Mandatory Sentencing and Racial Disparity: Assessing the Role of Prosecutors and the Effects of Booker

abstract. This Article presents new empirical evidence concerning the effects of United States v. Booker, which loosened the formerly mandatory U.S. Sentencing Guidelines, on racial disparities in federal criminal cases. Two serious limitations pervade existing empirical literature on sentencing disparities. First, studies focus on sentencing in isolation, controlling for the “presumptive sentence” or similar measures that themselves result from discretionary charging, plea-bargaining, and fact-finding processes. Any disparities in these earlier processes are excluded from the resulting sentence-disparity estimates. Our research has shown that this exclusion matters: pre-sentencing decision-making can have substantial sentence-disparity consequences. Second, existing studies have used loose causal inference methods that fail to disentangle the effects of sentencing-law changes, such as Booker, from surrounding events and trends.

In contrast, we use a dataset that traces cases from arrest to sentencing, allowing us to assess Booker’s effects on disparities in charging, plea-bargaining, and fact-finding, as well as sentencing. We disentangle background trends by using a rigorous regression discontinuity-style design. Contrary to other studies (and in particular, the dramatic recent claims of the U.S. Sentencing Commission), we find no evidence that racial disparity has increased since Booker, much less because of Booker. Unexplained racial disparity remains persistent, but does not appear to have increased following the expansion of judicial discretion.

authors. Sonja B. Starr is a Professor at the University of Michigan Law School. M. Marit Rehavi is an Assistant Professor of Economics at the University of British Columbia and a Fellow of the Canadian Institute for Advanced Research. For helpful comments and conversations, we thank David Abrams, Daron Acemoglu, Alberto Alesina, Joe Altonji, Alan Auerbach, Nick Bagley, John Bronsteen, Ing-Haw Cheng, Kristina Daugirdas, John DiNardo, Avlana Eisenberg, Leonid Feller, Nicole Fortin, Nancy Gallini, Nancy Gertner, David Green, Sam Gross, Don Herzog, Jim Hines, Jill Horwitz, Thomas Lemieux, Justin McCrary, Julian Mortenson, Brendan Nyhan, J.J. Prescott, Eve Brensike Primus, Adam Pritchard, Jeff Smith, Sara Sun Beale, and participants at the Ninth Circuit Judicial Conference, the National Sentencing Policy Institute, the NBER Summer Institute, the annual meetings of the American Law and Economics Association and the American Society of Criminology, workshops at the University of Michigan, UBC, Duke, and Loyola-Chicago, and the CIFAR-IOG Workshop. Sharon Brett, Michael Chi, Michael Farrell, Ryan Gersovitz, Seth Kingery, Matthew Lee, Midas Panikkar, Art Robiso, Sabrina Speianu, and Adam Teitelbaum provided able research assistance.

Introduction

In the United States, one of every nine black men between the ages of twenty and thirty-four is behind bars,1 and, in 2003, the Bureau of Justice Statistics projected that one in every three young black men could expect to be incarcerated at some point in his life.2 These rates far exceed those of any other demographic group—for instance, black males are incarcerated at nearly seven times the rate of white males.3 The impact of demographically concentrated incarceration rates on offenders, families, and communities is a critical social concern.4 But why do these gaps exist? Can they be explained by differences in criminal behavior, or by differences in how the criminal justice system treats offenders? If it is the latter, can the process be improved by reforms, such as changes to sentencing law?

These questions are not new. For decades, racial and other “legally unwarranted” disparities in sentencing have been the subject of considerable empirical research, which has in turn helped to shape major policy changes. Most importantly, the U.S. Sentencing Guidelines and their state counterparts were adopted with the goal of reducing such disparities. In 2005, when the Supreme Court’s decision in United States v. Booker rendered the formerly mandatory Guidelines merely advisory, Justice Stevens’s dissent predicted that “[t]he result is certain to be a return to the same type of sentencing disparities Congress sought to eliminate in 1984.”5 Whether this prediction was accurate is perhaps the foremost empirical question in sentencing policy today. The most prominent study to date, a 2010 report of the U.S. Sentencing Commission, gave an alarming answer: Booker and its judicial progeny had quadrupled the black-white sentencing gap among otherwise-similar cases, from 5.5% to 23.3%.6 In January 2013, the Commission issued an update with similar figures (revising the latter figure slightly downward, to 19.5%), this time combined with explicit calls for legislation in effect returning the Guidelines to something fairly close to their prior binding status.7

This Article introduces a new empirical approach and gives a very different answer. The Commission’s methods are hobbled by two serious limitations that also pervade the broader empirical literature on sentencing disparity.8 First, these studies consider the judge’s final sentencing decision in isolation, ignoring crucial earlier stages of the justice process. Those earlier stages have important sentencing consequences, and yet these studies exclude the portions of the ultimate sentence gap that result from earlier-stage decision-making from their estimates. Second, studies of changes in disparity after legal changes (like Booker) have failed to disentangle the effects of the legal change from surrounding events and background trends.

This Article develops these two critiques and discusses our own research on racial disparities among federal arrestees, which uses a method that avoids these problems. We first highlight some findings from our recent study showing that while a black-white gap appears to be introduced during the criminal justice process, it appears to stem largely from prosecutors’ charging choices, especially decisions to charge defendants with “mandatory minimum” offenses. These findings highlight the importance of taking into account the early parts of the justice process. With that in mind, we then present our new findings on Booker, estimating its effects not only on sentencing, but also on charging, plea-bargaining, and sentencing fact-finding, an analysis no prior studies have performed. Far from finding evidence that judges’ use of expanded discretion worsens disparity, we fail to find an increase in disparity and find suggestive evidence cutting in the opposite direction.9

Our research seeks to close a surprisingly wide gap that separates two bodies of scholarship: the theoretical and qualitative literature on how the criminal justice system functions (which uniformly recognizes the critical role of prosecutors) and empirical research on sentencing disparities (which effectively ignores that role). The modern criminal justice process is prosecutor-dominated. Prosecutors have broad charging and plea-bargaining discretion, and their choices have a huge impact on sentences. A central claim made by critics of mandatory sentencing is that restricting judicial discretion further empowers prosecutors, who tend to exercise that power in ways that perpetuate or worsen disparity. This “hydraulic discretion” theory has been described as a near-consensus view of sentencing scholars.10

Yet the empirical research on sentencing disparity has not tested these claims and fails to account for the role of prosecutorial discretion. Researchers typically estimate sentencing disparities in federal and other courts subject to sentencing guidelines after controlling for (among other things) the recommended guidelines sentence. But the guidelines recommendation is itself the end product of charging, plea-bargaining, and sentencing fact-finding. Controlling for it filters disparities in those processes out of the sentencing-disparity estimates and gives an incomplete view of the scope and sources of sentencing disparity.11 In effect, the existing literature focuses on disparities in compliance with the sentencing guidelines. While this is an important piece of the sentence-disparity picture, it is far from the only piece, because decisions made throughout the process ultimately affect the sentence. Moreover, sentencing-stage disparities might either offset or exacerbate disparities arising earlier, making it hard to interpret them in isolation.

We accordingly take a broader, process-wide approach, constructing a dataset that links records from four different federal agencies and allows us to trace criminal cases from arrest through sentencing. We focus on the gap between black men and white men in non-immigration cases. Instead of controlling for the Guidelines sentence, we control for the arrest offense and other characteristics that are fixed at the beginning of the justice process. The arrest offense is an imperfect proxy for underlying criminal behavior, but we believe it is the best proxy available for this purpose. Our method allows us to assess aggregate disparities introduced throughout the post-arrest justice process, from charging through sentencing. Further, it also allows us to analyze the contribution of each procedural stage (as well as underlying case differences) to the total black-white gap.

The problem with the prevailing method is not merely an academic concern. In Part II of this Article, we highlight and discuss key findings of our analyses of charging and sentencing in federal criminal cases from 2007 to 2009.12 That research shows that after controlling for the arrest offense, criminal history, and other prior characteristics, there remains a black-white sentence-length gap of about 10%. But judges’ choices do not appear to be principally responsible. Instead, between half and the entire gap can be explained by the prosecutor’s initial charging decision—specifically, the decision to bring a charge carrying a “mandatory minimum.” After controlling for pre-charge case characteristics, prosecutors in our sample were nearly twice as likely to bring such a charge against black defendants.13 In other words, studies that focus only on the judicial sentencing decision exclude what appears to be the most important procedural source of disparity in sentences.

A proper analysis of Booker’s effects on disparity, then, should take the whole justice process into account, to the extent possible. In Part III, we present the results of such an analysis. We begin that inquiry with a simple linear time-trend analysis, which shows that, when one measures sentence disparity in the broader way that we recommend, unexplained black-white disparity did not grow between 2003 and 2009, the period in which the Sentencing Commission found that it quadrupled. Indeed, our estimate of the disparity trend is negative, although imprecise. That is, the gap in sentences for similar black and white arrestees was, if anything, slightly smaller by the end of 2009 than it was just before Booker. The Commission’s claim that disparity grew over that same period is an artifact of its flawed way of measuring disparity.

Beyond the question of whether disparity has changed during the period surrounding Booker, we must further ask whether it has changed because of Booker.The two questions are not the same, but they are too often confused. In addition to the disparity-measurement question, a second serious flaw pervades the empirical literature on sentencing-law changes: the failure to provide a sound basis for causal inferences. This second problem is exemplified by the Sentencing Commission’s analysis. The Commission found that disparities after Booker (averaged over a period of years) were larger than disparities before it. Even assuming that were true, it would still be a huge logical leap to conclude that Booker caused this increase—a classic confusion of correlation and causation. Many things change over time—for instance, the mix of cases, the composition of the bench and of U.S. Attorneys’ and public defenders’ offices, substantive criminal legislation and case law, and the Department of Justice’s (DOJ’s) enforcement priorities and internal policies—and any of these changes could have racially disparate impacts on sentences. The greater disparity in the post-Booker period, therefore, could easily have nothing to do with Booker. Indeed, even if Booker had slowed an underlying trend of increasing disparity, the Commission’s methods would incorrectly imply that Booker led to greater disparity.

Accordingly, we employ a different approach that can disentangle the effect of Booker from underlying trends: a regression discontinuity-style estimator. Specifically, we assess whether, in the immediate aftermath of Booker, there is a sharp break in an otherwise continuous trend, which would provide a much stronger basis for inferring causality. Our method focuses on Booker’s immediate effects, not its long-term effects, which admittedly is both a strength and a weakness. The long-term effects are presumably what policymakers care most about, but there is no good way to identify Booker’s relationship to longer-term trends in disparity—the causal inference problem is too serious. The immediate effects can be more rigorously assessed. Fortunately, there is good reason to believe that if Booker had substantially changed racial disparity patterns in judicial decision-making, we would have seen at least part of the effect right away. Booker’s effects on Guidelines compliance were not slow or subtle—departure rates immediately and dramatically spiked. That is, Booker was a sudden shock to the scope of judicial discretion, and, if judges were inclined to exercise their discretion in ways that widen the black-white gap, one would expect to see disparity jump in response to that shock, right after Booker.

We do not see such a jump. Right after Booker, sentencing disparity did not increase, and may have modestly dropped. If Booker did have any adverse effects on black defendants relative to white defendants, it was probably a second-order result of charging changes: the use of mandatory minimum charges increased for black defendants immediately after Booker, but this effect appears to have been quite short-term.

We are very cautious about these findings. Even with our approach, identifying Booker’s effects is hard. While Booker has been described as a “natural experiment,”14 as an experiment it leaves much to be desired—it changed the legal regime for every non-petty federal offense at once, leaving no plausible control group. Our method does not require a control group and filters out longer-term trends effectively, but it could be tricked by month-to-month fluctuations. Moreover, Booker was not a clean break in settled law; it came on the heels of a period of serious lower-court confusion, further complicating causal inference. We conduct tests to evaluate these problems, but we cannot erase the noise in the data or the complexity of the history. Still, what we can say is that nothing in these data suggests that judges’ use of their post-Booker discretion exacerbated racial disparity.

Understanding the relative role of prosecutors and judges in producing disparities is important. The specter of increased disparity after Booker has been prominently cited to support new constraints on judicial discretion. For instance, the Department of Justice in the George W. Bush Administration advocated mandatory topless guidelines—effectively, mandatory minimums but no maximums.15 The Sentencing Commission has recently advanced a multi-pronged proposal to strengthen legislative and appellate court constraints on judicial sentencing discretion—a proposal that in effect would restore the Guidelines very nearly to the legal status they enjoyed before Booker.16

Such “solutions” could be counterproductive. Constraints on judges generally empower prosecutors by making their choices more conclusive determinants of the sentence. Our research suggests that prosecutorial decisions are important sources of disparity—especially the decision to file mandatory minimum charges, which are prosecutors’ most powerful tools for constraining judges. Note that we do not claim our findings prove “discrimination” by prosecutors or anyone else. We are limited to what our data can capture, and unobserved differences between cases could justify different charging decisions or sentencing outcomes. Still, we have rich controls, including detailed arrest offense information; criminal history; and other demographic, geographic, and socioeconomic fields, yet substantial unexplained racial differences remain.

In Part I, we briefly introduce the federal sentencing framework and review the legal scholarship on prosecutorial and judicial discretion. In Part II, we present our critique of the “sentencing only” approach used by the current empirical literature and discuss our preferred process-wide approach, its strengths and limitations, and some insights that can be gleaned from it. In Part III, we present our critique of the causal inference methods used by existing sentencing-reform research. We then pair our process-wide approach to estimating disparity with our regression discontinuity-style approach to causal inference in order to estimate Booker’s effectson racial disparity. We conclude with possible policy implications.

I. prosecutors, sentencing, and the “hydraulic discretion” theory

Federal prosecutors, like their counterparts in the states, have always possessed very broad discretion. Prosecutors choose what charges to bring, and the complex criminal code often provides a wide range of choices. Over 95% of convictions result from guilty pleas, and prosecutors control the terms of the deals they offer defendants.17 These can include the charges of conviction (charge bargaining), sentence recommendations and requests for departures from the usual range, and stipulations about sentencing-relevant facts (fact bargaining).

Traditionally, prosecutors’ discretion was matched by vast judicial discretion in choosing sentences, which was constrained only by broad statutory ranges—for instance, zero to twenty years. Statutory minimumsentences were not widespread before the 1980s, and still apply in only a minority of cases.18 Within the statutory ranges, judges were free to tailor sentences to the facts and the offenders’ circumstances. The disadvantage was that there was no good way to ensure that similar cases resulted in similar sentences.

In 1984, citing studies finding widespread racial, gender, inter-judge, and inter-district disparities in sentencing, Congress adopted the Sentencing Reform Act, which created a Sentencing Commission to devise binding Sentencing Guidelines.19 Under the Guidelines, complex rules determine the offense level, which is based on the conviction offense plus additional aggravating or mitigating sentencing facts, such as drug quantity or the defendant’s role in a group offense. The offense level is one of two axes of a sentencing grid; the other is the defendant’s criminal history category. Within each grid cell is a narrow range: eight to fourteen months, for instance.20 Prior to Booker, departures from this range were permitted only for specified reasons.

By greatly reducing judges’ discretion, the Guidelines concentrated tremendous power in prosecutors’ hands. As Kate Stith explains, “when judges had discretion to impose any sentence [in the statutory range], prosecutorial power was potentially limited or counterbalanced by the possibility of judicial discretion.”21 But under the Guidelines, plea-bargaining much more tightly constrained the sentence.22 The one feature of the Guidelines that was intended to limit prosecutorial power was the judge’s sentencing fact-finding authority. This system (called “real-offense” sentencing)23 allows the judge to base a sentence even on uncharged conduct, so long as the sentence falls within the statutoryrange for the crime of conviction. In principle, this system should reduce prosecutors’ ability to offer to understate the defendant’s culpability in exchange for a guilty plea.

Still, studies suggest that real-offense sentencing has not constrained prosecutors very much, because in practice prosecutors very strongly influence judges’ findings of fact. Plea agreements usually include factual stipulations, and, even though DOJ has long directed prosecutors not to bargain over these facts, many studies have documented the persistence of fact-bargaining.24 Judges are not bound by the factual stipulations, and the power to diverge from them (relying on sentencing-stage evidence or a probation office report) is an important aspect of judicial discretion. Judges typically lack the incentive, however, and may lack the information, to diverge from what the parties have agreed upon.25 One 1996 survey found that only 8% of judges said they “go behind” plea agreements “somewhat or very frequently”; 25% said they never do, while the rest said they did so “infrequently.”26 As Nancy King put it, “Establishing facts in an adversarial system without the assistance of adversaries is an awkward business.”27

To the Guidelines’ many critics, this empowerment of prosecutors was a serious flaw, leading to harsh results for defendants generally and undermining the Sentencing Reform Act’s disparity-reduction goals. As Albert Alschuler argued, “[T]he price of whatever success the Guidelines have achieved in reducing judge-created sentencing disparities has been the burgeoning of prosecutor-created disparities.”28 Scholars often refer to discretion in the criminal justice system as being “hydraulic,” such that attempts to constrain it in one place will merely shift it to another. Stephanos Bibas, for example, wrote, “The criminal justice system operates like a toothpaste tube, and departures that are squeezed out of the judge’s end of the tube will wind up in the prosecutor’s domain. This hydraulic pressure means that departures will still exist, but they will now occur more often on prosecutors’ terms.”29This theory has long pervaded scholarship about the Guidelines. As Terance Miethe wrote in 1987, “[T]his ‘hydraulic’ or ‘zero-sum’ effect is so firmly entrenched as a criticism of current reform efforts that most researchers begin with the assumption that the displacement of discretion exists . . . .”30

Note that, although scholars’ language often refers to shifts in “discretion,” this is a slight misnomer; the Guidelines did not really increase prosecutors’ discretion, which was already almost boundless. Rather, they increased their power: the choices prosecutors made more conclusively determined the sentence.31 In a 1996 survey, approximately 75% of district judges and chief probation officers said that prosecutors were now the actors with the most influence on final sentences—more than judges themselves.32 Prosecutors thereby obtained greater leverage in plea-bargaining—they could nearly promise that defendants would get more lenient sentences if they pled guilty and harsher ones if they refused. In 2004, Marc Miller wrote, “The overwhelming and dominant fact of the federal sentencing system . . . is the virtually absolute power the system has given prosecutors . . . . There is a lot of evidence to support this claim, but it can be demonstrated with one simple and awesome fact: Everyone pleads guilty.”33 After the implementation of the Guidelines in the early 1990s, plea rates rose from 87% of all federal convictions to 97% by 2004.34

Since then, however, federal sentencing law has undergone another major change. In January 2005, the Supreme Court decided United States v. Booker, which rendered the formerly mandatory Guidelines merely advisory.35 The Court held that a mandatory sentencing scheme in which a defendant’s maximum sentence could be increased based on judicial fact-finding violated the Sixth Amendment right to a jury trial.36 The Court could have remedied that defect by requiring more jury fact-finding, but it chose an alternate remedy: maintaining real-offense sentencing, but severing the provision of the Sentencing Reform Act that rendered the Guidelines mandatory.37 The Court’s remedial choice remains reversible by Congress,38 which has so far not taken action to reverse Booker. District courts today may depart from the Guidelines so long as the ultimate sentence is not “unreasonable.”39 In December 2007, in Gall v. United States and Kimbrough v. United States,the Supreme Court further clarified that courts of appeals should not deem sentences unreasonable merely because they fall outside the Guidelines,40 and that sentencing judges may depart from the Guidelines on the basis of policy disagreements.41

Booker was widely seen as an earthquake in federal sentencing law. Still, rendering the Guidelines advisory is not the same as eliminating them. Federal judges are still required to calculate the Guidelines sentencing range, and, although they are then free to depart from it, they usually do not.42 There are many possible reasons for this continued conformity: federal judges might believe that the Guidelines meet the goal of reducing disparity,43 wish to avoid open-ended, subjective sentencing assessments, seek insulation from criticism or reversal, or simply treat the Guidelines as an “anchor.”44

To the extent that judges continue to follow the Guidelines, the power the Guidelines conferred on prosecutors will presumably remain largely intact. In addition, even if judges felt totally unconstrained by the Guidelines, prosecutors would retain at least two powerful sources of sentencing influence. First, their charging and charge-bargaining choices shape the statutory minimum and maximum sentences, which remain mandatory. Second, because they negotiate the factual stipulations accompanying pleas and may introduce evidence at sentencing hearings, prosecutors have enormous influence over the information that gets to judges, and what judges know presumably will influence sentencing regardless of whether they follow the Guidelines. Thus, even in the post-Booker era, prosecutors should be expected to play a crucial role in the processes that shape sentencing.

In short, then, legal scholars and justice system participants widely agree both that prosecutorial choices are key drivers of sentences and that sentencing law reforms involve tradeoffs between judicial and prosecutorial power. One might expect that this broad consensus would shape empirical research on sentencing disparities and sentencing reforms, but, as we demonstrate below, it has not.

II. estimating racial disparity in sentencing: a process-wide approach

For decades, unwarranted disparities in sentencing have been a major focus of empirical research. Overwhelmingly, these studies focus exclusively on judges’ final sentencing decisions, ignoring the rest of the justice process. In Section II.A, we review those studies and explain why this problem is so serious. In Section II.B, we describe the dataset that we constructed to enable a broader approach, and in Section II.C, we highlight certain key findings of our recent study of racial disparity in charging and sentencing. In Section II.D, we discuss some limitations of this broader approach. Note that this Part does not focus directly on Booker’s effects or on changes over time. Rather, we begin by explaining why it is crucial for estimates of sentencing disparity to encompass the pre-sentencing stages of the process: a great deal of the ultimate sentence gap between similar black and white arrestees appears to emerge from decisions made at earlier stages. That insight provides one of the primary motivations for our approach in our analysis of Booker, presented in Part III.

A. Studies Estimating the Extent of Unwarranted Sentencing Disparities

Sentencing disparity studies generally begin by pointing to a gap in observed sentence outcomes and asking what generated it. For instance, black male defendants receive much longer sentences on average than white males do—a major contributor to their higher incarceration rates. But does the sentence gap arise because black defendants have committed more serious crimes or have more extensive criminal histories? Or are they treated differently in the criminal justice process?

Mass incarceration of black males has serious social consequences regardless of its causes. But if different offending patterns are to blame, the problem might be better addressed with policies focused on addressing the causes of crime, such as poverty. In contrast, if the criminal justice system is treating like cases differently, then policymakers should focus on fixing that problem. Researchers thus seek to isolate the component of the sentence gap arising in the criminal justice process by controlling for some measure of the underlying severity of the case. But what measure? The answer to that question is the key difference between our approach and those of prior sentencing studies.

When researchers focus on the federal courts or other guidelines-based systems, the typical approach is to control for the “presumptive” or recommended guidelines sentence—generally, the bottom end of the guidelines range.45 There are variations on this approach,46 but all of them estimate differences in the actual sentence relative to what the sentence “should have been” under the guidelines. Most studies also include controls for the statutory mandatory minimum.47 Studies in systems without guidelines similarly control for conviction severity.48

The problem with these approaches is that the key control variables are only distant proxies for the seriousness of the underlying conduct. They are the end product of the discretionary processes described above: charging, plea-bargaining, and sentencing fact-finding. And those processes might also produce disparities. The use of these control variables filters out the share of the ultimate sentencing disparity that comes from those earlier processes. The resulting measure of disparity is thus based on an artificially narrow focus on the final sentencing decision in isolation from all the other processes that produce the sentence. These estimates can be useful in understanding disparities in guidelines compliance, which is one important part of the criminal process. However, we believe that, for most purposes, policymakers likely have a broader interest in the full sentence disparity that an individual faces, regardless of where it originally arose in the justice process. If so, it is important for them to understand that the existing literature is estimating something much narrower.

The specification of an empirical model of disparity may seem like a purely scientific decision. But as Albert Alschuler has observed, it is bound up with normative questions: what kinds of disparities do we think are important?49 The choice of control variables determines what kinds of disparities one is measuring, and so it should be shaped by a sense of the types of disparities policymakers and stakeholders care about. There are many reasons one might worry about demographic disparities in the justice process. For instance, such disparities might violate the Equal Protection Clause, exacerbate the social consequences of mass incarceration within particular communities, interfere with retributive or utilitarian punishment objectives, or undermine the justice system’s credibility.

We do not intend in this Article to resolve what policymakers’ objectives should be. But none of the reasons we can think of for caring about demographic disparities suggest that policymakers should confine their interest to equalizing sentences for cases in the same Guidelines cell. Rather, all imply that the key question is whether people who have committed the same underlying criminal conduct (arguably including prior criminal history) receive the same sentence. Between the underlying criminal conduct and the sentence, there are many points in the process where disparities could be introduced. Policymakers should care about all of them.

Other scholars have noted this problem with the prevailing approach.50 This includes, to their credit, many of those who employ the approach themselves, who note that their accounts of disparities are incomplete.51 But these caveats generally are not mentioned when the work gets cited, and their importance may well be overlooked by policymakers. This is a serious mistake. The problem is not just that these accounts of disparity are insufficiently comprehensive—they are also potentially misleading, at least if one misinterprets them as a measure of whether judges are treating defendants with similar conduct equally. Absent an account of disparity at the earlier stages of the process, it is difficult to interpret disparities found in the final stage.

For instance, consider the Sentencing Commission’s prominent recent sentencing-disparity report. The report finds that from December 2007 to September 2011, black males received 19.5% longer sentences than white males, controlling among other things for the recommended Guidelines sentence.52 But how should this result be interpreted? Consider just three of many possibilities concerning what might have happened earlier in the justice process:

A.     Prosecutors charged white defendants more harshly and/or offered them worse plea deals, such that the resulting Guidelines recommendation averaged 19.5% higher for white defendants than for black defendants with similar offenses and criminal histories.

B.     Prosecutors charged white defendants more harshly and/or offered them worse plea deals, such that the resulting Guidelines recommendation averaged 30% higher for white defendants than for black defendants with similar offenses and criminal histories.

C.     Prosecutors charged black defendants more harshly and/or offered them worse plea deals, such that the resulting Guidelines recommendation averaged 30% higher for black defendants than for white defendants with similar offenses and criminal histories.

Under Scenario A, what looked like a 19.5% sentencing disparity now looks like judges sentencing more or less “correctly,” relative to underlying criminal conduct—they are correcting the disparity introduced by prosecutors. Under Scenario B, it actually seems that judges are not favoring white defendants enough—to sentence based on true culpability, they would have to do more to compensate for prosecutors favoring black defendants. In contrast, under Scenario C, judges are compounding the underlying charging and plea-bargaining disparities; the “true” sentencing disparity is actually much more than 19.5%. If you don’t know which of these scenarios (or others) is true, it is risky to use the 19.5% figure as a guide to policy.

Moreover, even if one were willing to assume that judges were the only relevant source of racial disparity in sentencing, the prevailing method would nonetheless be too limited, because it still filters out part of the judicial sentencing process. Controlling for the presumptive sentence means one is filtering out any disparities in judicial fact-finding. And in the Sentencing Commission studies specifically, the problem is even worse. In addition to the presumptive sentence and mandatory minimum, the Commission also controls for whether the judge departed upward or downward from the Guidelines range. In doing so, the Commission is not just considering the final sentencing decision in isolation—it is filtering out a key part of that sentencing decision itself. In effect, the Commission is estimating race gaps in the size of departures (and in sentence choices within the narrow Guidelines range), but filtering out whether there is a departure and, if so, in what direction. This is, to say the least, a strange choice, and one that could easily produce misleading results. This same problem also appears in the most prominent recent study responding to the Sentencing Commission report, that of Ulmer, Light, and Kramer; the authors critique other aspects of the Commission’s methods, but their main analysis of sentencing disparities also controls for departure status as well as the presumptive sentence.53

Another recent study by Joshua Fischman and Max Schanzenbach recognizes the problem with the presumptive sentence approach (and also does not control for departure status).54 Fischman and Schanzenbach instead control for the Guidelines “base offense level.” This is an improvement over the presumptive sentence approach; it provides a fuller measure of judicial sentencing disparity, and is probably the best approach possible using only the sentencing-stage data from the Sentencing Commission. But it still means that the authors’ sentence disparity estimates do not incorporate components introduced by the various prosecutorial decisions and negotiations, plus judicial fact-finding, that determine the base offense level.55 The base offense level is affected not only by charging and charge-bargaining, but also by a large part of the fact-finding required by the Guidelines. It incorporates, for instance, drug quantity in a drug trafficking case,56 or, in an assault case, the degree of physical contact and injury, the defendant’s intent, and the use of weapons.57 Sentence disparities arising from any of those factual determinations, or in the prior charging or plea-bargaining processes, would be filtered out by the use of the base offense level control. To fully avoid the limitations of the presumptive sentence approach, one needs a measure of case severity that precedes all of these discretionary processes.58

The problem with the presumptive sentence control is compounded by a distinct source of potential bias that the existing literature has overwhelmingly failed to acknowledge: sample selection shaping the pool of sentenced cases. Nearly every study of sentencing disparity is confined to a sample consisting of sentenced defendants only—in federal court studies, typically only those sentenced for felonies or Class A misdemeanors (“non-petty offenses”), which the Sentencing Commission collects data on. To make it into the sample, defendants must get through the criminal justice “funnel”: they must be arrested, charged, and convicted of a non-petty offense.

If these earlier processes are subject to demographic disparities, it could introduce sample selection bias into the estimates of sentencing-stage disparity. Suppose that all else equal, black defendants are more likely to be convicted of a non-petty offense, such that it takes a less serious case to get a black defendant sentenced. If so, we would expect black defendants and white defendants who get sentenced to be unobservably different: black defendants’ cases would be less serious in a way that controlling for observable variables cannot capture. Sentencing disparity estimates within that sample would be biased because they cannot account for this unobserved difference. Again, without assessing the “funnel,” one cannot know whether to expect such a bias to exist and, if it does, which direction it will cut.

Unfortunately, the empirical research on demographic disparities earlier in the justice process is relatively limited. It focuses almost entirely on certain measures of charge-bargaining, such as the rate of dropping charges; studies typically do not assess severity reductions.59 More importantly, few studies (and no federal studies) have assessed disparities in initial charging, even though it is difficult to interpret charge-bargaining results without doing so.60 A few state-level studies have found racial disparities in the use of certain particularly harsh mandatory minimums, including one study of “habitual offender” charges in Florida,61 another in Pennsylvania,62 and a Maryland study of add-on mandatory minimums for firearms.63

At the federal level, many observers, including the U.S. Sentencing Commission, have pointed to racial gaps in the rate of mandatory minimum convictions.64 Fischman and Schanzenbach’s study provides useful new evidence that mandatory minimums may be an important contributor to sentencing disparities.65 But these studies raise important further questions. Because they do not control for underlying pre-charge case features affecting a defendant’s eligibility for mandatory minimums (such as the arrest offense), they do not examine the reasons for the mandatory minimum gap. They do not tell us whether black defendants have simply committed more crimes to which mandatory minimums apply, or whether there are racial disparities in prosecutors’ exercise of charging or charge-bargaining discretion.66

A final disadvantage to the “presumptive sentence” approach is simpler: it controls only for differences in crime severity according to the Guidelines, not for differences in crime type. Judges might be more likely to depart from the Guidelines for some crimes than others, for reasons that have nothing to do with race. Such tendencies might well have racially disparate impacts, but they are not necessarily “unwarranted”—the nature of the offense is certainly a relevant sentencing consideration. Sentencing studies often do include controls for case type in addition to the presumptive sentence, but only for broad categories such as drugs or violent crime, which do not capture much nuance.67

More precise crime-type controls, which we provide, can enable us to better distinguish the disparate impact component of racial disparity (the component that can be explained by non-racial factors like case type) from the component that we cannot explain with the variables we can measure, which could represent disparate treatment on the basis of race. The distinction between disparate impact and disparate treatment is crucial as a matter of constitutional law,68 although the extent to which it is normatively important is open to debate.69 We think all factors contributing to racial disparity in sentencing—whether legally warranted or not—are important for policymakers to understand, a point we return to below. But we believe that disentangling the reasons can help policymakers figure out what to do about them. In any event, studies like the Sentencing Commission’s purport to estimate legally unwarranted disparities, and thus they should filter out legally relevant factors like case type.

B. Our Dataset

Our broader approach to the estimation of racial disparities requires something most researchers have not had: a dataset that traces federal cases from arrest through sentencing. We constructed it by linking files from four federal agencies: the U.S. Marshals Service (USMS) (data from arrest and/or booking), the Executive Office for U.S. Attorneys (EOUSA) (prosecutors’ investigation and case files), the Administrative Office of the U.S. Courts (AOUSC) (court records), and the U.S. Sentencing Commission (USSC) (sentencing-related data collected from judges).70 It covers two stages of the process that the Sentencing Commission data alone (the sole source for most federal studies) do not include.

First, our dataset includes the arrest offense, coded with 430 codes, and a text field describing the offense based on the arresting officer’s notes. This information allows us to substitute the arrest offense, instead of the presumptive sentence, as the key case-severity control. This substitution means that we are estimating sentencing gaps between black and white defendants who look similar near the beginning of the justice process, rather than between those whose cases have come to look similar near the end of it. We can thus estimate the aggregatesentencing disparity introduced by decisions throughout the post-arrest justice process. In addition, the arrest offense codes provide far more detail on crime type than sentencing studies typically control for. The arrest offense is not a perfect proxy for underlying criminal activity, to be sure. We discuss its limitations below.71

Second, our dataset includes rich information on initial charges, in addition to final charges. Specifically, we know the statutory sections under which the defendant was charged and convicted—for instance, 18 U.S.C. § 924(c).72 To assess charges quantitatively, we translated each combination of statutory sections into a numeric measure of total charge severity. This is not a simple task, which may be an additional reason prosecutorial decision-making is under-researched. Based on comprehensive research on every federal crime charged during the study period, we developed four different charge severity measures. The first three were grounded in sentencing law: the statutory maximum and minimum and a Guidelines-based measure.73 The fourth measure was based on sentencing practice: the mean sentence given in a baseline period before the study period. We then calculated the combined severity of all charges on all these measures, following the rule laid out in the Guidelines for sentencing in multi-charge cases: we assumed sentences on each charge would run concurrently, unless one of the statutes specified consecutive sentencing.74

Sometimes, the statutory provisions in the data contained multiple sentencing schemes depending on the facts of the case; even more often, the Guidelines sentence would vary according to the facts. Where possible, we resolved such ambiguities based on the other charges in the case; often, the presence of a second charge would make it evident that the prosecutor was alleging a particular fact that would affect the sentence on the first charge.75 In other cases, we used reasonable, research-driven assumptions about which subparagraphs were likely to apply to most cases brought under that statute.76 However, in drug cases, the ambiguities were too extreme to resolve with these methods—most cases were charged under omnibus provisions (such as 21 U.S.C. § 841(b)) encompassing all drug types and quantities. We could not meaningfully code the severity of such provisions, and thus cannot assess initial charging disparities in drug cases. It is still possible, however, to analyze drug cases focusing on disparities in the final mandatory minimum recorded at sentencing, a separate data field. Child pornography cases must also be excluded from initial-charging analyses because of a similar ambiguity, but they can likewise be included in analyses of the final mandatory minimum.77 We also excluded immigration cases for different reasons: their stakes typically turn on deportation, making prison sentence length analysis a very incomplete picture of case outcomes, and they involve different “fast-track” procedural environments, which present different policy considerations and also raise concerns about the quality of data.78

We focused on the race gap between black and white U.S. citizen males. In a separate study focused on gender disparity, discussed below, Starr also assessed the race gap among women.79 Outcomes for other racial groups were not analyzed because their numbers were very small. Hispanic defendants are included among the black and white defendants.80

C. Our Research on Racial Disparities in Charging and Sentencing: Some Key Findings

Our research on the disparities introduced throughout the post-arrest justice process, and their procedural sources, gives us strong reason to believe that the concerns expressed above about sentencing-stage-only estimates are problematic in practice as well as theory. We intend in future research to assess the specific contribution of every major stage of the justice process, but we began by focusing on initial charging and its role in explaining sentencing disparities. This stage has been almost entirely ignored by existing research, and it is especially important. In most federal cases, the initial charge is the final charge; charge-bargaining is the exception, not the rule.81 In this period, dropping charges once filed required a supervisor’s special approval.82 In initial charging, however, the line prosecutor had, and has, considerable discretion.83 In addition, before one can even begin to make sense of plea-bargaining disparities, one has to first know whether the baseline charges already reflect disparities.

The statistical analysis and the resulting estimates are described in detail in the study.84 Here, we highlight some key findings and focus on their implications for legal policy and for assessing the impact of Booker. We had three main research questions:

1.      Do prosecutors charge otherwise-similar black and white arrestees differently?

2.      Do otherwise-similar black and white arrestees ultimately receive different sentences?

3.      How much of the sentencing disparity can be explained by the charging disparity?

By “otherwise similar,” we mean similar in terms of the pre-charge case and defendant characteristics that we can observe. In the charging analysis (Question 1), we controlled for arrest offense; district; age; whether there were multiple defendants in the case; and county-level poverty, unemployment, income, and crime statistics. In the sentencing analysis (Questions 2 and 3), we added additional controls based on data recorded only for sentenced defendants: criminal history category and education level. Other variables were available only for subsets of the sample, but we checked to make sure that within those subsets, the results did not change when they were taken into account. These included defense counsel type, marital status, and Hispanic ethnicity, as well as dummy variables for whether certain facts were recorded in the written arrest offense description: possession of guns, other weapons, or drugs; conspiracy; racketeering; child victims; and official victims. For all three questions, we used a sample limited to male U.S. citizens.85

On Question (1), we didfind significant racial disparities in charge severity across all four charging measures. The racial gaps were fairly moderate (less than 10%), but significant.86 But the disparities in mandatory minimums were much more dramatic. After controlling for the variables above, we found black men were still nearly twice as likely to be charged with an offense carrying a mandatory minimum sentence.87

Question (2) focuses on the aggregate sentencing disparity introduced by the entire post-arrest justice process. Among those convicted there were significant unexplained sentencing disparities favoring white defendants. Most of the large raw sentencing gap (which was around 50%) could be explained by the observed case and defendant characteristics—that is, the gap declined substantially when we added the controls to the model. We then used decomposition methods to identify which controls were the most important in explaining the raw sentencing gap. The factors that could explain by far the largest components of the black-white gap were arrest offense and criminal history. But even after controlling for these and other variables, a gap of about 10% remained unexplained in the main sample, which excluded drug and child pornography cases.88 The gap was a bit larger in the sample that included drug and child pornography cases (such that the sample consisted of all non-immigration case types). Thus, like other studies, our analysis found significant unexplained racial disparities in sentences.

However, our analysis of Question (3) showed that these gaps do not appear to be solely (or even principally) driven by the final sentencing decision. Rather, initial charging—especially the decision to bring mandatory minimum charges—is an important driver of these sentencing disparities. Half of the 10% otherwise-unexplained sentence gap in the main sample disappeared when we controlled for mandatory minimum charges.89 Furthermore, that estimate almost certainly understates the impact of mandatory minimum charges because of the very conservative coding method we used—when our charge information was ambiguous, we assumed there was no mandatory minimum, which means we missed a substantial number of them.90 When we instead controlled for the final mandatory minimum sentence (which is unaffected by the coding ambiguities, because it is recorded by the sentencing judge), all the otherwise-unexplained racial disparity in the average sentence disappeared.91

We performed this latter analysis for drug cases and child pornography cases as well; this was possible because it did not require using the ambiguous initial charge data. In a sample consisting of all non-immigration case types, including drug and child pornography cases, no significant disparity remained after controlling for the final mandatory minimum.92 In short, the results when one includes drug and child pornography cases are consistent with the results when one excludes them: a substantial black-white gap that is unexplained by the control variables, but which appears to be driven largely by differences in the use of mandatory minimums.93

We subjected all of these findings to a battery of robustness checks to assess whether varying the control variables, the sample definition, or the estimation method changed the results. Similar disparity patterns appeared in all specifications and subsamples. Mandatory minimum charging disparities were similar across offense types, but the non-drug mandatory minimum that was the most common and the most responsible for driving sentencing disparities was the enhancement for crimes involving firearms, found in 18 U.S.C. § 924(c). This statute has particularly harsh penalties: at least five years, running consecutively to other charges. There are higher minimums if the firearm is brandished or discharged and astonishing minimums (at least thirty years) if there is more than one § 924(c) count, which could simply mean that the defendant was found with two guns.94 Prosecutors have considerable discretion in applying this statute, especially when the facts make the relationship of a gun to an offense ambiguous (for instance, when the gun is found in the defendant’s car trunk), and a lenient prosecutor may “swallow the gun” entirely.95 Michelle Alexander, in her recent book about race and incarceration, quotes a former U.S. Attorney describing one such incident:

I had an [assistant U.S. attorney who] wanted to drop the gun charge against the defendant [in a case in which] there were no extenuating circumstances. I asked, “Why do you want to drop the gun offense?” And he said, “He’s a rural guy and grew up on a farm. The gun he had with him was a rifle. He’s a good ol’ boy, and all good ol’ boys have rifles, and it’s not like he was a gun-toting drug dealer.” But he was a gun-toting drug dealer, exactly.96

Our results suggest that this incident may not have been an anomaly.

D. Interpretations and Limitations

Our research thus suggests that the post-arrest justice process—especially mandatory minimum charging—introduces sizable racial disparities. But are these gaps really the result of racially disparate treatment? Or do they stem from unobserved differences that might be appropriate bases for different treatment? As Judge Nancy Gertner has warned, the quest to eliminate improper disparities should not lead us to seek “false uniformity” among cases that are actually dissimilar despite superficial similarities.97

No observational study can fully tease out the causes of demographic disparities because no dataset can ever capture all the subtle ways in which cases can differ.98 So one must tread cautiously when discussing causation—we speak in terms of “unexplained disparity,” rather than claiming to have proven “discrimination.” Still, our data are rich enough to shed light on some plausible causal theories, as we will briefly discuss in this Section. In addition, we point to some ways in which our disparity estimates may be under-inclusive—they do not encompass every discretionary choice shaping the black-white gap. Finally, we discuss the way these racial disparities appear to interact with gender disparities to produce particularly bad outcomes for black males.

1. Possible Unobserved Offense Differences

A first potential concern with the arrest offense control is unobserved differences in the underlying criminal activity. This concern is less severe than it might have been: the detailed USMS offense codes, together with the written offense description field, capture considerable nuance in offense facts. In particular, they seem to effectively capture whether a gun was involved with the offense, which is important because of the substantial contribution of 18 U.S.C. § 924(c) charges to racial disparities.99 The multi-defendant case variable also captures an important offense characteristic, because multi-defendant cases often involve more serious crimes and often trigger conspiracy charges.

In drug cases, in addition to the limitations to the charge data, the arrest codes also contain an important ambiguity: they do not specify drug quantity, and other sources of initial alleged quantity are only reliable before 2004.100 But estimates on the most recent years with reliable quantity data (2001-03) were not substantially affected by the addition of quantity controls.101 There were also racial disparities favoring whites in the drug quantities found at sentencing fact-finding, after controlling for the seizure quantity and drug type recorded at arrest.102 This suggests that white defendants may be negotiating more favorable plea stipulations on quantity.

Similarly, the arrest data do not record the dollar value of losses in economic crimes. In some cases, the arrest codes suggest the scale of the crime (for instance, pickpocketing or vehicle theft), but in others (such as wire fraud) they do not. It is unlikely, however, that differences in loss quantity could explain the racial disparities—in fact, they probably cut in the opposite direction. At least as recorded at sentencing fact-finding, white defendants tend to be involved in significantly higher-value property crime cases, after controlling for the other covariates.

Another important factor not captured by the arrest data is the defendant’s relative role in group offenses. We do not know of any anecdotal reason to believe that such differences could explain the racial disparities, that is, that white defendants tend to be minor players in conspiracies while black defendants tend to be leaders. If this were the basis for the ultimate gaps, one would expect to see a noticeable difference in role adjustments at the sentencing fact-finding stage. But black defendants get only very slightly worse role adjustments on average: a difference of 0.04 offense levels on the forty-three-level Guidelines scale, after controlling for the observed variables.103 This difference is statistically significant, but it is very small, and suggests that role differences are unlikely to explain much of the black-white sentencing gap.

2. Possible Differences in Offender Characteristics

Beyond the offense characteristics, there might be relevant offender characteristics that contribute to the race gap. We control for criminal history, the main offender characteristic built into sentencing law.104 The most obvious other possibility is socioeconomic differences, which are highly correlated with race. While poverty would not be a “warranted” reason for worse case outcomes, it would be a non-racial one and might suggest different policy approaches. However, the unexplained disparities we identify exist even after controlling for a variety of socioeconomic indicators such as education, county-level variables, and defense counsel type (an excellent proxy for poverty because public defenders or other publicly funded counsel are appointed only if the defendant is poor). Perhaps more remarkably, our socioeconomic factors taken together do not contribute significantly to the “explained” share of the racial disparity.105 This appears to be because poverty itself (as reflected by these indicia) is not an important predictor of higher sentences.106 Notably, representation by a public defender is associated with slightly lower sentences, all else equal.

This absence of socioeconomic disparity is good news, and it cuts against conventional wisdom.107 Can it really be that poor defendants do not fare worse? It is possible that the conventional wisdom might not apply to the federal courts, where indigent defendants generally receive high-quality representation, especially from federal public defenders.108 We suspect that we would not have gotten the same result had we studied states in which indigent representation is under-resourced and in disarray.109 We note that this point may have policy implications: the federal example offers a potential model for those states. When a justice system devotes sufficient resources to indigent defense to attract strong lawyers, train them well, and keep caseloads reasonable, poverty need not drive outcomes, and the race gap will likely be smaller than it might otherwise be.110

3. Possible Sources of Disparity that Our Estimates Leave Out

Although it is possible that our estimates of “unexplained” racial disparities include components that in fact have legitimate but unobserved explanations, in another sense these estimates are arguably under-inclusive. Our process-wide approach estimates disparities across a much broader swath of the criminal justice process than existing studies do, but even our method does not encompass all of the key decision points. In addition to prosecutors and judges, other decision-makers shape criminal case outcomes—most notably, law enforcement agents and policymakers.

Any disparities produced by those actors’ choices will be found in the “explained” portions of the race gap—that is, the portions attributed to the control variables. It is important not to overlook those portions when thinking about what should be done about racial disparity, however. Rather than simply using regression methods to filter them out, as most studies do, we therefore used decomposition methods that allow us to estimate the relative contribution of each control variable to the total observed black-white gap. These methods showed that the variables with by far the most explanatory value are arrest offense and criminal history. These variables may capture important differences that we want sentencing law to reflect, but they also reflect discretionary choices.

First, the recorded arrest offenses will be affected by law enforcement choices.111 This is a key limitation of our strategy of controlling for the arrest offense. We stated earlier that policymakers should ideally ask whether those who committed the same crime end up with the same sentence, but this is a very hard question to answer empirically. Researchers cannot observe what the defendants actually did. The arrest offense is a much better proxy for actual conduct than the presumptive Guidelines sentence, but it is not a perfect one. If it diverges from actual conduct in a racially disparate way, our “unexplained” disparity estimates will not capture that divergence. Nor do our estimates capture sample selection introduced by police decisions that determine who lands in the federal criminal justice system at all.112

In theory, these limitations could bias our results in either direction, but we think they probably mean we are understating the total disparities in the justice system. For arrest-stage disparities to explain our results instead, even partially, one would have to believe that federal law enforcement favors black suspects. We think this is unlikely. Many criminal justice scholars have argued that black males are disproportionately targeted by law enforcement, while virtually nobody claims the opposite.113 Black people are arrested for drug crimes at a much higher rate than white people are, even though they self-report both drug use and drug dealing at equivalent or lower rates.114 Beyond comparing arrest rates to reported crime rates, policing disparities are hard to study empirically because the underlying criminal behavior usually cannot be observed by researchers. But the existing quantitative evidence either supports the conventional wisdom or at least does not cut in the oppositedirection.115 To be sure, federal law enforcement could be different, but we are likewise unaware of any anecdotal suggestions that federal agents favor black suspects.

In addition, both the arrest offense and the criminal history components of the “explained” disparity reflect subjective policy choices: important sources of disparity may simply be built into the law.116 In the Fair Sentencing Act of 2010, Congress responded to such a concern by partially mitigating the sentencing framework’s notoriously harsh treatment of crack cocaine cases.117 But the crack laws are not the only example of particularly heavy punishments being given to crimes disproportionately involving black defendants. The harsh gun enhancements under 18 U.S.C. § 924(c) are another example—because black men are more frequently arrested with guns, as shown by our data, these enhancements would disparately impact black men even if they were neutrally applied. Similarly, our data show that black males are also more frequently arrested for violent crimes, and sentencing law is often harsher on these crimes than on nonviolent crimes that might reasonably be considered more serious.118 These sentencing-law features are built into the arrest offense component of the measured disparities.

The criminal history component likewise reflects a subjective policy judgment to assign heavy weight to past crimes, even though those crimes have already been separately punished. While there are many competing considerations surrounding that judgment, it has a racially disparate impact. Moreover, this choice magnifies whatever racially disparate treatment exists in the criminal justice system by carrying its impact from one case to the next: the criminal history score may be influenced by disparate treatment in past cases. That past disparity will appear as part of the “explained” disparity, so it is easy to lose sight of it—it will be filtered away by controlling for criminal history.119 Underlying unwarranted disparity can thus come to appear legally warranted.

4. Race, Gender, and Their Interaction

Finally, another limitation is that we only include men. Starr’s related study examines gender disparities and race-gender interactions.120 She finds unexplained gender disparities that dwarf the racial disparities our joint study found: men receive sentences that are over 60% longer than women’s, even after controlling for the arrest offense, criminal history, and other pre-charge observable characteristics.121 These gaps are much larger than most other studies have estimated because—as with race—they appear to mostly arise prior to the final sentencing decision.122 The data suggest that differences in offender characteristics not captured by the main control variables may explain substantial shares of this gap, particularly differences in childcare responsibilities and perceived role in group offenses.123 But Starr finds large unexplained disparities (over 50%) even among non-parents and in one-defendant cases, so these explanations do not appear to come close to explaining the whole gender gap, nor do any of the other theories Starr is able to test.124

Notably, the gender gap was substantially larger (about 75%) among black defendants.125 The racial disparities we found for men do not recur among women; there is no significant unexplained black-white gap in sentences for female defendants. The black female/white female gap appears to be explained entirely by differences in arrest offense and criminal history—although, again, it is possible that these factors build in structural, arrest-stage, or other hidden sources of disparity.

As noted above, black males are incarcerated at extremely high rates in the United States, and, in assessing this problem, policymakers should consider both the race and gender dimensions and their interactions. Black male defendants appear to face not only the harsher side of both the racial and gender disparities, but also an additional interaction effect—an extra apparent penalty for being both black and male. Gender disparity need not be seen as being about special treatment of women—rather, one could ask why the criminal justice system appears to treat males so much more harshly. If it did not, Starr’s data suggest that many fewer black men would be in prison.

III. the booker question: does expanding judicial discretion increase racial disparity?

The discussion above illustrates the serious limitations of an empirical approach that focuses on the sentencing decision in isolation. In this Part, we apply that insight to the question that so worried Justice Stevens in his Booker dissent: has freeing judges to sentence outside the Guidelines led to an increase in unwarranted disparities? The Sentencing Commission has given the most prominent answer to this question so far, and its answer is a resounding yes. Its race findings have garnered understandable attention, because they are shocking: Booker and its progeny appear to have led to a nearly fourfold increase in racial disparity in sentencing, from 5.5% to 19.5%.126 This was an explosive finding, and it has led to calls (spearheaded by the Commission itself) to reinstate stronger constraints on judicial discretion.127 However, we show here that the Commission’s conclusions are unfounded. Properly analyzed, there is no evidence that unexplained racial disparity in sentences has increased since Booker—much less because of Booker.

There are two core problems with the Commission’s analysis of Booker—problems that also pervade the rest of the empirical literature examining the disparity consequences of sentencing law reforms. The first is that the studies estimate disparity in a very limited way—the problem discussed in Part II. In Section III.A, we explain why the “presumptive sentence” approach is a particularly poor choice for analyzing Booker’s effects, and we present a simple linear trend analysis showing that when disparity is estimated using our broader method, it has not increased in the years since Booker (and may have declined). In Section III.B, we discuss an additional serious problem with the existing studies: poor causal inference strategies. Even if it were true that disparity had increased after Booker, that is, these studies provide no reason to believe Booker was the cause. In Section III.C, we introduce a method that can be used to assess causation—a regression discontinuity-style approach. In Section III.D, we present the results of this analysis of Booker’s effects on sentencing as well as charging and plea-bargaining. Finally, in Section III.E, we discuss the limitations on our analysis and explain why researchers may never be able to give an entirely definitive answer to the question of Booker’s effects.128

A. The Changing Yardstick Problem

A subset of the sentencing disparity literature focuses on measuring changes in disparity resulting from changes to sentencing law, such as Booker. Like other sentencing disparity analyses, these studies typically control for the presumptive Guidelines sentence as well as the statutory mandatory minimum. The problem with this approach is largely explained above, but it impacts sentencing-reform studies in a slightly different way. In principle, studies focusing on changes in disparities have an advantage over those that estimate the extent of “unwarranted” disparity: the ability to ignore the possibility of stable differences between groups that the observed variables do not capture.129 Suppose the control variables amount to only a “broken yardstick” for measuring the defendant’s underlying criminal behavior—for instance, suppose the presumptive sentence variable diverges from true case severity in racially disparate ways. In a policy-change study, so long as the same broken yardstick is used before and after the policy change, one can validly estimate the policy’s relative effects on different groups. This advantage is a mixed blessing: estimates of changes in disparity are less policy-relevant if we do not know whether the disparity in either the pre- or the post-period is “real.” Still, not every study needs to answer every question, and research that brackets the “is this real?” question can be useful.

However, a serious problem arises if one cannot be confident that the yardstick itself has not been affected by the policy change. Consider again the 2012 Sentencing Commission report discussed above. It found that the black-white gap rose from 5.5% before Booker to 15.2% after, and finally to 19.5% after Booker’ssuccessor cases Kimbrough and Gall.130 Other studies have likewise found at least some increase in disparity after Booker or after Kimbrough and Gall (although not as large).131 Below, we discuss potential confounding factors that make it very problematic to infer that these changes were caused by either Booker or Kimbrough/Gall. But let’s start with a more basic question: do these numbers actually tell us that racial disparity in sentences has grown?

In each period, the Sentencing Commission estimates sentencing disparities conditional on the presumptive sentence (likely a “broken yardstick” for the reasons discussed above), and then compares the disparities across time periods. If one were certain that racial disparities in the processes determining the presumptive sentence remained constant pre- and post-Booker, then this would be a “same broken yardstick” comparison. Whatever biases were hidden in the presumptive sentence variable would affect the estimates for both time periods similarly, so the comparison would be apples-to-apples.

But the problem is that Booker may have replaced one broken yardstick with a different one by affecting charging, plea-bargaining, or sentencing fact-finding in racially disparate ways. In other words, cases with the same presumptive sentences may represent different actual conduct pre- and post-Booker in ways that vary by race. Sample selection bias is also a potential problem: Booker may have changed which cases are winnowed out by the “funnel” of the criminal process, such that the samples of sentenced cases before and after Booker are not fairly comparable.

There is good reason to worry about these potential biases. One clear lesson from the legal scholarship reviewed in Part I is that the stages in the criminal justice process are interrelated. Charging, plea-bargaining, and fact-finding all occur in anticipation of and in an attempt to influence the sentencing consequences. It is not even remotely safe to assume that changes in sentencing law do not affect decision-making at those earlier stages. After all, consider what happened after the Guidelines were adopted: a drasticincrease in guilty pleas, which legal scholars have (very plausibly) attributed to prosecutors’ sharp increase in leverage.132

There are many theoretically plausible ways decision-making prior to sentencing could have changed after Booker. For example:

·        Prosecutors might have to offer more favorable plea deals to induce guilty pleas, potentially resulting in more favorable findings of fact, reduced charges and presumptive sentences, and perhaps more trials.133

·        Prosecutors could respond to the reduction in their power to manipulate the Guidelines to control the sentence by expanding use of their other tool for constraining judges: statutory mandatory minimums.

·        Judges might become less willing to make findings of fact that diverge from the plea stipulations, because doing so is no longer necessary to achieve what they perceive as a just sentencing result—they can depart instead.

These changes would only bias estimates of post-Booker changes to racialdisparity if they had a racially disparate impact on the presumptive sentence or on the composition of the sentenced sample.134 It is possible that this is not so, of course, but one cannot simply assume it is not so—it must be tested. However, all of the existing studies of Booker (and prior studies of the initial shift to mandatory sentencing) do assume exactly that, usually implicitly. Other studies have criticized various other aspects of the Sentencing Commission’s Booker study and have reached different conclusions. But these studies too have taken the sentencing-stage-only approach, controlling either for the presumptive sentence or for something closely related (the Guidelines “base offense level”), and thus are subject to the same concern.135

These studies, in short, ignore the “hydraulic discretion” theory that has dominated theoretical scholarship about sentencing reform.136 Conversely, key aspects of the hydraulic discretion theory remain almost completely untested empirically.137 No empirical studies have yet used case data to assess changes in disparities in charging, plea-bargaining, or sentencing fact-finding in the wake of Booker. One study surveyed federal district court judges and defense attorneys about their perceptions of whether aspects of plea-bargaining had changed.138 However, the researchers did not evaluate these perceptions’ accuracy, and the perceptions of judges and defense counsel varied quite substantially.139

Just a few studies have looked at changes in charging and plea-bargaining disparities in response to earlier changes to sentencing law and policy. Wooldredge et al. found that Ohio’s shift to mandatory sentencing reduced racial disparities in charge-bargaining, yet increased racial disparities in sentencing (a surprising result).140 But the authors did not evaluate changes in initial charging, without which the results are harder to interpret. In a 1987 study of Minnesota’s adoption of mandatory sentencing guidelines, Miethe did evaluate initial charging and found a small but significant increase in gender disparity and no significant change in racial disparity; plea-bargaining disparities were unchanged.141 No studies have evaluated changes in disparities in sentencing fact-finding.

Beyond the failure to account for pre-sentencingstages of the process, recall that the Sentencing Commission’s study of Booker has an additional problem: it also controls for departure status, thereby also filtering out some of the potential disparities in the sentencing decision as well. This is an especially surprising choice for a study of Booker’s effects, because, as we will see below, Booker dramatically changed the probability of a departure from the Guidelines by authorizing departures that were previously forbidden. It is odd to compare racial disparities in sentencing before and after Booker only afterfiltering out those mediated by racial differences in departure rates.

In Table 1, we show that the “changing yardstick” problem is neither merely theoretical nor subtle: the use of these problematic control variables can completely changethe apparent trends in racial disparity. We used a simple linear time-trend model to estimate the overall difference in sentences imposed on black and white defendants, as well as the average growth in that gap over time.142 We included cases sentenced between the PROTECT Act and the end of fiscal year 2009, and focused on black and non-Hispanic white men.143 Thus, this analysis covers the time period and groups for which the Sentencing Commission found the purported quadrupling of disparity.144 The sample includes all non-immigration cases except those subject to major substantive sentencing-law changes during the study period: identity theft, obscenity/child sexual exploitation, and sex offender registration. For reasons explained above, we omit immigration cases.145

The purpose of Table 1 is to show the contrast in racial disparity estimates and time trends when one uses our preferred method of measuring disparity (described in Part II) as compared to variations on the “presumptive sentence” method. In Column 1, we show the estimated linear trend in average sentence when controlling for the arrest offense and other prior characteristics (our preferred method).146 That is, Column 1 shows the trend over time in the aggregate black-white sentence disparity introduced during the post-arrest justice process.The estimated trend in racial disparity is insignificant, and its sign is actually negative: the model (noisily) estimates that the unexplained black-white sentence gap declined by 2.1 months, from about 12.7 months to about 10.6 months, over the course of the period.147

The negative sign of this estimated change is consistent across a variety of estimation strategies and sample definitions. For instance, while Table 1 shows the results when sentence length is estimated in months (including non-incarceration sentences as zeros), we get similar results if we use a log-linear model excluding the zeros. We also get essentially identical results when we estimate yearly rather than monthly trends. Likewise, we see no rise in disparity over time when, instead of estimating linear trends, we estimate the differences in the “black” effect among the three key time periods that the Sentencing Commission study identifies (PROTECT-to-Booker, Booker­-to-Gall, and post-Gall).148 And indeed, some reasonable variations on our approach produce significant and much larger estimated downward trends. For instance, the Table 1 results exclude offense categories that were affected by major substantive changes in the law, because we wanted to focus on disparity trends in the administration of the law. But had we included these offense categories (as the Sentencing Commission did), the estimated decline in disparity during the study period would have been significant and nearly three times as large—about six months total.149

Why, then, does the Sentencing Commission find an increase in disparity during this period? There may be a variety of explanations,150 but a prime reason appears to be that racial disparity in the processes determining the presumptive sentence declined significantly over the same period. By controlling for the presumptive sentence, the Commission filtered out that reduction in disparity, leaving only a misleading picture. The black-white gap in sentences relative to the presumptive sentence may have grown, but that is because the black-white gap in presumptive sentences shrank (after controlling for underlying case characteristics). In other words, when one controls for the presumptive sentence, the disparities look larger in the later period because the presumptive sentence control is filtering out less of the disparity. The presumptive sentence was not the “same broken yardstick” during this period. Over time, the yardstick changed.

Columns 2 through 4 of Table 1 illustrate this point. In the regression shown in Column 2, rather than controlling for the arrest offense, we substituted the final offense level, the mandatory minimum indicator, and broad offense-type categories associated with the offense of conviction. This reflects a fairly typical version of the presumptive sentence approach. Recall that the presumptive sentence is determined by the final offense level (and the criminal history category, which we control for in all regressions). The regression in Column 3 is identical except that we more closely approximate the Commission’s approach by also adding departure status controls.151 After these modifications, both of these regressions show a significant linear increase in racial disparity over time, albeit not as dramatic an increase as the Commission itself found. In the Column 2 version, the unexplained black-white gap increases from about 3.2 months at the beginning of the period to about 6.5 months at the end. When departure status is added as a control in Column 3, the black-white gap is estimated to rise from about 0.9 months at the beginning of the period to about 4.2 months at the end.152

Thus, when we use variations on the presumptive sentence approach, we do see significant increases in disparity, just as other studies have found. But that approach is inappropriate and misleading, because of the “changing yardstick” problem. Column 4 focuses directly on that changing yardstick. In Column 4, we show a time-trend regression with the final offense level as the outcome of interest. After controlling for the arrest offense and other pre-charge characteristics, the unexplained black-white disparity in final offense levels declined by nearly one level during this period. For the average case in the sample, a change of one offense level is associated with a five-month change in presumptive sentence length—close to the difference between the disparity trend estimate in Column 1 (-2.1 months) and those in Columns 2 and 3 (+3.3 months).153 That is, the changing nature of the presumptive-sentence yardstick appears to explain nearly all the difference between the disparity decline that we measure using our method (Column 1) and the apparent increase that one sees when one uses a method paralleling those of other studies.

Thus, the overall unexplained racial disparity in the post-arrest justice process certainly does not appear to have increased from 2003 to 2009, and if anything, it seems to have decreased. The linear trend results do suggest that the procedural sources of disparity may have shifted over the course of the period, with the earlier stages in the process becoming a bit less important and the judicial sentencing decision becoming a bit more important. However, it bears noting that throughout the time period, the earlier process stages appear to be the dominant procedural sources of disparity. That is, the overall estimated racial disparities are much larger when one controls for the arrest offense—thereby incorporating disparities from those earlier procedural stages—than when one uses either version of the presumptive sentence model (compare the “black” coefficient in Column 1 to the “black” coefficients in Columns 2 and 3). This is consistent with our research on the sources of post-Booker disparities,154 which finds that even in the most recent years, charging decisions appear to be the major driver of sentencing disparity.

Note that we make noclaims as to the causes of these longer-term trends, and specifically, we do not claim to have established that Booker caused them. As we explain in the next Section, causal inference from changes over lengthy periods of time is a fraught enterprise. Table 1 merely shows that, even setting aside the causal inference concern, racial disparity in the post-arrest justice process is no worse today than it was before Booker was decided.

B. The Causal Inference Problem

In addition to the use of inappropriate control variables, there is another major methodological problem with previous studies of Booker’s effects: they lack a basis for sound causal inference. Causal inferences from changes over time are always risky, because many things change over time. Comparisons of averages between periods before and after a policy change, while appealingly simple, can be misleading.

These studies generally compare the average disparity before and after a policy change. In most, disparities are estimated separately for each period using a regression model that controls for the presumptive sentence and other observed variables.155 The recent federal studies have focused not just on Booker, but also on other recent policy changes affecting judges’ sentencing discretion. One such change was Title IV of the PROTECT Act of 2003, which imposed rules intended to discourage downward departures from the Guidelines. It required courts to report to Congress on departure rates, required written justifications for departures, provided for de novo appellate review of departures in some cases, restricted the Sentencing Commission from creating new grounds for downward departures, limited judicially initiated downward adjustments for “acceptance of responsibility,” and directed DOJ to adopt an action plan for reducing departures.156 The Supreme Court’s December 2007 decisions in Kimbrough and Gall (discussed above), which reinforced the Booker holding, have also been a focus of the recent research.157

The Sentencing Commission focused on three primary time periods, with cases classified by sentencing date: (1) PROTECT-to-Booker (nearly two years), (2) Booker-to-Kimbrough/Gall (nearly three years), and (3) post-Kimbrough/Gall (nearly two years). It found the lowest black-white disparities in period (1), when judicial discretion was the most limited, and the greatest in period (3), when discretion was broadest.158 A competing study by Jeffrey Ulmer, Michael Light, and John Kramer criticized aspects of the Commission’s method, but it too compared averages across these time periods (as well as earlier periods).159 It similarly found increases in racial disparity in the post-Booker and post-Kimbrough/Gall periods, although these effects were concentrated in the decision whether to incarcerate defendants rather than in sentence length among those incarcerated.160 A recent study by Jeffrey Nowacki similarly compares the cases from 2002-2004 (pre-Booker) to those from 2005-2008 (post-Booker), and finds a fairly small but significant increase in disparity in the latter period, controlling for final Guidelines offense level, criminal history, and other variables.161

But comparison of averages across such broad periods is at best suggestive and is too blunt a tool for causal inference. Differences in the averages between periods might merely reflect longer-term trends or other intervening events. If racial disparity were rising steadily throughout the period, for instance, the average disparity after Booker would necessarily be larger even if Booker had no effect on racial disparity. In fact, this would be true even if Booker actually slowed the rate of increase in disparity.

Sentencing disparity might well be affected by numerous non-Booker-related developments over periods of this length. One possibility is changes in the underlying case mix—including case types, severity, and defendant characteristics—as underlying crime patterns and federal law enforcement priorities change. Controlling for case characteristics within each time period, as the Commission and similar studies do, only filters out the effects of differences in the distributions of characteristics for black versus white defendants during that period. It does not mean that changes in the case mix between time periods will not affect the disparity estimates. The type of model used by the Commission and in similar studies gives a single estimate for the effect of being black, averaged across all (male) cases, but in practice this average surely hides heterogeneity. That is, the gap between white males and black males might in practice vary depending on the nature of the case or the defendant’s characteristics.

For instance, imagine that there are just two kinds of cases in a sample—fraud and robbery—and that the average unexplained black-white gap is 5% for frauds and 20% for robberies. The Commission’s approach would produce an average disparity estimate somewhere between 5% and 20%, depending on what fraction of the cases are frauds and what fraction are robberies. If the fraction that are robberies is gradually growing over time, then racial disparity will appear larger in the regressions from the later periods even if nothing else changes (that is, even if the gap remains 5% for fraud cases and 20% for robbery cases).162

Changes in the case mix are not the only potentially confounding developments that could occur over time. Other possibilities include the policies and prosecution strategies of the Department of Justice changing or taking time to trickle down to line prosecutors; changes in the composition of the judiciary, U.S. Attorneys’ and public defenders’ offices; or administrative changes in supervision of prosecutors that shift their incentives. Even if these developments had no racial purpose, they might have had racially disparate impacts. Causal inferences would be more credible if effects were visible in a much shorter time window, such that one could more confidently assume that Booker is the only important change that could have driven the outcome. One can also filter the surrounding trends out of the estimates of the policy’s effects by including them in the regression.

Among the recent Booker studies, Fischman and Schanzenbach’s offers an improvement on the standard approach.163 Their model filters out year-to-year variation in sentencing patterns for different categories of crimes and judicial districts, which captures an important subset of the things that might vary over time. They focus on changes in appellate review of sentencing and find that, in general, looser review has not been associated with increased racial disparity, although (like the Sentencing Commission) they do find a recent increase in disparity after Kimbrough and Gall.164 However, their approach only filters out trends in racial disparity if they are mediated by the crime category or district; any trends driven by other factors are left in. Below, we set forth an approach that filters out continuous trends in racial disparity itself (rather than trends in particular factors that contribute to it) and that uses monthly data to capture within-year variation as well.

C. Our Method

In order to disentangle Booker’s effects from surrounding trends,rather than comparing racial disparities averaged over periods of years, we create flexible regression models that filter out month-to-month trends (including non-linear trends) in sentences and other relevant outcomes. We then look for sharp breaks in these trends—discontinuities—immediately after Booker. This approach is, in effect, a regression discontinuity-style estimator (RD), and, for simplicity, we will use the label RD here.165 Like other studies, we base our causal inferences on changes over time, and any unmeasured changes that coincided with Booker could trick us. But because we are looking for immediate sharp changes, this concern is less grave. While a lot can change in a couple of years, usually a lot less changes suddenly in a couple of months. In addition, even if continuous background trends did have a noticeable effect on disparities in those couple of months, our method filters the trends out. We are looking only for sharp breaks that coincide with Booker. If the surrounding trends are fairly smooth and there is a sudden break at Booker, the inference that Booker caused the change depends only on the assumption that no other unobserved factor affecting sentencing disparity suddenly changed at the time of Booker.

Our sample runs from fiscal years 2001 to 2009 and includes women and non-citizens (with controls for gender and citizenship). This broad sample definition is useful in improving the precision of the estimates by increasing the sample size within each month. However, the results are substantively similar if these groups are excluded. The sample includes all non-immigration cases except identity theft, which was subject to other major sentencing-law changes very near Booker.166

Our overall research interest is in measuring the effect of changes to judicial sentencing discretion on sentencing and case processing disparities. We begin by looking at Guidelines departure rates, not because that is the ultimate outcome of interest, but because departure rates help us determine which legal reforms amounted to important changes to judges’ discretion in practice. They directly measure Guidelines compliance and thus are the most logical measure of the extent to which the Guidelines actually constrained judicial behavior at any given time. We focus our attention on Booker itself, not on its progeny Kimbrough and Gall or on the PROTECT Act’s tightening of the Guidelines. The reason can be seen plainly in Figure 1, which plots departure rates by sentencing month.167 Note that 96% of these departures are downward.

Figure 1.

departures over time

The vertical lines in Figure 1 mark four key events: the PROTECT Act, Blakely (Booker’s immediate predecessor), Booker, and Kimbrough/Gall (which clarified and strengthened Booker’s holding).168 As this graph makes clear, Booker was a major shock to the sentencing discretion afforded to judges. Departures increased immediately and substantially, from about 30% to about 40%. Although there are other month-to-month fluctuations, Booker marks by far the most dramatic break. After the immediate Booker jump, departures continue on a gradually downward trajectory similar to the one that existed before Booker—but the whole graph is shifted upward by about 10%, and the departure rate never returns to its pre-Booker low. In other words, Booker’s effects were sudden, but they were also lasting.

The sharpness of the change at Booker helps to alleviate one substantial concern about RD—its inability to capture effects that occur slowly. It is very possible that the full effects of Booker took a while to take hold—for example, the size of departures could have grown over time as judges became more comfortable with their newfound discretion. The inability to test that possibility is a disadvantage to our method. Policymakers are of course likely to be interested in Booker’s long-term effects. But focusing on the short-term effects can tell us something important about the expected direction of Booker’s long-term consequences, even though we cannot directly measure those long-term consequences.

Why, after all, would one ever have worried that Booker might increase sentencing disparity, as critics, including the Sentencing Commission, did? The theory is that giving judges more discretion frees them to sentence in ways that turn on their conscious or unconscious sympathies with, or predictions about, particular defendants, and that those sympathies or predictions will differ on the basis of race or other factors correlated with race. That is, the theory assumes that judges have inclinations that effectively favor white defendants over similar black defendants (more strongly than the previous mandatory-Guidelines regime already favored white defendants). Booker provides a chance to test whether that theory appears to be true. Legally, making the Guidelines non-mandatory was a sudden and enormous change to judicial discretion. The departure graph shows that this change was not just theoretical and did not take long to have effects in practice. On the contrary, the doctrinal shock to the scope of judicial discretion immediately manifested itself in substantially more frequent judicial exercises of discretion. If judges were, in fact, inclined to use broader sentencing discretion in ways that disadvantage black defendants, one would expect to see at least some of that effect in the immediate vicinity of Booker, even if the full effects of the decision took a while to play out. If there is no jump in disparity at Booker, it suggests that judicial inclinations were not what critics feared they were.

In contrast, the PROTECT Act and Kimbrough/Gall did not produce nearly as dramatic a change to the sentencing regime in practice. PROTECT appears to have caused no sudden change at all in departures. Kimbrough and Gall may have been more important—departure rates did rise afterwards—but the rise continued a trend that began three months before the decisions, and there was no sudden break in the trend (nor was there a sudden break at the time of Rita v. United States,169 five months earlier).170 Even if Rita and Kimbrough/Gall collectively led to an increase in departures, the fact that the decisions were separated by five months makes this too diffuse a change to judges’ sentencing discretion to assess with our method. And even combined, the change over that whole period is still much smaller than the change at Booker. One should not expect small changes to have big effects, and if they appear to, one has to suspect some confounding factor. Booker, as the bigger change, is the more logical place to test the effects of changing judicial discretion.

We thus assess the effects of Booker’sshock to judges’ departure discretion on other stages and outcomes in the justice process. Because criminal cases have several key dates, the RD method can be used to isolate Booker’s effect oneach key stage in the process. However, it cannot be used to directly estimate the aggregate effect of Booker on all stages. The Sentencing Commission and other Booker researchers have always divided cases by sentencing date, but many cases’ processing dates straddle Booker, so one cannot simply deem cases “pre-Booker” or “post-Booker.” We assess Booker’s effects on charging, as well as the sentencing consequences of those charging changes, by assessing what happens when the charging date passes Booker. Cases charged shortly before Booker will overwhelmingly have been disposed of and sentenced after Booker,171 so focusing on the immediate effects as the charging date passes Booker means that the sentencing effects of changing charging practices can be separated from the sentencing effects of changes to other process stages.

Likewise, we assess plea-bargaining changes and their sentencing effects by assessing what happens when the convictiondate passes Booker, and we assess changes in judicialbehavior by assessing what happens when the sentencingdate passes Booker. Note that the judicial behavior being measured involves not only changes to the final sentencing decision but also changes to sentencing fact-finding. Assessing the conviction date and the sentencing date separately helps to disentangle judges’ contributions to disparities in sentencing fact-finding from disparities in the negotiated plea stipulations.

The most serious complication in drawing causal inferences about Booker is that the decision was hardly a bolt from the blue. Rather, Booker followed six months after the Supreme Court’s decision in Blakely (denoted by the second vertical line in Figure 1), which applied the same Sixth Amendment analysis to a state sentencing scheme. It was Blakely that was an unexpected earthquake, rendering it fairly obvious that the federal Guidelines were in constitutional trouble.172 What was not clear was what the Supreme Court would do to remedy the constitutional defect. Instead of the advisory guidelines approach (which none of the circuits had adopted), the Court could have struck the Guidelines down entirely, left them mandatory but shifted fact-finding to the jury, or left the whole matter to Congress. The lower courts began weighing in, and the Supreme Court quickly agreed to review Booker.173

The Blakely decision raises a dilemma for causal inference for three reasons. First, it could mean that the effects we are looking for happened in a more diffuse manner starting before Booker, because courts or parties adjusted their behavior in anticipation of the mandatory Guidelines’ fall. In that case, estimating discontinuities at Booker alone might understate the effects of moving away from mandatory Guidelines. Second, the anticipation of Booker may have affected the mix of cases decided immediately before and after Booker, if district courts delayed sentencings while waiting for the Supreme Court’s opinion. Such changes in cases could confound estimates of Booker’s effects. Third, even assuming Booker did cause the measured changes, not all of Booker’s effects can necessarily be attributed to the expansion of judicial discretion. In addition to rendering the Guidelines advisory, Booker may have affected outcomes by ending the chaotic interregnum period and rejecting the alternative remedies that the Court could have chosen. These problems are not unique to our method—they afflict all studies of Booker—but they cannot be ignored.

For this reason, we constrain our analysis to five federal judicial circuits: the Second, Fourth, Fifth, Sixth, and Eleventh. Within two to six weeks of Blakely, these five courts of appeals issued decisions holding that Blakely did not apply to the federal Guidelines.174 In those circuits, Booker’s legal effects were simpler: it changed the governing law from the old regime (mandatory Guidelines) to the new one (advisory Guidelines). During the Blakely-to­-Booker period, there was neither legal chaos nor a third legal regime. Figure 1, which is limited to these “business as usual” circuits, shows that nothing happened to departure rates at Blakely or during the interregnum—there was no trend break until Booker.

Our focus on these circuits is only a partial solution to the Blakely problem. While district courts were required to follow the “business as usual” approach, if the parties anticipated that the Supreme Court would change the law before sentencing, they were free to let that expectation affect their charging and plea-bargaining decisions.175 Therefore, as detailed below, we also analyze changes happening at the time of Blakely to see whether there is evidence of such anticipation effects.

D. Regression Discontinuity Estimates of Booker’s Effects

Here we present our RD estimates for key charge severity, plea-bargaining, and sentencing measures. In addition to the results presented below, we also assessed changes in the criminal justice “funnel,” which could have introduced sample selection bias into the RD estimates. However, we found no significant change in the rate of filing charges in district court as the charging date passed Booker, nor in the rate of non-petty convictions as the disposition date passed Booker.176

1. Changes to Charging

The principal charging dynamic that we sought to analyze is whether Booker affected prosecutors’ use of mandatory minimums, which our (post-Booker) findings discussed in Part II show to be a key driver of the black-white gap. There is also a logical causal mechanism for such an effect. Booker reduced prosecutors’ ability to use the Guidelines to control sentencing outcomes, an ability that confers massive leverage in plea-bargaining. Without being able to rely on the Guidelines, it is plausible that prosecutors might turn more often to their other tool for constraining judges: mandatory minimums.

Our findings above also clearly showed that it was the initial charging stage in which the mandatory minimum disparity emerged, so that is a key stage to analyze. As explained above, we could not code initial charges in drug or child pornography cases. We only know the final mandatory minimum in these cases. Fortunately, unlike in the analysis in Part II, in this part of our analysis there is a solution to this problem. RD allows us to assess changes to the final mandatory minimum when the charging date passes Booker.177 Even though the outcome variable is measured at the conviction stage, changes in it that are triggered by the timing of the charge are probably the result of charging changes.178 This approach allows us to assess all case types.

The results from the formal RD analysis are presented in Table 2, which shows the estimated discontinuous change in mandatory minimum convictions at Booker. Within each panel of the table, the first row (“Overall Discontinuity”) estimates the change for the whole population at Booker,while the second (“Black-White Difference Discontinuity”) estimates the Booker-relatedchange for black defendants relative to white defendants. That is, the second row measures the change in racial disparity at Booker. To see the estimated change for black defendants at Booker, one adds the estimates in the two rows.The estimated change for white defendants at Booker is simply the overall discontinuity.

We estimate regressions that include separate non-linear time trends for black and white defendants, before and after Booker—that is, we filter out both the overall underlying trends and the underlying trends in the black-white disparity. The regressions also filter out the month-to-month variation in arrest offenses and other pre-charge features of the case.179 The estimated discontinuities represent the break in the curve at Booker—that is, the difference between the intercepts of the pre-Booker curve and the post-Booker curve.

Within each panel of Table 2, the four columns show the results of multiple specifications that use different methods of fitting curves to the data—we vary the length of the time window used to estimate the curves on each side (twelve months versus eighteen months) as well as the degree of the polynomial function of time (quadratic versus cubic). There is no one “right” choice for the window or the polynomial. A result is more robust if it is consistent across specifications, which suggests that it is not just an artifact of a subjective modeling choice.

We find that as the charging date passes Booker,there is a significant, discontinuous increase in the mandatory minimum rate—but only for black defendants (Panel 1A). The estimated increase in the black-white disparity in mandatory minimums is quite large in all specifications, ranging from six to eleven percentage points, and is significant in three out of four specifications (and marginally significant in the fourth).180 Most of the increase in disparity is due to an increase for black defendants, but there also appears to be a smaller reduction in the frequency with which white defendants received mandatory minimum sentences.

Figure 2a provides an approximate visual representation of this result.181 Although the RD is estimated based on a narrower window of time surrounding Booker, the graphs show longer surrounding trends to provide context. The hollow circles and dots represent the monthly averages in the residuals for white and black defendants, respectively, from a regression on all the variables from the RD. A residual is the difference between the actual outcome observed for an individual and the outcome predicted by a multivariate regression based on other observed characteristics (for example, arrest offense). Figure 2a thus shows the trends in average black and white charges after controlling for the cases’ underlying characteristics other than race. Curves are then fitted to these monthly averages to approximate the month-to-month trends for black and white defendants, and the vertical distance between the black and white curves represents the unexplained racial disparity at any given time.

Figure 2a.

fraction of cases with a statutory minimum after accounting for defendant and case mix

The figure shows that the estimated jump in disparity after Booker is heavily influenced by the charging patterns in the first three months after Booker, especially the first month. Although there is an unexplained race gap in mandatory minimums through most of the period (the black line is above the white line), the trends had converged in the period leading up to Booker. In the month of Booker, there was a huge spike in black mandatory minimums.After the first few months, however, things seem to have reverted more or less to the previous trends. The race gap fluctuated somewhat, but the dominant background trend was a steady rise in mandatory minimums for both black and white defendants, and that trend continued.

Overall, although there is a significant break, the patterns are much less dramatic than what we saw with the overall frequency of departures (Figure 1), in which the changes were much larger and stuck. When a trend break is driven largely by a one-month anomaly, one has to wonder if it is due to chance. Here, the divergence from the trend in that one month far exceeds the noise found in the rest of the data, so we suspect that it is connected to Booker, but, nonetheless, it did not seem to last. Perhaps prosecutors responded to the immediate shock of Booker with some degree of panic and hedged their bets against a possible coming wave of Guidelines departures by charging mandatory minimums (in a pattern disparately affecting black defendants). If so, charging may have reverted to normal when prosecutors saw that Booker did not cause a major drop in sentences (as we shall see below). This, of course, is only speculation. What we do know is that, despite the significant discontinuity, Booker’s longer-term effects on charging look fairly subtle.

We next assess whether the ultimate sentence length was discontinuously affected by the charging date passing Booker—that is, did post-Booker changes in charging translate into sentencing consequences? We find only weak evidence on this point. All four specifications estimate that racial disparity in the sentence rose for cases charged immediately after Booker, with point estimates varying from four to ten months. However, the estimates are imprecise; three of the four are marginally significant (at the 0.10 level), and the fourth is insignificant. Visually, one can see the reason for the imprecision in Figure 2b: there is considerable noise in the sentence-length data, compared to which the break does not appear particularly clear.182

Figure 2b.

average prison sentence in months after accounting for defendant and case mix

2. Changes in Plea-Bargaining

We now turn to Booker’s effects on plea-bargaining, which we assess by examining what happens when the disposition date passes Booker. Specifically, we assess three outcomes: the conviction mandatory minimum, the final Guidelines offense level, and sentence length. The mandatory minimum and the offense level represent two key subjects of plea negotiations: the charge of conviction and the stipulations of sentencing facts. By assessing the effects of the conviction date on the offense level, we can separate out Booker’s effects on fact-bargaining from its effects on judicialfact-finding (which will be assessed below). We then turn to the ultimate sentencing consequences of any plea-bargaining changes.

These results can be quickly summarized: nothing dramatic happened, or at least, nothing that can be picked out from the noise of the surrounding data (Table 2, Column 2; Figures 3a-3c). Mandatory minimum rates for white defendants are in general noticeably higher after Booker than before it (Figure 3a), but that increase actually occurred several months before Booker. Prosecutors, unlike judges, were free to adapt their behavior before the Court ruled, so these changes could have been in anticipation of Booker; if so, that would mean that Booker could have increased white mandatory minimums, but too slowly for the RD analysis to detect. Booker does not appear to have had any significant discontinuouseffects on racial disparity in plea-bargaining or on plea-bargaining outcomes generally.

Figure 3a.

fraction of cases with a statutory minimum after accounting for defendant and case mix

Figure 3b.

average offense level after accounting for defendant and case mix

Figure 3c.

average prison sentence in months after accounting for defendant and case mix

3. Changes in Sentencing Fact-Finding and Sentencing Outcomes

Finally, we assess changes in judicial decision-making by examining what happens when the sentencing date passes Booker. We focus our analysis on three outcomes: departures, the final Guidelines offense level, and sentence length. Booker directly expanded judges’ legal authority to depart, and we showed in Figure 1 that this expansion had an immediate effect. In Figure 4a and Panel 3D, we break this effect down by race. We focus here on judicially initiated departures by excluding government-initiated departures for cooperating witnesses in order to examine the use of judicial discretion. The patterns are similar if one assesses all departures instead.183 The estimates all show a jump in white departure rates of five to seven percentage points and a slightly larger jump in black departure rates (eight to ten percentage points). If anything, then, black defendants may have benefited morefrom the increase in departures, but the change in black-white disparity is insignificant in most of the specifications.184 Notice that in Figure 4a, both the black and the white trends of declining departure rates after Booker are identical to the trends before it—but both curves are shifted upward. In other words, Booker’s boost to departures occurred immediately, affected black and white defendants quite similarly, and clearly had a lasting effect.

Figure 4a.

average departure rate (not government initiated) after accounting for defendant and case mix

Booker’s legal holding did not directly affect fact-finding, but it could have affected it indirectly (even setting aside any effects on plea negotiations, which our focus on the sentencing date filters out). If a judge believes the sentencing range that follows from the plea agreement is inappropriate, she has two options for altering it: she can make findings of fact that “go behind the plea” or she can depart from the Guidelines.185 Expanded authority to do the latter might make it less necessary to do the former.186

Therefore, in Panel 3B and Figure 4b, we assess whether fact-finding disparities differed in cases sentenced immediately after Booker. The results are inconclusive because the estimates are imprecise, but again, if anything, it looks as though changes in judicial decision-making after Booker cut in the direction of reducing the black-white gap. The sign of the change in disparity is negative in all four specifications (with point estimates ranging from -0.5 to -1.1 offense levels).187 The final offense level increases for white defendants in three out of four specifications, but decreases for black defendants in three out of four specifications. Note that, while Figure 4b shows a fairly clear long-termtrend of higher offense levels for white defendants, that increase cannot be safely causally attributed to Booker because RD estimates only the local effect right at the discontinuity. We return to the question of assessing long-term trends in Section III.E below.

Figure 4b.

average offense level after accounting for defendant and case mix

Finally, we look at the effect on sentence length as the sentencing date passes Booker—the inquiry that provides the most direct counterpoint to the Sentencing Commission’s claims about Booker’s effects. As Figure 4c and Panel 3C of Table 2 show, there appears to have been an immediate drop in the length of black defendants’ sentences at Booker. White sentences did not fall, however, even though white departures increased. Perhaps the increase in departures was offset by the fact-finding changes discussed above.188 Thus, there is an estimated reduction in black-white sentence disparity in cases sentenced just after Booker (by between four and fifteen months, depending on the specification). This directly contravenes the conclusion implied by the Sentencing Commission’s report. However, the contrary conclusion is only tentative. There is again considerable noise in the sentencing data, and the estimate is only significant in two of the specifications. Still, one can say that these data certainly provide no evidence of an increase in sentence disparity at Booker.

Figure 4c.

average prison sentence in months after accounting for defendant and case mix

Taking Figures 4a through 4c together, one can see that the sustained trend of increasing offense levels seen in Figure 4b may help to explain what otherwise might have been a mystery: why (as Figure 4c shows) sentences did not go down in the long run after Booker, even though downward departures went way up and stayed up (Figure 4a). The effect of the departure increase may have been canceled out by the rise in offense levels (for both black and white defendants). The magnitude of the rise in offense levels looks fairly small—perhaps half of one offense level—and one might wonder how such a subtle shift could cancel out such a large increase in departures. The answer is that although the increase in departures at Booker was a very sharp break in the prior trend, it still only affected a small percentage of cases (about 8%, according to the RD). The average size of a departure from 2005 to 2009 was twenty-nine months, so a back-of-the-envelope calculation suggests that Booker brought the average sentence down by only about 2.3 months. An increase of just one-half an offense level, applied to the average case in the sample, would raise the low end of the Guidelines range by two months, enough to cancel out most of that departure effect.

Thus, although Booker was the biggest sudden change to federal judges’ sentencing discretion since the Guidelines’ adoption, it nonetheless was perhaps less of a revolution than various observers either feared or hoped. Booker is only what federal judges make of it, and, so far, that appears not to have been much. This post-Booker stability should not be taken as especially good news for those concerned about incarceration rates for black men. If Booker does not change judicial behavior very much, then it cannot do what critics of the Guidelines hoped: substantially mitigate the Guidelines’ harshness. In the long run, sentences have continued to increase, even after controlling for shifts in the pool of offenses and offenders. And with plea levels still over 96%, prosecutors’ tremendous leverage appears to remain intact.

E. Limitations and Causal Inference Challenges

Unlike the Sentencing Commission, we find no evidence that Booker increased racial disparity in the exercise of judicial discretion; if anything it may have reduced it. The only possibly adverse effects for black defendants that we see arise from prosecutors’ shift to mandatory minimums, although that shift appears to have been temporary. Like the results of the charging study discussed in Part II, these findings cut against the case for restoring constraints on judicial discretion. Still, there are some limitations to our method. As we have already discussed, it provides only local estimates of immediate effects, rather than long-term effects. Beyond that, there are a few other things to keep in mind.

1. Limitations of the RD Method

First, it is important to understand what our RD analysis does not assess. In the charging study described in Part II, we sought to disentangle the share of the black-white gap that was explained by the disparate impact of factors such as criminal history from unexplained disparities that could represent racially disparate treatment.189 Here, in our Booker analysis, we only do that in a limited sense. We do control for the arrest offense and the other pre-charge covariates, so in that sense we are measuring changes in (apparently) “unwarranted” disparity. Controlling for those variables means that if the relative composition of the black and white defendant pools (in terms of the observable variables) changed suddenly right around Booker—either due to random or seasonal variation in crime or to reaction to Booker itself—it should not bias the results.

But the coefficients on those variables—the strength of the relationships between each of them and the outcome variable—are estimated only for the entire time period. While the trends will filter out any smooth (gradual) changes over time, they cannot filter out sharp sudden changes that coincide with Booker. We do not separately estimate, for instance, the relationship between criminal history and sentence length before and after Booker. If criminal history becomes a stronger predictor of sentence length graduallyduring the time period, the polynomial trends in our regression would filter that change out. But if the relationship between criminal history and sentence length changes suddenlyat Booker—if Booker changes it—our method will not filter out that change.

In effect, what that means is that we are focused on the question, “Did Booker change racial disparity patterns in charging, plea-bargaining, and sentencing?” rather than “Why did Booker change those patterns?” If, for instance, prosecutors started using mandatory minimums more against black defendants, this need not have been motivated by race—it could have been motivated by wanting to crack down on gun crimes, for instance. In short, we are estimating Booker’s racially disparate impacts. We do not filter out the share of those impacts that are mediated by other variables—not just because doing so is impractical with our method but also because it is undesirable. If policymakers care about the effects of sentencing reform on black incarceration rates, filtering out everything that is not racially motivated would not convey those consequences fully. Together, the results of the study described in Part II and our Booker results in this Part present a fairly rich picture of the static factors (case features) and dynamic factors (sentencing law reform) that contribute to outcomes at each procedural stage.

Second, while RD effectively filters out long-term trends, it is vulnerable to statistical noise that might generate false positives. If the graph is sufficiently noisy, one might be able to see discontinuities at lots of points. Of course, Booker need not have been the only shift over the course of the study period to be a real shift. But if there are frequent breaks, even at points where there are no known triggering events, then not much can be made of finding a break at Booker as well.

We think that with appropriately cautious interpretation, this is not such a serious problem—far less serious than the causal inference problem that pervades other studies. This is why we fit the monthly trends with multiple kinds of functions and do not put stock in an apparent discontinuity that appears only in one version. It is why we do not use even higher-order polynomials, which would likely over-fit the data. It is also why the graphs matter, perhaps more than the numbers. If a discontinuity cannot be picked out with the eye—or if it looks no different from many other unexplained breaks—then it is probably nothing to write home about.

As an additional precaution, we conducted placebo tests on every outcome variable, re-running all of the analyses shown in Table 2, except applied to twelve other arbitrary breaking points across the study period.190 We deemed the results of these tests “false positives” when, at the breaking point in question, a significant discontinuity appeared in more than one out of the four model specifications. These tests were reasonably reassuring. In the mandatory minimum variable, when the placebo tests were run by charging date or by disposition date, there were false positives at just one out of twelve of these breaking points; when the tests were run by sentencing date, there were no false positives. This makes us more confident that the spike in cases in which mandatory minimum offenses were charged just after Booker—although brief—was likely something real, because this variable is not particularly noisy. The sentence length variable was visibly noisier in the graphs and unsurprisingly had more false positives in the placebo tests: just one when the placebos were run by charging month, but four when run by disposition month or by sentence month. In the offense level variable, there were two false positives when the placebos were run by charging month or by disposition month, and one when they were run by sentence month. The departure variable had two false positives (run by sentencing month), but visual inspection makes clear that Booker was by far the cleanest break in the study period.191

2. Blakely and Anticipation of Booker

Finally, we return to the question of Blakely and anticipation of Booker. Blakely is marked with a dotted line in the figures, and we also repeated all the numeric analyses on it. There are no apparent breaks in departures, offense level, or sentence length when the sentencing date passes Blakely (Figures 4a-4c). It appears that the courts included in these analyses really did follow the “business as usual rule.”

But what about prosecutors? As to plea-bargaining, we find no evidence of discontinuous changes caused by Blakely in the “business as usual” circuits. When time trends are estimated based on the dispositionmonth, severity on all measures (mandatory minimum rates, offense levels, and the ultimate sentence) looks relatively low during the first two months after Blakely, especially for white defendants (Figures 3a-3c). One might wonder whether this is because Blakely increased defendants’ plea-bargaining leverage.192But a downward trend in these severity measures had already been underway for at least six months before Blakely, and the post-Blakely months do not represent a significant break from that trend. Moreover, the downward trend turns around again by the third month after Blakely. In short, while there are some trend fluctuations when the outcome variables are graphed by disposition date, they do not seem connected to Blakely (or Booker, as discussed above).

The one thing that does look like it changed discontinuously after Blakely is disparity in mandatory minimums, which declined (Figure 2a). The reduction consists mostly of a rise in mandatory minimums for white defendants and is concentrated in drug cases. For cases charged during the whole six-month period between Blakely and Booker, the black-white gap in mandatory minimums looks quite small, until it jumped in the month of Booker. This is another potential reason not to make too much of the spike in charging disparity at Booker—in addition to being temporary, it could have been partly the result of the disparity being anomalously smallduring the Blakely-to-Booker period. Also, changes in charging disparity around Blakely might affect the interpretation of our analysis of changes in pleabargaining or sentencing after Booker (since the same cases could be charged near Blakely and then either plea-bargained or sentenced near Booker).

However, there are two reasons we believe the post-Blakely change in mandatory minimum disparity does not pose a serious problem for our interpretation of the Booker results. First, the mandatory minimum changes after Blakely (unlike those we observed after Booker)did not translate into discontinuous changes in sentence disparity in cases charged after Blakely (Figure 2b). Further analysis suggests that this is because the increase in the presence of mandatory minimums in white defendants’ cases was offset by an increase in waivers of those mandatory minimums under the “safety valve” exception that applies in some drug cases.193 The subset of cases in which mandatory minimum charging patterns changed after Blakely were drug cases that were safety-valve eligible, meaning that the mandatory minimum is less consequential than usual.194

Second, the time between each key date in a case varies considerably. For instance, it is not as though all of the cases charged in the month after Blakely were sentenced in the month right after Booker. Rather, from one sentencing month to the next, there is a gradual increase and then a gradual decrease in the probability of the case having been charged right after Blakely. In other words, whatever effect changes in charging after Blakely had on sentencing should be part of the continuous polynomial trends that the RD filters out. To substantially affect the discontinuity estimates at Booker, the probability of having been a post-Blakely case would have to have plunged suddenly in the month of Booker.This is a substantial advantage of RD over other methods.195

A final concern about the interregnum period is that some cases could have been delayed until after Booker, such that the cases immediately after Booker would not have the same characteristics as those immediately before it. Such manipulation could pose a threat to identification using RD. Fortunately, it is not the case that any manipulation of timing is fatal to causal inference. As David Lee and Thomas Lemieux explain, “If individuals—even while having some influence—are unable to precisely manipulate the assignment variable, a consequence of this is that the variation in treatment near the threshold is randomized as though from a randomized experiment.”196 The non-manipulation assumption is thus relatively modest—it only requires that cases sentenced very near Booker were not subject to the court’s precise manipulation of which side of the line they fell on. If a court merely took steps to make it more likely that a case would be sentenced after Booker, such as scheduling the sentencing hearing for a faraway date, this would not be seriously problematic. The scheduling would have gotten the case near Booker, but there would still have been a chance element determining which side it landed on. This chance element is amplified by the fact that nobody knew when the Supreme Court would rule: legal observers performed terribly at predicting Booker’s release, with many predicting a very fast decision after the October argument.197 In addition, sentencing hearings are scheduled months in advance so as to allow the Probation Office time to complete the pre-sentence investigation report and to allow the parties time to prepare (and to arrange for the presence of witnesses in some cases). This delay makes it especially difficult to precisely manipulate the timing of a case relative to a Supreme Court decision.

Still, we analyzed the number and characteristics of cases on either side of Booker, looking for any evidence of manipulation. We found none. The number of cases sentenced in December 2004 was 1679; the number in January 2005 was 1682. If sentencings were being delayed, one would expect the mean elapsed time since the plea to be greater for cases after Booker, but in fact, the mean elapsed timeswere nearly identical (indeed, very slightly shorter after Booker): 3.99 months before versus 3.96 months after. The breakdowns by race and crime category were likewise essentially identical before and after.198 If anything, there may have been some delaying of cases in November 2004 when 1566 cases were sentenced, the lowest volume that year. Expectations of an early Booker decision were high during November 2004,199 but the dip was small, and it appears the counts went back to normal once the Court did not release its decision quickly. After Booker, the number of cases also stayed normal; it was slightly higher in March (when 1825 cases were sentenced), but this was lower than four other months in 2004 and 2005. In short, there is very good reason to believe that the courts in the circuits included in our analyses really did conduct “business as usual,” or at least that any manipulations were too imprecise to threaten RD’s assumption of effective randomness in the immediate vicinity of the discontinuity.200

Conclusion

Determining the causes of racial disparities in criminal justice is not easy. We believe our approach improves substantially on existing research, but we do not offer definitive answers and doubt that anyone will soon. So what are policymakers to do? We do not seek to answer that question completely. Even if we had crystalline empirical answers, criminal justice policy does not turn on demographic disparity alone—many competing objectives must be considered. That said, our results have implications for these dilemmas, and we fear that the contrary results of existing research may be distorted to support counterproductive “solutions” to racial disparities. We close with some brief thoughts on these points.

First, despite our concerns about the methods of the Sentencing Commission and others, we agree that the high rate of incarceration of black men is a serious social problem and that examining the possible contribution of disparities in the criminal justice system is important. Our research suggests that, in the federal system, disparities in the post-arrest justice process contribute to this problem. After controlling for the arrest offense, criminal history, and other prior characteristics, sentences for black male arrestees diverge substantially from those of white male arrestees (by around 10% on average). While this disparity does not seem to be growing, it is persistent.

Second, the procedural source of this disparity matters, and it is thus a mistake to focus on judicial sentencing alone. Our research suggests that racial disparities in recent years have been largely driven by the cases in which judges have the least sentencing discretion: those with mandatory minimums. Our assessment of Booker is more tentative, but we find no evidence that it increased racial disparity. The Sentencing Commission’s contrary conclusion is based on deeply flawed methods.

For these reasons, we are particularly concerned about proposals to respond to sentencing disparities by restoring tighter constraints on sentencing, especially those that entail expanding mandatory minimums.201 Our results suggest that this would not reduce disparities in the justice process. Quite the contrary: we find that prosecutors file mandatory minimums twice as often against black men as against comparable white men. Moreover, for those concerned about mass incarceration of black men, expanding mandatory minimums would be counterproductive. Even setting aside racial disparities internal to the criminal justice system, sentencing law changes that increase severity have a particularly adverse impact on black men, who are disproportionately involved in the system in the first place. Making sentencing law more rigid would likely exacerbate this problem even if it led to more equitable administration of the law—and our results suggest that it would likely lead to less equitable administration.

Third, we do not advocate attempting to reduce disparity by taking discretion away from prosecutors. Eliminating prosecutorial discretion is probably impossible. The Department of Justice has certainly tried. The disparities we found persisted despite the Ashcroft Memo ordering prosecutors to charge and pursue the “most serious, readily provable offense,” as well as DOJ bans on fact-bargaining.202 Taken at their word, these policies would have stripped almost all discretion from line prosecutors. But such policies are very difficult to enforce, because line prosecutors inevitably must subjectively evaluate the available evidence.203 And even if constraining prosecutorial discretion did succeed, one might see another “hydraulic” effect. If prosecutors had to pursue every case law enforcement brought them to the fullest, their current power over case outcomes might shift another step back—to law enforcement, where it might be even harder to monitor. Prosecutors’ decision-making is notoriously difficult to observe—unlike judges, they do not publish written reasoning. But law enforcement is even more of a “black box.”

Even if all discretion could somehow be removed from the justice system, we doubt this would create a justice system anybody would want. Flexibility allows appropriate tailoring of both charges and sentences to the circumstances of individual cases, so as to avoid unduly harsh punishments when they are not justified. Efforts to eliminate unwarranted disparities are important, but they should not come at the cost of unwarranted uniformity. Instead, rather than looking for ways to curtail prosecutorial discretion, legislators could consider curtailing prosecutorial power by dialing back existing mandatory minimums. If sentencing laws were less rigid, it would be less necessary for decision-makers to find ad hoc means of mitigating their impact. The Fair Sentencing Act of 2010, which reduced crack sentences, showed that it is politically possible to reform excessive sentencing laws, and that empirical evidence of racial disparities can help to bring such changes about.204

One potential next focus could be the severe gun enhancements in 18 U.S.C. § 924(c). These laws hit black men particularly hard because, as our data show, they are more frequently arrested for gun crimes andbecause of large apparent disparities in prosecutors’ exercise of charging discretion. Certainly, policymakers must weigh this problem against concerns about gun violence. Notwithstanding these serious concerns, we wonder whether the mandatory minimums in the statute are truly alwaysnecessary, such that judicial discretion should be precluded. For instance, is a five-year add-on sentence really necessary in every case in which a firearm has merely been carried—let alone a mandatory extra twenty-five years for a second gun and yet another twenty-five for a third?205 Prosecutors would likely feel less need to “swallow a gun” if the gun did not automatically trigger a massive additional penalty.

Finally, while our approach is far more comprehensive than that of prior sentencing studies, there is enormous room for further exploration. For instance, we plan to explore further the possible role of sentencing fact-finding in producing racial disparities. More research is also necessary to see whether patterns like those we found are also present in state courts. More generally, we do not claim to have proven purposeful discrimination by prosecutors or anyone else—it would be impossible to do so with administrative data like ours. Other kinds of studies may be necessary to dig deeper into causal theories for racial disparities: perhaps experimental studies in which race is randomly assigned to otherwise identical prosecutor files, or qualitative studies involving reviews of case files and interviews.206 DOJ itself is well positioned to carry out such work. One easy step would be for DOJ to keep statistics on mandatory minimum charging decisions by race when it tracks prosecutors’ performance. Doing so would not only facilitate research but could also help prosecutors who do not want to contribute to disparities but might not be conscious of them. The government itself should take the elimination of disparities in criminal justice as seriously as other civil rights enforcement matters, and it should think creatively about solutions and strategies for answering the empirical questions that remain.