ is the date of the announcement; 
$f(\cdot)$ is a smooth function of distance from the same; and the parameter of interest, 
$\beta_1$, captures the discontinuous shift in punishment severity following the announcement. In most specifications, we include district fixed-effects (
$\alpha_j$) to account for cross-district differences in sentencing norms, crime, constituency preferences, and prosecutor (each district elects one chief felony prosecutor). In some specifications, we also include pretreatment dummies 
$X_{it}$, which capture a defendant’s gender and whether the type of crime prosecuted was a violent crime, a drug crime, a property crime, a traffic crime, or some other infraction. Our theoretical prediction is that the sign of the parameter of interest, 
$\beta_1$, should be negative for defendants aligned with their prosecutors, and positive for unaligned defendants. To test this prediction, we estimate Equation (1) separately according to the felon’s political alignment vis-à-vis the prosecutor.Footnote 22 Throughout, we usemean square error (MSE) optimal bandwidths with the bias-correction method proposed by Calonico et al. (Reference Calonico, Cattaneo and Titiunik2014), and standard errors clustered at the district level.Footnote 23
After reporting our main regression results, we turn to an investigation of the announcement’s total effect on sentencing: i.e., its effect on both direct changes to sentence severity and indirect changes to sentence severity through changes in charge severity. We test for a direct sentencing effect by estimating the announcement’s effect on sentence severity only for cases charged prior to the announcement. We also examine how prosecutor use of specific sentencing tools shifted post-announcement.
Testing for an indirect sentencing effect via changes in charge severity is harder, because cases charged after the announcement are necessarily sentenced after it as well, making it difficult to distinguish the effect of shifts in charge severity from direct sentence manipulation. Our solution is to estimate the pre-announcement relationship between charge severity and eventual sentence length, then use this relationship to derive bounds on the size of the announcement’s effect on sentence severity via charge severity.
Throughout, we conduct a number of robustness and placebo tests to bolster confidence in our results. In the Online Appendix, we conduct additional tests to disentangle our explanation from one based on districts’ or prosecutors’ ideological preferences.
4. Main results
We begin with a graphical assessment of the announcement’s effect on felony charge and sentence severity. The results are presented in Figure 2. The left-hand column depicts binned averages of the severity of the top charges brought against defendants in Circuit Court in a twelve week window around the announcement, adjusted for prosecutor fixed effects. The right-hand column depicts binned averages of the lengths of the actual felony prison sentences imposed on defendants in Circuit Court during the same time period, adjusted for prosecutor fixed effects. We separately fit linear predictions and kernel-weighted polynomial curves to the data on either side of the announcement. The top row presents the announcement’s effect on all charges and sentences. The middle and bottom rows present the announcement’s effect on charges and sentences for aligned and unaligned defendants, respectively. Consistent with our theory, we observe post-announcement shifts by alignment status: increases in average charge and sentence severity for unaligned defendants, and decreases for aligned defendants.
Announcement effect on charge (left column) and sentence severity (right column).
Figure 2 Long description
Six scatter plots, each with diamond markers, a vertical dashed reference line at Apr 22 and two fitted curves shown as one solid line and one dashed line. All Defendants, Charge Severity (in years). Horizontal axis label: Date. Horizontal axis tick labels: Mar 3, Mar 28, Apr 22, May 17, Jun 11. Vertical axis tick labels: 5, 10, 15, 20, 25. The diamond markers span roughly from about 10 to above 20. The solid fitted line slopes slightly downward before Apr 22, then rises after Apr 22 and later turns downward near Jun 11. The dashed fitted line is close to the solid line before Apr 22, then rises to a higher level after Apr 22 and later turns downward near Jun 11. All Defendants, Prison Sentence (in years). Horizontal axis label: Date. Horizontal axis tick labels: Mar 3, Mar 28, Apr 22, May 17, Jun 11. Vertical axis tick labels: 0, 0.5, 1, 1.5, 2. The diamond markers span from 0 up to near 2, with many points between about 0.5 and 1.2. The solid fitted line is near 0.9 before Apr 22, dips slightly approaching Apr 22, then rises after Apr 22 and levels near about 0.9 to 1.0 toward Jun 11. The dashed fitted line shows a dip just before Apr 22 and a sharp rise just after Apr 22, then returns toward about 0.9 to 1.0. Aligned Defendants, Charge Severity (in years). Horizontal axis label: Date. Horizontal axis tick labels: Mar 3, Mar 28, Apr 22, May 17, Jun 11. Vertical axis tick labels: 5, 10, 15, 20, 25. The diamond markers span roughly from about 12 to above 20. The solid fitted line rises gradually before Apr 22, drops at Apr 22, then stays near about 15 to 16 and declines near Jun 11. The dashed fitted line follows a similar pattern, with a drop at Apr 22 and a later decline near Jun 11. Aligned Defendants, Prison Sentence (in years). Horizontal axis label: Date. Horizontal axis tick labels: Mar 3, Mar 28, Apr 22, May 17, Jun 11. Vertical axis tick labels: 0, 0.5, 1, 1.5, 2. The diamond markers span from below 0.5 up to near 2. The solid fitted line declines from above 1 near Mar 3 toward about 0.9 before Apr 22, drops at Apr 22 to around 0.7, then rises steadily to above 1 by Jun 11. The dashed fitted line is near about 0.9 before Apr 22, dips at Apr 22, then rises and shows a small dip around May 17 before rising again. Unaligned Defendants, Charge Severity (in years). Horizontal axis label: Date. Horizontal axis tick labels: Mar 3, Mar 28, Apr 22, May 17, Jun 11. Vertical axis tick labels: 5, 10, 15, 20, 25. The diamond markers span roughly from about 13 to above 20. The solid fitted line slopes downward before Apr 22 from around 18 toward about 16, then continues downward slightly after Apr 22 toward about 15 to 16 by Jun 11. The dashed fitted line rises sharply just after Apr 22 to near 20, then falls and later rises again around May 17 before falling toward Jun 11. Unaligned Defendants, Prison Sentence (in years). Horizontal axis label: Date. Horizontal axis tick labels: Mar 3, Mar 28, Apr 22, May 17, Jun 11. Vertical axis tick labels: 0, 0.5, 1, 1.5, 2. The diamond markers span from about 0.3 up to above 1.5. The solid fitted line is near about 0.8 to 0.9 before Apr 22, drops at Apr 22 to around 0.7, then declines steadily toward about 0.6 by Jun 11. The dashed fitted line rises sharply just after Apr 22 to above 1, then declines toward about 0.8 by Jun 11.
4.1. Local-linear estimates
Table 2 presents local-linear estimates of the immediate effect of McAuliffe’s order on the average severity of the top charges filed (Panel A) and prison sentences imposed (Panel B) in Circuit Court, disaggregated by alignment status. For each defendant type, the first column presents unadjusted results for comparison. The second column adds district fixed effects to take into account variation across districts in crime rate, crime type, demographics, and prosecutor identity. The third column presents results further adjusted for defendant gender and crime type.Footnote 24
Effect of McAuliffe’s order, by alignment status
Table 2 Long description
Outcomes are reported in two panels, charge severity and sentence severity, each split into unaligned defendants and aligned defendants with three columns per group. Panel A, charge severity: RD Estimate for unaligned defendants is 2.945, 3.049, and 2.464, with standard errors 1.534, 1.205, and 1.184; for aligned defendants it is minus 2.108, minus 2.174, and minus 1.787, with standard errors 1.77, 1.065, and 1.076. Panel A Left Intercept is 16.771, 16.78, and 16.694 for unaligned defendants and 18.581, 18.754, and 18.805 for aligned defendants, with standard errors 0.983, 0.716, 0.741 and 1.349, 0.874, 0.846. Panel A bandwidth is 67.053, 61.664, and 51.763 for unaligned defendants and 70.306, 71.345, and 57.194 for aligned defendants; effective observations are 6161, 5647, 4699 and 8016, 8085, 6593. Panel B, sentence severity: RD Estimate for unaligned defendants is 0.378, 0.469, and 0.402, with standard errors 0.358, 0.271, and 0.273; for aligned defendants it is minus 0.17, minus 0.169, and minus 0.132, with standard errors 0.161, 0.19, and 0.184. Panel B Left Intercept is 0.748, 0.759, and 0.759 for unaligned defendants and 0.876, 0.864, and 0.87 for aligned defendants, with standard errors 0.097, 0.084, 0.087 and 0.12, 0.152, 0.137. Panel B bandwidth is 52.6, 55.082, and 54.025 for unaligned defendants and 70.994, 71.84, and 73.568 for aligned defendants; effective observations are 4525, 4815, 4728 and 7802, 7880, 8057. District FE is No, Yes, Yes for both defendant groups, and Covariates is No, No, Yes for both defendant groups.
Notes: Charge and sentence severity shown in years. Left Intercept is the estimated outcome immediately before the announcement. For each defendant type, the second and third columns include district-fixed effects, and the third column conditions on gender and crime type. Standard errors clustered at the district level. Only African-American and white defendants (98% of all defendants) included.
Consistent with the graphical analysis above, we find that across specifications, the announcement drove increases in charge severity and sentence length for unaligned defendants, and decreases for aligned defendants.Footnote 25 Overall, for unaligned defendants, the executive order corresponded to an average increase in initial charge severity of two to three years, and an average increase in actual sentence length of four to five months. Aligned defendants appear to have experienced about a two-year decrease in initial charge severity, and around a 1.5-month decrease in sentence severity, although the last effect is consistently statistically insignificant at conventional levels.Footnote 26
These results are broadly robust to a range of alternative specifications, placebo tests, and bandwidth choices. First, in Figure 3, we replicate our analysis but replace the announcement date (April 22, the third Friday in April) with placebo dates on the third Friday of the two months prior to and following the announcement, respectively. The results are encouraging.Footnote 27 Second, if our hypothesis is correct, only felony charges and sentences should have been affected by the announcement, because only felony sentences are disenfranchising. Accordingly, in Table 3, we estimate the announcement’s effect on misdemeanor offenses charged or sentenced in Circuit Court in 2016. Consistent with our theory, the resulting estimates are insignificant across all specifications. Third, in Figure 4, we present the coefficient estimates for our covariate-adjusted local-linear regressions beginning with a five-day, user-set bandwidth on either side of the announcement and increasing in two-day increments to a 90-day bandwidth. As is clear from the figure, our results track those presented in Table 2.
Replication of main results, placebo dates.
Figure 3 Long description
A point and error bar plot titled, Aligned Defendants. The horizontal axis label reads, Date, with tick labels Feb 19, Mar 18, Apr 22, May 20, Jun 17. The vertical axis label reads, R. D. Estimate and 95 percent C. I, with tick labels negative 4, negative 2, 0, 2, 4. A dashed horizontal reference line is drawn at 0. Five point markers with vertical error bars are plotted. The point at Feb 19 is below 0, with an error bar spanning across 0. The point at Mar 18 is above 0, with an error bar spanning across 0. The point at Apr 22 is below 0, with an error bar spanning across 0 and this point and its error bar are styled differently from the other four. The point at May 20 is above 0, with an error bar spanning across 0. The point at Jun 17 is above 0, with an error bar spanning across 0. The image B showing a point and error bar plot titled, Aligned Defendants. The horizontal axis label reads, Date, with tick labels Feb 19, Mar 18, Apr 22, May 20, Jun 17. The vertical axis label reads, R. D. Estimate and 95 percent C. I, with tick labels negative 2, negative 1, 0, 1. A dashed horizontal reference line is drawn at 0. Five point markers with vertical error bars are plotted. The point at Feb 19 is above 0, with an error bar spanning across 0. The point at Mar 18 is below 0, with an error bar spanning across 0. The point at Apr 22 is near 0 and slightly below 0, with an error bar spanning across 0 and this point and its error bar are styled differently from the other four. The point at May 20 is near 0 and slightly below 0, with an error bar spanning across 0. The point at Jun 17 is above 0, with an error bar spanning across 0. The image C showing a point and error bar plot titled, Unaligned Defendants. The horizontal axis label reads, Date, with tick labels Feb 19, Mar 18, Apr 22, May 20, Jun 17. The vertical axis label reads, R. D. Estimate and 95 percent C. I, with tick labels negative 4, negative 2, 0, 2, 4. A dashed horizontal reference line is drawn at 0. Five point markers with vertical error bars are plotted. The point at Feb 19 is below 0, with an error bar spanning across 0. The point at Mar 18 is above 0, with an error bar spanning across 0. The point at Apr 22 is above 0, with an error bar above 0 and this point and its error bar are styled differently from the other four. The point at May 20 is above 0, with an error bar above 0. The point at Jun 17 is above 0, with an error bar spanning across 0. The image D showing a point and error bar plot titled, Unaligned Defendants. The horizontal axis label reads, Date, with tick labels Feb 19, Mar 18, Apr 22, May 20, Jun 17. The vertical axis label reads, R. D. Estimate and 95 percent C. I, with tick labels negative 2, negative 1, 0, 1. A dashed horizontal reference line is drawn at 0. Five point markers with vertical error bars are plotted. The point at Feb 19 is above 0, with an error bar spanning across 0. The point at Mar 18 is below 0, with an error bar spanning across 0. The point at Apr 22 is above 0, with an error bar above 0 and this point and its error bar are styled differently from the other four. The point at May 20 is below 0, with an error bar spanning across 0. The point at Jun 17 is above 0, with an error bar spanning across 0. Across the four plots, the Apr 22 point is the only point that is consistently styled differently. In the two Unaligned Defendants plots, the Apr 22 point is above 0 with an error bar above 0. In the two Aligned Defendants plots, the Apr 22 point is at or below 0 with an error bar spanning across 0.
Replication of main results, variation of bandwidth.
Figure 4 Long description
The title, Charges For Unaligned Defendants. The horizontal axis label is, Bandwidth, with values from 0 to 90. The vertical axis label is, Estimate and 95 percent CI, with values from negative 10 to 14. The legend lists, Unadjusted and, Adjusted. Each series is drawn as a line with point markers and vertical confidence interval bars at each bandwidth value. The plotted estimates start at bandwidth near 5 with values above 0 and wide confidence intervals. As bandwidth increases from about 10 to about 25, the estimates move closer to 0 and the confidence intervals become narrower. From about bandwidth 30 through about 90, both series cluster near a small positive value above 0 with relatively short confidence interval bars. The image B showing the title, Sentences For Unaligned Defendants. The horizontal axis label is, Bandwidth, with values from 0 to 90. The vertical axis label is, Estimate and 95 percent CI, with values from negative 2 to 3. The legend lists, Unadjusted and, Adjusted. Each series is drawn as a line with point markers and vertical confidence interval bars at each bandwidth value. The plotted estimates at bandwidth near 5 are above 0 with wide confidence intervals. From about bandwidth 10 to about 30, the estimates decline toward 0 while the confidence intervals shorten. From about bandwidth 30 through about 90, both series remain slightly above 0 with small changes across bandwidth. The image C showing the title, Charges For Aligned Defendants. The horizontal axis label is, Bandwidth, with values from 0 to 90. The vertical axis label is, Estimate and 95 percent CI, with values from negative 10 to 14. The legend lists, Unadjusted and, Adjusted. Each series is drawn as a line with point markers and vertical confidence interval bars at each bandwidth value. The plotted estimates at bandwidth near 5 are near 0 with wide confidence intervals. Between about bandwidth 10 and about 20, the estimates dip below 0, reaching the lowest point in the early bandwidth range and the confidence intervals remain relatively wide. From about bandwidth 25 through about 90, both series rise toward 0 and then stay close to 0 with narrower confidence interval bars. The image D showing the title, Sentences for Aligned Defendants. The horizontal axis label is, Bandwidth, with values from 0 to 90. The vertical axis label is, Estimate and 95 percent CI, with values from negative 2 to 3. The legend lists, Unadjusted and, Adjusted. Each series is drawn as a line with point markers and vertical confidence interval bars at each bandwidth value. The plotted estimates at bandwidth near 5 are near 0 with wide confidence intervals. From about bandwidth 10 to about 25, the estimates stay close to 0 while the confidence intervals shorten. From about bandwidth 30 through about 90, both series remain close to 0 with small variation across bandwidth.
Effect of McAuliffe’s order, by alignment status, on misdemeanor offenses
Table 3 Long description
Two panels report charge severity and sentence severity, each with results for unaligned defendants and aligned defendants under two specifications, one without covariates and one with covariates. Panel A, charge severity: RD estimate is 0.029 and 0.025 for unaligned and aligned without covariates, and 0.038 and 0.041 with covariates; left intercept is 0.909 and 0.910 without covariates, and 0.900 and 0.899 with covariates. Panel B, sentence severity: RD estimate is minus 0.001 and minus 0.006 without covariates, and 0.016 and 0.016 with covariates; left intercept is 0.035 and 0.035 without covariates, and 0.036 and 0.036 with covariates. Bandwidth values are 58.710, 68.743, 47.433, and 49.872 in Panel A, and 66.748, 67.056, 77.875, and 73.996 in Panel B. Effective observations are 1555, 1881, 1616, and 1658 in Panel A, and 1803, 1829, 2604, and 2514 in Panel B. District FE is Y in all columns, and covariates are N for the first specification and Y for the second specification in both panels.
Notes: Charge and sentence severity shown in years. Left Intercept is the estimated outcome immediately before the announcement. For each defendant type, the first column includes district-fixed effects, and the second column also conditions on gender and crime type. Robust standard errors clustered at the district level. Only African-American and white defendants included (98% of all defendants).
In the Online Appendix, we probe the robustness of our results to different theories of alignment and the inclusion of additional data. First, we re-estimate our main models after removing all districts headed by Independent prosecutors, and show that the results persist, although they are sometimes weaker (Table A1, Figures A1 and A2). Second, we test the robustness of our theory of alignment to an alternative treatment in which both white and African-American felony defendants living in strong Democratic districts (defined as districts with Democratic prosecutors in which at least 70% of the population voted for Barack Obama in 2012) are coded as Democrat-aligned (Table A2). The results are consistently signed and qualitatively similar, but they are weaker. Third, we re-estimate our main models including probation violation reinstatements (Table A3) and show that the results are similar. Finally, because elected chief prosecutors generally manage a team of assistant prosecutors, we explored the possibility that the announcement’s effect might depend on chief prosecutors’ control over their agents: in larger districts, subordinate prosecutors might have more independence, and the announcement might have had less of an effect. However, we find little evidence of a size-based effect (Figure A4).
4.2. Alternative specifications
The RDiT analysis above relied on the assumption that potential outcomes for aligned and unaligned defendants are a smooth function of the running variable. Because the announcement was unexpected, a plausible alternative assumption is that for a short enough time window around the announcement, the treatment (the announcement) was as-if-randomly assigned. Accordingly, we conduct a series of simple, pooled fixed effects regressions for two to ten-day windows around the announcement. In these estimates, the treatment takes the form of a simple indicator variable which switches from zero to one on the date of the announcement. The results are presented in Figure 5. Despite the narrow time windows, we observe consistent and almost-immediate post-announcement increases in charge and sentence severity for unaligned defendants, and consistent decreases for the aligned. These effects converge to effects similar in size to those in Table 2.
Effect of announcement, pooled difference-in-means regressions.
Figure 5 Long description
Charge Severity, Unaligned Defendants. The horizontal axis label is Window Around Announcement (Days), with values 2, 3, 4, 5, 6, 7, 8, 9, 10. The vertical axis label is Estimate and 90 percent and 95 percent CI, with labeled values negative 12, negative 8, negative 4, 0, 4, 8, 12, 16. A horizontal reference line is drawn at 0. The legend lists Unadjusted and Adjusted, shown as two differently styled point and error bar series. At day 2 and day 3, the central points for both series are above 0, with long vertical confidence intervals spanning across multiple tick intervals. From day 4 through day 10, the central points remain above 0 and the confidence intervals are shorter than at day 2 and day 3. Sentence Severity, Unaligned Defendants. The horizontal axis label is Window Around Announcement (Days), with values 2, 3, 4, 5, 6, 7, 8, 9, 10. The vertical axis label is Estimate and 90 percent and 95 percent CI, with labeled values negative 2, 0, 2, 4. A horizontal reference line is drawn at 0. The legend lists Unadjusted and Adjusted, shown as two differently styled point and error bar series. At day 2 and day 3, the central points for both series are above 0, with long vertical confidence intervals extending from below 0 to above 0. From day 4 through day 10, the central points are close to 0 and above 0, with short confidence intervals clustered near the 0 line. Charge Severity, Aligned Defendants. The horizontal axis label is Window Around Announcement (Days), with values 2, 3, 4, 5, 6, 7, 8, 9, 10. The vertical axis label is Estimate and 90 percent and 95 percent CI, with labeled values negative 12, negative 8, negative 4, 0, 4, 8, 12, 16. A horizontal reference line is drawn at 0. The legend lists Unadjusted and Adjusted, shown as two differently styled point and error bar series. Across day 2 through day 10, the central points for both series are below 0. At day 2 and day 3, the confidence intervals are longer than at later days. From day 4 through day 10, the central points remain below 0 and the confidence intervals are shorter. Sentence Severity, Aligned Defendants. The horizontal axis label is Window Around Announcement (Days), with values 2, 3, 4, 5, 6, 7, 8, 9, 10. The vertical axis label is Estimate and 90 percent and 95 percent CI, with labeled values negative 2, 0, 2, 4. A horizontal reference line is drawn at 0. The legend lists Unadjusted and Adjusted, shown as two differently styled point and error bar series. At day 2 and day 3, the central points are near 0, with confidence intervals extending above and below 0. From day 4 through day 10, the central points stay close to 0, with short confidence intervals near the 0 line. Across the four plots, the unaligned charge severity estimates are positioned above 0 while the aligned charge severity estimates are positioned below 0 and both sentence severity plots show estimates clustered near 0 at day 4 through day 10 compared with wider intervals at day 2 and day 3.
In the Online Appendix, we also present the results of a complete randomization inference procedure proposed by Cattaneo et al. (Reference Cattaneo, Idrobo and Titiunik2024). The procedure tests a sharp null hypothesis of no treatment for any unit for a series of small windows around the cut-point by selecting a random subset of possible treatment profiles, and measuring the extremeness of the observed test statistic against those generated from the randomly chosen profiles. We limit our examination to windows (mass points) of one to five days around the announcement, among the subset of districts for which data are available in these windows before and after the treatment. The results are shown in Table A4. Coefficient estimates are consistently signed, although they are statistically significant only for charge severity.
4.3. Alternative explanations
Finally, in Section B.4 of the Online Appendix, we consider several alternative explanations for our results. Specifically, we rule out the possibility that our results were generated by prosecutor- or district-level differences in racial attitudes, by showing that results are similar for African-American and white aligned and unaligned defendants. We also test whether prosecutors’ personal opposition to the announcement affected their post-announcement charging/sentencing behavior, and show that it did not.
5. Mechanisms
Turning to an examination of the mechanisms behind our results, we begin by asking how these results came about. Here, we work to understand the channels through which the announcement affected disenfranchisement status: did prosecutors primarily adjust charges in response to the announcement, or did they directly alter sentences as well—and if so, by what methods?
Next, we consider why. Here, we attempt to disentangle two possible motives for charge/sentence manipulation: a personal, office-seeking motive, in which prosecutors seek to maximize the likelihood of their own reelections, and a partisan, policy-seeking motive, in which prosecutors seek to improve the likelihood of reelection for copartisans at other levels of government.
5.1. Direct and indirect effects on sentencing
In this section, we consider the channels through which Governor McAuliffe’s announcement may have shaped charge and sentence severity. An initial question is whether the announcement directly affected prosecutors’ sentencing choices, or only changed their initial charging behavior. We attempt to answer this question in two ways. First, we re-estimate the announcement’s effect on average prison sentences, restricting our analysis to cases charged before the announcement. The results (presented in Online Appendix Table A5) are similar to those in Table 2, suggesting that our main sentencing results do capture some direct effect on sentencing.Footnote 28
Second, we examine the announcement’s effect on prosecutors’ use of five separate tools which directly shape sentencing outcomes: dismissals, charge reductions to misdemeanors, and requesting a time served, supervised probation, or prison sentence. Ideally, we would examine how prosecutors’ use of each tool changed in real time after the announcement. Unfortunately, we lack dates for informal plea agreements and amendments prior to cases’ final resolutions. As a next-best strategy, we conduct a local-linear RD estimation of the announcement’s effect on the incidence of each outcome (recorded at the conclusion of the case). The results, displayed in Figure 6, show that for unaligned defendants, the announcement decreased the probability that felony charges were dismissed, reduced to misdemeanors, or sentenced to time served, and increased the probability of receiving a prison or probation sentence. For aligned defendants, the announcement somewhat decreased the probability of receiving a prison or probation sentence, and significantly increased the probability of a time served sentence or charge reduction to a (non-disenfranchising) misdemeanor. We show in the Online Appendix (Figure A3) that these effects largely persist in a series of pooled fixed effects regressions for two-to-ten-day windows around the announcement. We find an especially strong effect on the provision of time served sentences to aligned defendants, perhaps because these sentences permit prosecutors to obtain convictions on felony offenses without—after the announcement—ever causing disenfranchisement, and show in Table A6 that this result is robust to the Fisher complete randomization test we conducted in the previous section.
Effect of announcement on sentencing outcomes.
Figure 6 Long description
Unaligned Defendants. The y-axis label is, RDD Estimate and 95 percent CI, ranging from minus 0.15 to 0.15 with ticks at minus 0.10, minus 0.05, 0, 0.05, 0.10 and 0.15. The x-axis categories are Case Dismissed, Charge(s) reduced to misdemeanor(s), Sentenced to Time Served, Supervised Probation and Prison Sentence. A horizontal dashed reference line is drawn at 0. Two vertical interval estimates are shown for each category, labeled in the legend as Unadjusted and Adjusted. Case Dismissed shows both intervals below 0, with centers near minus 0.05 and endpoints roughly between about minus 0.08 and about minus 0.02. Charge(s) reduced to misdemeanor(s) shows both intervals below 0, with centers near minus 0.08 and endpoints roughly between about minus 0.12 and about minus 0.04. Sentenced to Time Served shows both intervals below 0, with centers near minus 0.05 and endpoints roughly between about minus 0.08 and about minus 0.02. Supervised Probation shows both intervals above 0, with centers near 0.05 and endpoints roughly between about 0.00 and about 0.10. Prison Sentence shows both intervals above 0, with centers near 0.10 and endpoints roughly between about 0.05 and about 0.15. Aligned Defendants. The y-axis label is, RDD Estimate and 95 percent CI, ranging from minus 0.15 to 0.15 with ticks at minus 0.10, minus 0.05, 0, 0.05, 0.10 and 0.15. The x-axis categories are Case Dismissed, Charge(s) reduced to misdemeanor(s), Sentenced to Time Served, Supervised Probation and Prison Sentence. A horizontal dashed reference line is drawn at 0. Two vertical interval estimates are shown for each category, labeled in the legend as Unadjusted and Adjusted. Case Dismissed shows both intervals below 0, with centers near minus 0.05 and endpoints roughly between about minus 0.08 and about minus 0.02. Charge(s) reduced to misdemeanor(s) shows both intervals above 0, with centers near 0.06 and endpoints roughly between about 0.03 and about 0.09. Sentenced to Time Served shows both intervals above 0, with centers near 0.07 and endpoints roughly between about 0.04 and about 0.10. Supervised Probation shows both intervals below 0, with centers near minus 0.06 and endpoints roughly between about minus 0.10 and about minus 0.02. Prison Sentence shows both intervals below 0, with centers near minus 0.05 and endpoints roughly between about minus 0.08 and about minus 0.02.
5.2. The total sentencing effect
The results above suggest that to understand the announcement’s full effect on sentencing (and disenfranchisement) outcomes, we must account for both its direct effect via sentencing strategies and its indirect effect via charges. The latter is difficult, because all cases charged post-announcement were necessarily sentenced post-announcement. Our solution is to estimate the pre-announcement relationship between charge severity and sentence severity, then use these estimates to predict the effect of post-announcement charging shifts, accounting for uncertainty in both predictions by performing these calculations for each of 1,000 cluster-bootstrapped samples.
Figure 7 displays our estimates of the indirect change in sentence severity induced by post-announcement changes in charge severity, across bootstrapped samples, for aligned defendants (left) and unaligned defendants (right). Among our samples of aligned defendants, we estimate that post-announcement decreases in charge severity led to a 30 to 40-day decrease in average prison sentences, although the effect skirts conventional levels of statistical significance. For unaligned defendants, we estimate that post-announcement increases in charge severity led to a 50–60-day average increase in sentence length.
Inferring the announcement’s total effect on sentencing via our estimates of its direct and indirect effects requires the assumption that the mapping from charge to sentence severity was not too altered by the announcement. Given this assumption, we can place rough bounds on the size of the announcement’s effect. Recall that our estimate of the direct effect on sentencing, presented in Table 3, was a prison time increase of four to five months for unaligned defendants, and a (statistically insignificant) decrease of approximately one to one and a half months for aligned defendants. If charge severity shifts substitute partially or entirely for sentencing shifts, these changes may approximate the total effect. If charging and sentencing adjustments are complements, then after the announcement, unaligned defendants may have received sentences as much as seven months longer, and the aligned as much as three months less.
Bootstrapped estimates of indirect sentencing effect.
Figure 7 Long description
A histogram titled, Aligned Defendants. The horizontal axis is labeled, Bootstrapped Estimates, with tick labels negative 0 point 6, negative 0 point 4, negative 0 point 2, 0 and 0 point 2. The vertical axis is labeled, Density, with tick labels 0, 2, 4 and 6. Two overlaid histograms are shown with a legend listing, Unadjusted and, Adjusted. The bars form a single main cluster centered around negative 0 point 2, with the tallest bars between about negative 0 point 25 and negative 0 point 15. The distribution extends with lower bars toward negative 0 point 6 and toward 0 point 2. Multiple vertical reference lines are drawn, including a solid line near negative 0 point 2 and another solid line slightly to the right of it, plus dashed vertical lines positioned around negative 0 point 3, around negative 0 point 2, around 0 and slightly above 0. The image B showing a histogram titled, Unaligned Defendants. The horizontal axis is labeled, Bootstrapped Estimates, with tick labels negative 0 point 2, 0, 0 point 2, 0 point 4 and 0 point 6. The vertical axis is labeled, Density, with tick labels 0, 1, 2, 3, 4 and 5. Two overlaid histograms are shown with a legend listing, Unadjusted and, Adjusted. The bars form a single main cluster centered around 0 point 2, with the tallest bars between about 0 point 15 and 0 point 25. The distribution extends with lower bars toward negative 0 point 2 and toward 0 point 6. Multiple vertical reference lines are drawn, including a solid line at about 0 point 2 and another solid line slightly to the right of it, plus dashed vertical lines positioned near 0, near 0 point 1, near 0 point 3 and near 0 point 4.
5.3. Personal or partisan motives?
Were Virginia’s chief prosecutors manipulating disenfranchisement status to further their personal electoral prospects, or to improve the electoral fortunes of copartisans more broadly? Both motives are theoretically possible. With regard to prosecutors’ own races, the negligible cost of manipulation—since defendant partisanship can be readily inferred—may make it worthwhile even when disenfranchisement is unlikely to tip the scale: after all, prosecutors do not know what their margin of victory will be, and a prosecutor who prevents a single vote for his opponent has effectively voted twice. At the same time, Virginia is known as a swing state where statewide (and federal) races are sometimes decided with very small margins, making felon disenfranchisement a potentially valuable tool in shaping outcomes statewide or even nationally—and the possibility that felon enfranchisement in Virginia might tip the scale in the 2016 presidential election was explicitly raised post-announcement (Horwitz and Portnoy, Reference Horwitz and Portnoy2016).
To disentangle these motives, we begin with the hypothesis that prosecutors wishing to affect the outcome of an election might attempt to front-load disposition dates for unaligned defendants before the election, but hold off on sentencing aligned defendants until after it. This would generate a post-election decrease in the number of daily case dispositions for unaligned defendants, but an increase for aligned defendants. Prosecutors concerned only about their own electoral fortunes should arguably engage in such behavior only around their own elections, while prosecutors more broadly interested in electoral outcomes might be expected to manipulate disposition dates around every election.Footnote 29
To explore this hypothesis, we plotted a simple district-weighted count of felony cases decided for 50 days on either side of each federal (even-year) or state (odd-year) election in Virginia between 2012 and 2019, and separately fitted linear predictions and kernel-weighted polynomial curves to either side of the election date. The results are presented in the Online Appendix (Figures A9 and A10). We find little evidence for an effect in state election years, but in three of four federal elections we observe higher numbers of unaligned cases decided prior to the election, followed by a substantial post-election drop.
If prosecutors engage in strategic disenfranchisement to further partisan goals, more politically engaged prosecutors may be more enthusiastic manipulators of disenfranchisement. Because Commonwealth’s Attorneys are elected, they all arguably meet baseline levels of political engagement. To determine whether prosecutors exhibited varying levels of concern for political outcomes besides their own electoral contests, we collected their political donation behavior, matching them by first and last name (and middle initial) to Virginia donors listed in the DIME (Bonica, Reference Bonica2014, Reference Bonica2016). DIME contains biennial information on individual contributions to local, state, and federal elections from 1980 to 2022 as well as common-space ideal-point scores (“cf scores”) for donors. We successfully obtained 95 prosecutor-DIME donor matches, nearly all of which we validated against occupation (“prosecutor,” “Commonwealth’s Attorney”) employer information (“County”), and/or addresses. We cross-checked unmatched prosecutors against the OpenSecrets database and the Virginia Public Access ProjectVAData (VPAP) records to confirm that they had indeed made no (recorded) contributions.
We begin by testing whether political donor prosecutors were more responsive to the announcement than non-donors, and whether more recent donors were more responsive than less recent donors. Accordingly, we use DIME’s biennial donation information to construct a set of measures of donation recency where the largest measure includes all donations within the entire pre-announcement interval for which we have DIME data (1980–2016), and the smallest includes only donations made between 2014 and 2016. We then separately estimate the announcement’s effect on prosecutors who did/did not donate within each interval. Figure 8 shows the district- and covariate- adjusted effect of the announcement on charging and sentencing behavior among prosecutors who did (top row) and did not (bottom row) donate within each interval. As the figure shows, donors (especially more recent donors) appear to respond consistently to the announcement, while non-donors display little change in behavior overall.
Announcement effect by recency of last donation.
Figure 8 Long description
Eight dot and error bar plots with a horizontal reference line at 0 and dots with vertical error bars labeled as 95 percent CI. Two section headings appear: Donated Within and Did Not Donate Within. Each plot uses the vertical axis label, RDD Estimate and 95 percent CI. Shared horizontal axis categories shown as tick labels are, 1980 to 2016, 1996 to 2016, 2006 to 2016, 2014 to 2016. The Donated Within section uses the horizontal axis label, Donation Made Within. The Did Not Donate Within section uses the horizontal axis label, No Donation Made Within. Donated Within, Charges For Unaligned Defendants: vertical axis range negative 8 to 8. Dots are positioned above 0 across the categories, with dot positions around 3 to 5. Donated Within, Charges For Aligned Defendants: vertical axis range negative 8 to 8. Dots are positioned below 0 across the categories, with dot positions around negative 1 to negative 4. Donated Within, Sentences For Unaligned Defendants: vertical axis range negative 1 to 1. Dots are positioned above 0 across the categories, with dot positions around 0.4 to 0.8. Donated Within, Sentences for Aligned Defendants: vertical axis range negative 1 to 1. Dots are positioned near 0 and slightly below 0 across the categories, with dot positions around negative 0.2 to 0. Did Not Donate Within, Charges For Unaligned Defendants: vertical axis range negative 8 to 8. Dots are positioned near 0 and above 0 across the categories, with dot positions around 0 to 2. Did Not Donate Within, Charges For Aligned Defendants: vertical axis range negative 8 to 8. Dots are positioned near 0 and above 0 across the categories, with dot positions around 0 to 4. Did Not Donate Within, Sentences For Unaligned Defendants: vertical axis range negative 1 to 1. Dots are positioned near 0 and above 0 across the categories, with dot positions around 0 to 0.6. Did Not Donate Within, Sentences for Aligned Defendants: vertical axis range negative 1 to 1. Dots start above 0 and move below 0 across the categories, with dot positions around 0.5 to negative 0.2.
Other possible proxies for political engagement are ideological extremism (more extreme prosecutors may care more about electoral outcomes) and donation size (more generous donors may care more about outcomes). Using the DIME dataset, we construct measures of both. To measure ideology, we use common-space DIME scores (which exist only for donors), and label prosecutors as “extreme” if their cf-scores exceed the median among prosecutors on “their” side of 0.Footnote 30 An ideal measure of donation size would adjust for characteristics like wealth and age to avoid conflating these characteristics with political involvement. Unfortunately, we lack information on these characteristics. As a first cut, we used news reports, professional networking sites, and historical election records to hand-code prosecutors’ years of tenure as Commonwealth’s Attorneys, calculated prosecutors’ average annual donations during their time in office, and then treated prosecutors as large donors if their average yearly gifts while in office exceed the median.
The results of this exercise are presented in the Online Appendix (Figure A7). We find no consistent difference in the behavior of “extreme” as opposed to “moderate” prosecutors. However, we do find some differences in the post-announcement behavior of larger, as opposed to smaller, donors: overall, individuals who gave larger average amounts during their tenure as Commonwealth’s Attorneys appear to have responded somewhat more strongly to the announcement.
While partisan feeling can arguably be proxied for through measures of political engagement, it is difficult to measure the strength of a prosecutor’s personal desire for reelection. However, it seems plausible that politically vulnerable, office-seeking prosecutors might be especially prone to voter pool manipulation. This possibility is difficult to test rigorously, because political vulnerability is endogenous to political aptitude. Nevertheless, as a first cut, we code a prosecutor as vulnerable if he faced an opponent who garnered at least 10% of the vote in the previous election, and separately evaluate the announcement’s effect on this subgroup of prosecutors and their “safe” counterparts. We show in the Online Appendix (Figure A8) that both groups engaged in similar charging and sentencing behavior post-announcement.Footnote 31
6. Discussion
Scholars interested in the strategic behavior of elected prosecutors have often focused on their incentives to improve conviction rates, sentencing outcomes, and trial wins in order to signal quality or competence to a fixed pool of voters. Such behavior would arguably be consistent with a prosecutor’s responsibility, as an elected official, to perform the will of her constituents—albeit in tension with her obligation as an officer of the court to perform justice. Our findings complicate the story further, suggesting that prosecutors may also use the tools of their office to shape the voter pool and improve the chance of a favored electoral outcome.
Our findings also contribute to recent scholarship on the ways in which political actors may attempt to “tilt” electoral outcomes in their own favor. Although existing work focuses on the incentives of state-level politicians to construct laws and electoral rules that bend outcomes toward themselves (Eubank and Fresh, Reference Eubank and Fresh2022; Helmke et al., Reference Helmke, Kroeger and Paine2022), our findings suggest that the local officials who implement these laws may also play an important role. An interesting avenue for future research would be to explore the extent to which local-level and state-level actors have complementary, as opposed to competing, goals. For example, if government is divided at the state and local levels, laws written at the state level with a view to disenfranchising one group might be used, at the local level, to disenfranchise another.
Finally, a major implication of our paper is that the composition of the felon population may depend on the partisan identity of local criminal justice officials. More specifically, the assignment of felon status may be endogenous to the degree of political threat or benefit a defendant poses to a prosecutor. Further research might explore the implications of this endogeneity for broader studies of felon political behavior.
Acknowledgements
We thank Chris Berry, Tom Clark, Sarah Daniel, Jamie Druckman, Sanford Gordon, Carlo Horz, Alex Lee, Murat Mungan, J.J. Prescott, the participants at MPSA 2022, Berkeley’s Comparative Politics Colloquium, the 2024 Law and Economics Conference at Texas A&M School of Law, and the 2025 Justice and Injustice Conference at MIT, and two anonymous reviewers, for their helpful comments.
Declaration of Interests
None.
Funding Statement
None.
Supplementary material
The supplementary material for this article can be found at https://doi.org/10.1017/psrm.2026.10139.
Open access
