Official Corruption Abroad and in the United States

Official corruption, conventionally defined as the use of public office—elected or otherwise—for private gain (e.g., Nye Reference Nye1967), is the subject of a fertile research agenda in empirical and theoretical political economy. Scholars working in the comparative context have examined the causal antecedents of corruption, examining its sociodemographic (Lipset, Seong, and Torres Reference Lipset, Seong and Torres1993), cultural (Rose-Ackerman Reference Rose-Ackerman1999; Treisman Reference Treisman2000), and institutional (Brown, Touchton, and Whitford Reference Brown, Touchton and Whitford2006; La Porta et al. Reference La Porta, Lopez-de-Silanes, Shleifer and Vishny1999; Persson, Tabellini, and Trebbi Reference Persson, Tabellini and Trebbi2003) origins.

Corruption has also been the subject of scrutiny for numerous observers of American politics. In Volume II of The American Commonwealth, Lord Bryce endeavors to assess the prevalence of bribery, kickbacks, and misappropriation of public funds in different branches of federal, state, and local governments (Reference Bryce1995 [1888], 832–3). More recently, scholars of domestic governance have sought to explain variation among the states in perceptions of corruption (Boylan and Long Reference Boylan and Long2003) and in federal corruption prosecutions and conviction rates. Goel and Nelson (Reference Goel and Nelson1998) find higher corruption conviction rates in states with larger government expenditures. Meier and Holbrook (Reference Meier and Holbrook1992) detect higher conviction rates in more urban states with less educated citizenries, larger fractions of citizens with Irish or Italian ancestries, lower voter turnout, and higher total government employment. Alt and Lassen (Reference Alt and Lassen2002) find higher perceived levels of corruption in states with closed primaries, restrictive ballot access for voter initiatives, and loose restrictions on campaign finance.

Prosecution of Public Corruption in the United States

The Justice Department prosecuted nearly 5,000 defendants classified as state or local “corrupt government officials” from 1986 to 2008 (Transactional Records Access Clearinghouse [TRAC], Syracuse University). The lead charge in 25% of the indictments was violation of 18 U.S.C. 1951, the Hobbs Act, which prohibits robbery or extortion affecting interstate commerce. The next most common offense was under 18 U.S.C. 666 (19% of prosecutions), which outlaws theft and bribery in entities receiving more than $10,000 in federal funds. Other commonly employed corruption statutes included the mail fraud statute (18 U.S.C. 1341, 12% of cases), the statute governing conspiracies to defraud the federal government (18 U.S.C. 371, 9% of cases), and the Racketeer Influenced and Corrupt Organizations statute (18 U.S.C. 1962, 4% of cases).

Although the 93 U.S. Attorneys and their assistants retain significant discretion over whether to bring a case (cf. Richman Reference Richman1999), they do not operate in a vacuum.Footnote ² Corruption cases nearly always begin with investigations by other agencies, which may or may not end in referrals to a U.S. Attorney's Office. Of the approximately 16,000 referrals to the Justice Department concerning state and local corruption cases from 1986 to 2008, a large majority (82%) came from the FBI. By comparison, the next largest source, the Internal Revenue Service (IRS), accounted for only 3% of referrals. Figure 1 outlines the typical progression of a case once it is referred to a U.S. Attorney's Office, along with the number of referrals by outcome. The office can drop the referral outright. If it does not, the case becomes a “matter,” typically developed by an Assistant U.S. Attorney and the referring agency. The office can subsequently decline the case or bring it before a grand jury to bring an indictment. (It is exceedingly rare for a grand jury to refuse to indict.) Roughly one third of referrals (4,970 cases) eventually resulted in indictments. Of the indictments, 86% (4,264 cases) resulted in convictions (roughly four fifths of which were guilty pleas, and the remainder guilty verdicts), 5% (243 cases) in jury verdicts of not guilty, and 9% (463 cases) in dismissals.

FIGURE 1.

Disposition of State and Local Corruption Referrals from Investigative Agencies by U.S. Attorneys' Offices, 1986–2008

Note: Outcomes not depicted include referrals in which charges were eventually folded into other cases, or in which charges were dropped and then refiled.

The use of law enforcement generally, and federal law enforcement in particular, as a means to reduce public corruption at the state and local levels is largely an innovation of the second half of the 20th century (Anechiarico and Jacobs Reference Anechiarico and Jacobs1994). Not surprisingly, this development has been accompanied by concerns that the discretion to investigate and prosecute officials for violating anticorruption statutes could be abused for partisan gain (Abrams and Beale Reference Abrams and Beale2006).

Politicization and Bias

Political scientists and public administration scholars have long recognized efforts by presidents to influence bureaucratic policy making and performance, especially through the placement of loyalist appointees in key positions of authority (e.g., Lewis Reference Lewis2008; Moe Reference Moe1985; Nathan Reference Nathan1975). At the same time, other scholars of bureaucracy have pointed to the success of bureaucratic entrepreneurs in cultivating a degree of policy-making autonomy from their political principals (Carpenter Reference Carpenter2001) or advancing “strategically neutral” (i.e., self-consciously apolitical) procedures (Huber Reference Huber2007).

The possibility that law enforcement might be politicized to serve the president's political aims, and the institutional resilience of the Justice Department against such efforts, has been a recurrent theme throughout the department's history. Throughout much of the 20th century, “Main Justice” (the department's Washington, DC, headquarters) sought to centralize control over the far-flung U.S. Attorneys, who had been largely politically autonomous since the office's creation in 1789 (Eisenstein Reference Eisenstein1978). Whitney North Seymour, Jr., himself a former U.S. Attorney, describes the electoral motivations behind the Nixon Justice Department's prioritization of narcotics prosecution (Reference Seymour1975, 119–35, 226). More recently, Whitford (Reference Whitford2002) finds evidence that U.S. Attorneys' aggregate caseloads respond to national political trends. Meier and Holbrook (Reference Meier and Holbrook1992) find some evidence that public officials from Democratic localities were disproportionately targeted under Reagan, whereas Heidenheimer (Reference Heidenheimer, Heidenheimer, Johnston and LeVine1989, 583–4) discusses anecdotal evidence of disproportionate targeting under Nixon and Ford.

The issue of politicization of law enforcement achieved most recent salience in April 2007, when newly elected Democratic majorities in Congress convened hearings to investigate the dismissal of seven U.S. Attorneys on December 7, 2006, as well as several others in the preceding two years. Critics of the Bush administration contended that a failure to employ public corruption prosecutions for partisan ends lay in part behind the firings, mustering anecdotal evidence to support the claim. One fired attorney, Carol Lam (U.S. Attorney for Southern California), had indicted San Diego Republican Congressman Randy “Duke” Cunningham. A January New York Times editorial posited that the Cunningham investigation had also led her to investigate Republican Representative Jerry Lewis, to the consternation of Republican officials. Another attorney, David Iglesias (New Mexico), testified before the Senate Judiciary Committee that he had received telephone calls from Senator Pete Domeneci and Representative Heather Wilson (both New Mexico Republicans) inquiring about progress in corruption investigations of prominent New Mexico Democrats. A third, John McKay (Western Washington), testified that the Chief of Staff of Representative Doc Hastings (R-WA) had called to inquire about federal investigations into voter fraud following the 2004 Washington gubernatorial election. A fourth, Thomas M. DiBiagio (Maryland), in an interview with the New York Times, claimed his dismissal was the result of his investigation of Republican Governor Robert L. Ehrlich, Jr. (Lichtblau Reference Lichtblau2007). Most recently, a joint report of the DOJ's Office of Professional Responsibility and Inspector General references allegations that the Attorney General's Chief of Staff, Kyle Sampson, removed U.S. Attorney for Eastern Wisconsin Steven Biskupic from a list of potential targets for termination following his prosecution of a Democratic public official (USDOJ 2008, 19).

Primitives and Equilibrium

There is a prosecuting attorney a and N public officials, indexed by i = 1, . . ., N.Footnote ⁹ The prosecuting attorney is characterized by her partisan affiliation p _a ∈ {D, R}.Footnote ¹⁰ A public official is described by his partisan affiliation p _i ∈ {D, R} and his type m _i ∈ ℝ.Footnote ¹¹ The partisan affiliations of official i and prosecuting attorney a are common knowledge. Type is initially the official's private information and represents the marginal benefit to the official of engaging in (unprosecuted) corruption (described in greater detail later). Types are drawn from party-specific distributions with probability density functions g _D(⋅) and g _R(⋅). These have continuous support over the real line, and their shape is common knowledge to the players.

The game unfolds in three steps. First, officials observe their types and choose levels of corruption c _i ≥ 0. Second, if an official does break the law (c _i >0), with probability q the infraction is detected by law enforcement and referred to the prosecutor, and with probability (1−q) it is undetected (or unreferred). Finally, the prosecutor observes the referrals and associated values of c _i, and decides whether to prosecute them.Footnote ¹²

The payoffs to the prosecutor stem from three sources. First, there is an opportunity cost k associated with pursuing a case.Footnote ¹³ Second, there is a career benefit associated with prosecuting high-profile cases (i.e., those with larger c _i). Finally, there is a political benefit to a prosecutor from party p _a associated with prosecuting a public official from party p _i. It is this parameter that captures the notion of partisan bias.

Definition. A prosecutor from party p maintains partisan bias if for p ≠ p′.

In other words, the prosecutor is biased if the political benefit to her of pursuing a case against an official from the opposite party is greater than the benefit of pursuing a case against a co-partisan. To simplify exposition, I will assume throughout that k always exceeds b for all configurations of partisanship; this rules out prosecutions against defendants engaging in de minimis levels of corruption. I will further assume that for p ≠ p′ (note the weak inequality). This implies that a prosecutor can be biased against her political opponents or unbiased, but not biased against her allies. (I return to this assumption in the Discussion section.)

Rather than fully model procedures following a formal indictment, I adopt the following reduced form: if an official is indicted, he will receive an expected sentence (brought about by a plea bargain or the certainty equivalent of the lottery of a full trial) equal to s(c _i), which is continuously differentiable and increasing at an increasing rate for c _i ≥ 0, with s(0)=0 and s′(0)=0.

Let Q _i be an indicator equal to one if a case is referred and zero otherwise, A _i an indicator equal to one if the prosecuting attorney brings a case against official i and zero otherwise, and c an N × 1 vector of corruption levels. Utility functions are given by

To simplify notation, I henceforth assume without loss of generality that the prosecuting attorney is from party R and label the political benefit from prosecuting a party p official b _p.

The subgame perfect Nash equilibria to this game are straightforward, so I defer formal characterization to Lemma 1 in Appendix A. In equilibrium, prosecutors never indict officials against whom no referral is brought. Conditional on observing a referral, the prosecuting attorney will pursue a formal charge against an official if and only the observed level of corruption of an official from party p exceeds a threshold equal to k−b _p. Officials fall into one of three relevant categories (a fourth category, described in Lemma 1, is knife's edge): the first consists of those who experience negative marginal utility from corruption (m _i < 0) and who therefore do not engage in it (c _i* = 0). The second group consists of individuals whose optimal level of corruption given the threat of prosecution falls below the prosecutor's threshold for indictment. These officials will engage in corruption at the threshold level (c _i*=k−b _p), knowing that even if they are detected, they will not be prosecuted. The remaining officials engage in levels of corruption greater than the prosecutor's threshold; those levels are strictly increasing in the official's type, m _i, and decreasing in the probability of referral q.Footnote ¹⁴

Empirical Implications and Identification

In this section, I explore the empirical implications of the model, consider potential threats to inferring partisan bias with observational data on corruption prosecutions, and derive a strategy for overcoming these threats. Formal propositions and proofs appear in Appendix A.

The foregoing suggests that a partisan-biased prosecutor will be willing to file weaker cases against political opponents than allies, which will in turn produce lower sentences. Suppose the underlying distribution of official types for party D, g _D(⋅), is identical to that of party R, g _R(⋅). Partisan bias on the part of a prosecutor from party R should then lead to (1) lower average sentences for defendants from party D than defendants from party R, and (2) a higher proportion of defendants from party D in the set of prosecutions than in the general population.

The assumption that the distribution of benefits to corrupt behavior is the same across the two parties is, of course, unlikely to hold in reality. In the U.S., for example, Democrats tend to be disproportionately concentrated in urban areas, where opportunities for (and rewards to) corruption may be greater. Differences in these distributions threaten to confound efforts to assess bias using cross-sectional data on corruption prosecutions from a given administration.

To make this issue concrete, assume that the party-specific distributions of types are not necessarily equal, but may be ordered by monotone likelihood ratio (MLR) dominance.Footnote ¹⁵ Informally, MLR dominance is a common way of characterizing one distribution as “larger” than another; an example would be two normal distributions with the same variance, one of which has a higher mean than the other.Footnote ¹⁶ First, suppose g _R(⋅) strictly MLR dominates g _D(⋅); this would imply officials from party R tend to enjoy higher returns from corruption than officials from party D and will, ceteris paribus, engage in more corrupt activity as a consequence. Given a prosecutor from party R, the expected sentence for officials from party D could be less than the expected sentence for officials from party R in the presence or absence of partisan bias. Figure 2A displays the intuition graphically: the posited difference in distributions will lead to a lower expected level of corruption—and thus lower sentences—from party D than from party R, even when there is no partisan bias on the part of the prosecutor (b _D = b _R=b). In the presence of partisan bias, it would be impossible to distinguish the effect of the bias from the effect of the difference in the underlying distributions.

FIGURE 2.

Potential Threats to Inferring Bias Stemming from Underlying Interparty Differences in Returns to Corrupt Activity: (A) Confounding Yields Overestimate of Partisan Bias, (B) Confounding Yields Underestimate of Partisan Bias

Note: In the situation depicted in (A), the equilibrium distribution of (prosecuted) corruption for party R dominates that of party D, leading to a lower average sentence for party D even in the absence of prosecutorial partisan bias against party D. In the situation depicted in (B), the equilibrium distribution of corruption for party D dominates that of party R, pushing the average sentence for party D up relative to that of party R; if the average sentence for party D is still lower than that of party R, the source of the disparity must be prosecutorial bias.

Next, suppose that g _D(⋅) weakly MLR dominates g _R(⋅). Given a prosecutor from party R, the expected sentence for officials from party D would be lower than the expected sentence for officials from party R only in the presence of partisan bias. As Figure 2B suggests, dominance of the distribution of party D types pushes the expected sentence for defendants from party D up relative to the expected sentence for defendants from party R. If, in spite of this, we nonetheless observe a significantly lower average sentence for defendants from party D than party R, the source of the difference must be partisan bias.

In terms of estimation, a difference in the underlying party-specific distributions is akin to omitted variables bias (OVB). In the first case, the OVB is away from zero, whereas in the second, the OVB is toward zero. Note that if one is assessing partisan bias of a prosecutor from party D, the potential threats to inference will be reversed: if g _R(⋅) dominates g _D(⋅), the OVB will be toward zero, whereas if g _D(⋅) dominates g _R(⋅), the bias will be away from zero.

Rather than assume, implausibly, that the underlying distributions are equal across parties, my identification strategy instead relies on a comparison of corruption case outcomes under both party D and party R prosecutors, under the less stringent assumption that g _D(⋅) and g _R(⋅) do not change drastically over adjacent administrations.Footnote ¹⁷ First, I consider conditions under which one can infer an ordering of the party-specific distributions from the data, which would in turn allow one to sign the OVB. It turns out that patterns in the data would permit this. In particular, if we assume that g _D(⋅) and g _R(⋅) can be ranked by MLR dominance, then disproportionate targeting of defendants from party D (relative to their proportion in the general population—not the set of referrals) by a prosecutor from party D can occur only if g _D(⋅) strictly MLR dominates g _R(⋅).

The intuition is simple: the presence of a party D prosecutor will push down the proportion of partisan-affiliated defendants from party D if she is biased, and have no effect on that proportion otherwise. If, in spite of this, we observe that proportion exceed its analog in the general population, then the only possible source of the disproportionality is a discrepancy in the distributions. For similar reasons, disproportionate targeting of officials from party R by prosecutors from party R can occur only if g _R(⋅) strictly MLR dominates g _D(⋅).Footnote ¹⁸ In other words, if we observe disproportionate prosecution of co-partisans by a prosecutor, then differences in observed sentences between the parties under that prosecutor will tend to overstate the extent of that prosecutor's partisan bias (OVB away from zero), whereas differences in observed sentences under a prosecutor from the opposite party will tend to understate the extent of that prosecutor's bias (OVB toward zero).

Second, let E[s|p _i, p _a] represent the expected sentence of officials from party p _i under an administration from party p _a. In Appendix A, I demonstrate that the sample analog of the quantity

provides an unconfounded measure of the total extent of partisan bias summed across two adjacent administrations of different parties. Readers may recognize this quantity as a differences-in-differences (DiD). The DiD estimator recovers an unbiased measure of the aggregate effect of partisanship by controlling for (“differencing out”) time-invariant differences between the party-specific type distributions and administration-specific effects (e.g., how much the administration prioritizes public corruption prosecutions generally). Critically, however, the estimator does not permit one to apportion the partisan bias between the two administrations.

Discussion of the Model

Before proceeding to the empirical analysis, I discuss the reasoning behind several important features of the model. First, the model does not distinguish between cases that go to trial and those that result in plea bargains. A simple permutation in which the prosecutor offered the defendant a “take it or leave it” plea bargain to avoid the gamble of a trial and with an exogenously given bargaining breakdown probability would yield results substantively similar to those described previously. Note that in the model, the function s(⋅) represents sentences brought about by plea bargains as well as the expected sentence given the lottery of a full trial; consequently, proper empirical tests for differences in sentencing will include plea bargains, acquittals, dismissals, and guilty verdicts in the calculation of the average observed sentence.

Second, to keep the exposition simple, the model assumes the referral process and the sentence function s(⋅) are not affected by the partisanship of the defendant. With respect to the latter, the fact that federal judges are themselves appointees with political affiliations may call this assumption into question. Later in the article, I discuss my approach for handling this challenge in the empirical analysis. With respect to the former, a plausible case could be made that pressure brought to bear on federal investigators works in the same direction as the partisan bias of the U.S. Attorneys themselves (and, indeed, might be initiated by them). If this is the case, then evidence of partisan bias may be attributed to the Justice Department as a whole, rather than the U.S. Attorneys in isolation.

Third, the model assumes that the referral accurately reflects the level of corruption in which an official engaged. In practice, the referral may contain noise that is (partially or fully) resolved during the discovery period between indictment and a trial. A simple version of the model with uncertainty resolution would have the prosecutor learn the true value of c _i conditional on paying the cost k. Such a model would share many features of the model described previously: most important, the prosecutor's strategy would be characterized by a threshold governing whether to indict given the quality of the initial referral, and that threshold would be lower for opponents given partisan bias.

The chief difference between such a model and the one described previously is that these thresholds would incorporate, in addition to any partisan bias, the prosecutor's prior beliefs about a defendant's type. So, for example, suppose the distribution of types from party D dominated the distribution from party R. The prosecutor would respond to this information by lowering the threshold for indictment for party D below that of party R, even in the absence of partisan bias. At the margin—that is, given a referral that makes the prosecutor exactly indifferent between indicting and not indicting—the equilibrium thresholds would exactly offset the difference in the distributions. As an empirical matter, however, we observe the average sentence; uncovering the marginal sentence is considerably more difficult.Footnote ¹⁹ To the extent that the model with uncertainty resolution better captures reality, the DiD test for aggregate partisan bias across administrations will be more informative than the tests for determining bias within an administration.

Description of Data

To test for systematic partisan bias at the Justice Department, I gathered two samples of state and local corruption prosecutions. The first consists of cases concluded during the Bush administration from 2004 to 2006, during which John Ashcroft and Alberto Gonzales each served as Attorney General. The second consists of cases concluded during the Clinton administration from 1998 to 2000, toward the end of Janet Reno's term as Attorney General. The method employed to compile the data was somewhat involved and is described in detail in Appendix B. These time frames were chosen for two reasons. First, the quality of electronic court records prior to 1998 (particularly in some judicial districts) is dramatically lower than more recent data. Second, using these periods eliminates cases that began under one president and concluded under another. At first glance, such cases may seem particularly attractive, pointing in the direction of a regression discontinuity-type research design. However, my theoretical model offers no coherent predictions for those cases.

For the 2004–2006 sample, I obtained information on the prosecution outcomes of 222 defendants. Before discussing their partisan composition, I note several other interesting features of the data. First, notwithstanding the DOJ's classification of these cases as “official corruption,” 87 of the individuals (39%) are not government officials, but private citizens who may or may not be involved with corrupt officials. These include contractors accused of bribery, party operatives accused of buying votes, and a minister accused of establishing a bogus welfare-to-work program. Second, slightly more than half of the observations (115) are individuals who cannot be readily classified as belonging to one or the other party. In addition to some of the private citizens just mentioned, there are also public officials engaged in routine government operations, such as law enforcement officials (e.g., sheriffs' deputies and probation officers accused of extortion), school superintendents, liquor commission investigators, and water district managers. Officials who can be classified as partisan include mayors and town supervisors, city council members and treasurers, judges, and aides to elected officials. The modal lead charge for defendants is the bribery statute (48 defendants), followed by the Hobbs Act (39), conspiracy to defraud the United States (37), and mail fraud (20). Of the 222 cases, 204 resulted in guilty verdicts: 177 of those from plea bargains and the remainder from jury trials. Approximately two thirds of cases in which the defendant was found guilty (130) resulted in at least some prison time for the defendant. The median length of incarceration given a prison sentence was 21 months. The maximum sentence was 188 months. Of the remaining 18 cases, six were dismissed and 12 concluded with the defendant's acquittal at trial.

There are 223 cases in the 1998–2000 sample. Sixty-six of these were private citizens, and 77 could be readily classified as having a partisan affiliation. Violations of the Hobbs Act constituted the modal lead charge (72 defendants), followed by violations of the bribery statute (56). Of the 210 cases resulting in guilty verdicts, 175 emerged from plea bargains. Seven cases ended with not guilty verdicts, and six with dismissals. Interestingly, a slightly larger proportion of guilty verdicts in the Clinton sample ended in incarceration: 157, or 75%. Of those cases, the median sentence was 24 months, and the maximum 488 months.Footnote ²⁰

Partisan Composition of Defendants

Table 1 displays information on the partisan breakdown of defendants in the two sampling periods. Of the 222 cases for which I have collected data in the 2004–2006 (Bush administration) period, 84 of these individuals could be identified either as Democrats or as affiliated with a Democratic politician (e.g., in a fraudulent transaction). In contrast, only 23 defendants could be classified as either Republican or Republican affiliated. The ratio of 3.65 Democrats to 1 Republican prosecuted echoes the discrepancy observed in the Shields/Cragan study cited previously. The discrepancy becomes even more pronounced if one restricts attention to public officials: over six times as many Democratic public officials are observed in the data as Republican.

TABLE 1.

Partisan Affiliation of Public Corruption Prosecution Defendants, Bush and Clinton Samples

How do these figures differ from the partisan breakdown of defendants prosecuted under Clinton? Of the 223 cases coded, 77 could be identified with one of the two major parties: 49 Democrats and 28 Republicans. The data indicate that Democrats were disproportionately represented in the sample of defendants relative to Republicans in a Democratic administration. Among all defendants, there were 1.75 times as many Democratic-affiliated defendants as Republican-affiliated ones. Restricting attention to public officials, this ratio climbs to 2.6 to 1.

While I lack precise data on the ratio of Democrats to Republicans in the general population, it is not controversial to assume, based on extant surveys during the period, that the ratio was less than 1.8:1.Footnote ²¹ The overrepresentation of Democrats in the set of prosecutions under Clinton, although less pronounced than under Bush, suggests that disproportionality cannot by itself be taken to indicate anti-Democratic bias or “profiling” by the Bush administration in corruption prosecutions.

More important for current purposes, the fact that Democrats appear to be disproportionately prosecuted by the Clinton administration, provides evidence that the benefit to engaging in corruption typically tends to be larger at the state and local levels for Democrats than for Republicans. Employing the criteria discussed previously, this pattern in the data allows me to assess the direction in which the following results might be confounded: in particular, estimates of sentencing disparities are likely to overstate the true extent of partisan bias in the Clinton Justice Department, whereas those estimates are likely to understate the true extent of partisan bias in the Bush Justice Department.

Descriptive Results

Having assessed an important issue of potential confounding, I next turn to the specific prediction that in the presence of prosecutorial partisan bias, the average sentence of prosecuted partisan opponents will tend to be lower than that of prosecuted allies. Results appear in Table 2. Because sentences involving probation are not scalable on the same metric as those involving incarceration, I employ two different measures of total punishment. Columns (1) through (3) consider prison sentences in months, treating defendants who received probationary sentences as equivalent to those who were acquitted. In contrast, columns (4) through (6) incorporate information on the length of probationary sentences, under the uncontroversial assumption that the most severe probationary sentence (60 months) is more lenient than the least severe incarcerative sentence (one month). How the “pain” associated with an extra month of probation compares with that of an extra month of prison is unknown, so I present an intermediate case in which an extra month of prison is assumed to be five times as painful. So, for example, five years (60 months) probation would be coded as 12 units of punishment, and one month of incarceration as 13. Results employing different “exchange rates” between prison and probation are qualitatively similar to those reported here. Columns (1) and (4) in Table 2 display average sentences for different categories of defendants with identifiable partisan affiliations prosecuted under the two administrations, using the two measures of punishment. Interestingly, the data suggest that the average prison sentence for partisan-affiliated public corruption defendants under the Bush DOJ (22 months) was slightly longer than under Clinton (16 months), although this difference is not statistically significant.

TABLE 2.

Descriptive Indicators of Partisan Bias in Sentencing: Administration-specific Differences Between Republican and Democratic Defendants and Differences-in-Differences

Notes: Sentences and differences in columns (1) through (3) denote months of incarceration placing zero value on probation; sentences in columns (4) through (6) are calculated as 0.2 times the number of months of probation in the sentence if the sentence is solely probationary, and 12 plus the number of months of incarceration plus 0.2 times the number of months of probation if the sentence includes imprisonment (see text for additional explanation). One-tailed p values in parentheses.

Next, I turn to tests of administration-specific sentencing differences, reported in columns (2) and (5) of Table 2. The numbers in parentheses are one-tailed p values for corresponding t tests assuming unequal variances. (One-tailed tests are appropriate given the directional nature of the hypotheses tested.) For differences between Republican and Democratic average sentences during the Bush administration, a positive difference is evidence of partisan (pro-Republican) bias, as it is consistent with prosecution of weaker cases against Democrats. Turning to the results for the Bush administration, we find a positive difference pooling across all defendants, consistent with anti-Democratic or pro-Republican bias. However, the pooled results miss statistical significance at conventional levels. Confining attention to the sentences of public employees, however, the difference in means is statistically significant. This difference is substantively large as well: for example, the average imprisonment under Bush for Republican public employees is nearly twice that of the Democratic average.Footnote ²² Confining attention to private citizens with partisan affiliations, differences are quite small and nowhere close to significant. Results employing the alternative punishment measure incorporating probation are broadly similar to those using the imprisonment measure.

For differences between Republican and Democratic average sentences during the Clinton administration, a negative difference is evidence of partisan (pro-Democratic) bias. Pooling over all defendants with identifiable partisan leanings, the data indicate that Democrats received prison sentences approximately six months more severe than Republicans. This difference is statistically significant for both punishment measures reported in Table 2. Confining attention to public employees only, differences are highly significant and of the anticipated sign. Under Clinton, Democratic officials received sentences 10 to 11 months more severe than Republican officials on average.

The data are thus consistent with partisan bias in the prosecution of public officials in both the Clinton and Bush administrations; however, they do not indicate partisan bias in the prosecution of private citizens. Taken together with the results in the previous section concerning confounding, the evidence suggests that observed differences under Bush are attributable to partisan bias and not to underlying differences between defendants from the two parties. The observed differences under Clinton may, however, be wholly or party attributable to such differences.

I report DiD estimates in columns (3) and (6). A positive, significant DiD reflects high total partisan bias summed across the Clinton and Bush administrations. Pooling across all defendants with identifiable partisan affiliations, I detect large, positive effects with both measures of punishment. Confining attention exclusively to public officials prosecuted under public corruption statutes, one observes effects even more pronounced, both in their magnitude and their statistical significance. Across the two administrations, the DiD estimates imply between 30- and 40-month aggregate differences in sentences attributable to partisan bias. As the p values in Table 2 indicate, these effects are very precisely estimated. Last, I detect no significant aggregate partisan effects when confining attention to private citizens.

Conditioning on Covariates

The foregoing analysis assumes that conditional on the partisan affiliation of the defendant, individual cases are exchangeable. In fact, there may be other features of the legal and political environment that affect sentencing. For example, prosecutors may get greater recognition from prosecuting elected officials than private citizens or administrative functionaries. Likewise, prosecutors may obtain scale economies from going forward with cases involving multiple defendants. Finally, judges, who must approve all sentences whether they follow plea bargains or guilty verdicts at trial, are themselves political appointees and may differ in their attitudes toward sentencing.

To account for this potential heterogeneity in cases, I assess the robustness of the descriptive results via three different statistical approaches: least squares regression, exact matching, and genetic matching.Footnote ²³ These approaches permit me to estimate the average treatment effect of being a Republican defendant as compared to a Democratic defendant conditional on the previously mentioned features of the environment. The included covariates are whether the defendant was a private citizen, whether he or she was an elected official, whether the sentence was approved by a judge appointed by a Democratic president, and whether the sentence was part of a case with multiple defendants. Because case priorities may vary by the region of the U.S. Attorney's Office (Eistenstein 1978), I also match on regional indicators: Midwest, Northeast, and South (the excluded category is the West). Heteroscedasticity-consistent standard errors are reported for the regression estimates, and bias-corrected standard errors (Abadie and Imbens 2006) for the matching estimates.

In the first four columns of Table C.1 in Appendix C, I report pre- and postmatching balance statistics as a means of diagnosing the success of the genetic matching procedure. (By definition, exact matching entails perfect balance.) Specifically, I employ standardized mean differences and p values for a t test that the covariate means are equal across defendant partisan affiliation (Imai, King, and Stuart Reference Imai, King and Stuart2008; Sekhon n.d.). Balance is indicated by smaller mean differences and larger p values. The diagnostics suggest that excellent balance is obtained on these covariates in both the Bush and Clinton samples. For example, the lowest p value after matching is .7 in the Bush sample and .37 in the Clinton sample.

Table 3 displays estimates for the average effect of being a Republican defendant compared to a Democrat using regression and matching approaches.Footnote ²⁴ Estimates from all three approaches confirm the descriptive results described previously. Pooling over public officials and private citizens, we continue to observe higher sentences for Republicans than Democrats under Bush and lower sentences for Republicans under Clinton, as well as large and highly significant DiD estimates. The most substantial departures from the descriptive results occur in the exact matching estimates, which boost the estimated treatment effect of being a Republican under Bush to more than 27 months. One is hesitant to make too much of this difference, however, because obtaining exact matches requires discarding more than 40% of the cases in the sample.

TABLE 3.

Regression and Matching Estimates of Administration-specific Differences in Sentences Between Republican and Democratic Defendants and Differences-in-Differences, Excluding Crime-level Covariates

Notes: See notes in Table 2 and text for description of measure incorporating probation. Heteroscedasticity-consistent standard errors reported for regression estimates; Abadie and Imbens (Reference Abadie and Imbens2006) standard errors employed for matching estimates, with standard errors for differences-in-differences matching estimates calculated assuming independence of Bush and Clinton samples.

Note that I do not include controls for observable features of the underlying crime in the list of covariates. This omission is made to avoid posttreatment bias, which can emerge if the analyst controls for variables that are causally dependent on the treatment variable of interest (in this case, the partisanship of the defendant). The theoretical model implies that the distribution of criminal activity itself is, in the presence of bias, affected in equilibrium by the partisanship of the defendant. The sentence is simply a noisy measure of that criminal activity. Other features of crimes aside from the sentence are also dependent on the defendant's partisanship; thus, controlling for them may bias the estimated effect of partisanship.

Nonetheless, it is still useful to see whether matching on these features of the cases changes anything. I therefore reran the analysis from Table 3, including three indicator variables for whether the top charge in the indictment was Racketeering, Fraud, or Bribery (the excluded category is Obstruction of Justice). Balance statistics for the genetic matching appear in the fifth through eighth columns of Table C.1 in Appendix C. Results for regression and matching analysis incorporating crime-level covariates are displayed in Table C.2 in Appendix C, and are quite similar to the estimates that do not include them in the list of covariates. Note that exactly matching on the type of crime drastically reduces the sample size by more than 75%; in fact, in the analysis of sentences of private citizen defendants under Clinton, only four exact matches could be found.

Heterogeneity Across U.S. Attorneys' Offices

The foregoing analysis is premised on the assumption that it is possible to assess the extent of partisan bias in the Justice Department taken in toto. The decision to prosecute a public corruption cases, however, lies largely with the individual U.S. Attorneys and their assistants, who may exercise autonomy in setting office priorities. Accordingly, any heterogeneity in the extent of partisan bias among different U.S. Attorneys may manifest itself in variation across districts in differences in the observed sentences of Republican and Democratic public corruption defendants.

Ideally, one would estimate sentencing differences (and DiDs) for every U.S. Attorney's Office. However, many of the districts have only one or a handful of cases associated with them. An alternative approach is to model heterogeneity in the effects of partisan bias parametrically, in the context of a random coefficient model (see, e.g., Gelman and Hill Reference Gelman and Hill2007, ch. 11), in which district-level differences in Republican and Democratic corruption sentences are assumed to be draws from a normal distribution whose estimated mean and standard deviation reflect, respectively, the typical effect and the extent of heterogeneity.

Table 4 displays estimates from a series of such models. In addition to the estimate of the mean partisan effect, its standard error, and the one-tailed p value, I also report, in columns (4) and (8) the estimated standard deviation of the distribution of partisan differences. Estimates of the mean effect of defendant party and the uncertainty surrounding them are quite similar to the models estimated assuming homogeneous effects across districts. Two features of these estimates are particularly noteworthy, however. First, the magnitude of estimated standard deviation of the effects across districts in the pooled (public and private) sample suggests considerable variation in the differences in sentences for Republican and Democratic defendants. To see which districts departed most significantly from the mean effect, I calculated best linear unbiased predictors for district-level party effects. In the Bush data, the districts of Connecticut, Western North Carolina, and Western Tennessee showed unusually small (but still positive) differences between Republican and Democratic defendants, whereas Eastern California and Northern Illinois featured the largest differences. Interestingly, none of the dismissed U.S. Attorneys served in those districts. In the Clinton data, Southern Florida and Eastern New York displayed unusually small (but still negative) differences, and the difference for Western Oklahoma was the wrong (i.e., positive) sign. Differences for Northern Alabama, Northern Illinois, and Southern Ohio were atypically large in magnitude.

TABLE 4.

Accounting for Interdistrict Heterogeneity: Random Coefficient Model Estimates of Administration-specific Differences in Sentences Between Republican and Democratic Defendants and Differences-in-Differences, Excluding Crime-level Covariates

Notes: See notes in Table 2 and text for description of measure incorporating probation. Standard errors for differences-in-differences estimates calculated assuming independence of Bush and Clinton samples.

Second, restricting attention to public employee defendants only, the variance of effects across districts remains large for the Bush administration, but is quite small for the Clinton administration. In fact, a likelihood ratio test comparing the random coefficient model to simple linear regression for the Clinton/public employee sample is right at the threshold of rejecting the latter (χ² = 4.48, p = .11). The apparently greater homogeneity in effects across districts under Clinton relative to Bush is intriguing, and suggests an avenue for future research on the extent of administrative centralization under each.

Although limitations in the data preclude estimating separate sentencing differences for most districts, an important exception to this rule is the Northern District of Illinois, which handles corruption cases from Chicago and its surrounding suburbs. I have data from this district on Democratic and Republican defendants under both the Bush and Clinton administrations. Northern Illinois is also a “hard case” for demonstrating partisan bias because of the reputation of Bush-appointed U.S. Attorney Patrick Fitzgerald for nonpartisanship. The U.S. Attorney for Northern Illinois from 1998 to 2000 was Clinton appointee Scott Lassar.

Table 5 displays the results of regression and matching analyses employing cases only from the Northern District of Illinois. Because of the small sample size, I report only results pooling across both public and private defendants. (Balance statistics for the genetic matching appear in Table C.1 in Appendix C. The procedure failed to produce good balance on the party of the president who appointed the presiding judge in a case.) The results for the single district mirror those for the national sample. We observe Republican defendants receiving substantially and statistically significantly higher sentences under Fitzgerald, and Democrats receiving higher sentences under Lassar. One challenge associated with focusing attention on this particular district is the fact that Democratic-affiliated defendants tend to work in Chicago government, whereas Republican-affiliated defendants tend to work for the state or come from smaller towns such as Cicero. Of course, these differences tend to persist across administrations, affording validity to the DiD estimates as evidence of partisan bias aggregated across the two administrations.

TABLE 5.

Regression and Matching Estimates of Administration-specific Differences in Sentences Between Republican and Democratic Defendants and Differences-in-Differences, Northern District of Illinois Only

Notes: See notes in Table 2 and text for description of measure incorporating probation. Heteroscedasticity-consistent standard errors reported for regression estimates; Abadie and Imbens (Reference Abadie and Imbens2006) standard errors employed for matching estimates, with standard errors for differences-in-differences matching estimates calculated assuming independence of Bush and Clinton samples.