MEASURING INTERJUDGE SENTENCING
DISPARITY: BEFORE AND AFTER THE FEDERAL
SENTENCING GUIDELINES*
JAMES M. ANDERSON,
Defender Association
of Philadelphia

JEFFREY R. KLING,
Princeton University
and National
Bureau of
Economic Research

and
KATE STITH
Yale Law School

Abstract
This paper evaluates the impact of the Federal Sentencing Guidelines on interjudge sentencing disparity, which is defined as the differences in average nominal prison sentence lengths for comparable caseloads assigned to different judges.
This disparity is measured as the dispersion of a random effect in a zero-inflated
negative binomial model. The results show that the expected difference between
two typical judges in the average sentence length was about 17 percent (or 4.9
months) in 1986–87 prior to the Guidelines and fell to about 11 percent (or 3.9
months) in 1988–93 during the early years of the Guidelines. We have not sought
to measure the effect of parole in the pre-Guidelines period, other sources of disparity such as prosecutorial discretion, or the proportionality of punishment under the
Guidelines as compared with the pre-Guidelines era.

I. Introduction

O

ne of the chief objectives of the Sentencing Reform Act of 19841 was
to reduce sentencing disparity among similar offenders. The act described
* Assistance in data production was generously provided by Ralph Mecham, Steve Schelsinger, and Cathy Whitaker at the Administrative Office of the U.S. Courts. Helpful comments were made by participants in the conference sponsored by the John M. Olin Program
in Law and Economics at which an earlier version of this article was presented, and at various
stages of the project by Daron Acemoglu, Josh Angrist, Jushan Bai, Katherine Brownlee,
José Cabranes, Gary Chamberlain, Ken Chay, Peter Diamond, Hugh Eastwood, Dan Freed,
Jerry Hausman, Bo Honoré, Larry Katz, Kara Kling, David Lee, Steve Levitt, Jeff Liebman,
John Lott, Whitney Newey, Abigail Payne, Anne Peihl, Steve Pischke, Jack Porter, and Jim
Poterba. Kling acknowledges financial support from a National Science Foundation Graduate
Fellowship and an Alfred P. Sloan Doctoral Dissertation Fellowship.
1
Sentencing Reform Act of 1984, 28 U.S.C. § 991(b) (1988).
[Journal of Law and Economics, vol. XLII (April 1999)]
 1999 by The University of Chicago. All rights reserved. 0022-2186/99/4201-0011$01.50

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this purpose as ‘‘avoiding unwarranted disparities among defendants with
similar records who have been found guilty of similar criminal conduct.’’ 2
Both the act and its legislative history demonstrate that Congress’s overriding concern was to reduce disparity thought to result from the exercise of
judicial discretion in sentencing. The act was sponsored and shepherded
through Congress by an unusual coalition of liberals and conservatives. Liberals expressed particular concern that permitting the exercise of discretion
compromised the ideal of equal treatment under the law, while conservatives were concerned as well with perceived undue leniency in sentencing.3
To accomplish these ends, the act created the United States Sentencing
Commission to develop federal Sentencing Guidelines. As the associate attorney general wrote to the first chairman of the commission,‘‘Simply
stated, unwarranted disparity caused by broad judicial discretion is the ill
that the Sentencing Reform Act seeks to cure.’’ 4 The commission’s Sentencing Guidelines, which became effective on November 1, 1987, restrict
the exercise of judicial discretion to a narrow sentencing range in each case
and limit judicial departures from that range. The sentencing ranges of the
Guidelines are a small percentage of the statutory ranges 5 that were available to judges in the pre-Guidelines era; it was presumably hoped that sentencing disparity would be reduced commensurately.
This paper examines the impact of the Guidelines on one particular type
of disparity: interjudge disparity in the average length of prison sentences
of criminal defendants in federal district courts. After a brief review of the
Guidelines and the mechanisms through which they may affect disparity,
we explore methods of measuring interjudge disparity.
Using the fact that cases are randomly assigned to judges in many districts, we define interjudge disparity as relative differences in the average
2
See also 28 U.S.C. § 994(f ) (1988) (‘‘The Commission, in promulgating guidelines pursuant to subsection (a) (1), shall promote the purposes set forth in section 991 (b) (1), with
particular attention to the requirements of subsection 991 (b) (1) (B) for providing certainty
and fairness in sentencing and reducing unwarranted disparities’’).
3
See generally Kate Stith & José A. Cabranes, Fear of Judging: Sentencing Guidelines in
the Federal Courts 38–48 (1998).
4
Stephen S. Trott, Letter to Hon. William W. Wilkins (April 7, 1987). The letter from
Trott (who was associate attorney general writing on behalf of the Department of Justice) to
Wilkins (who was the first chairman of the Sentencing Commission) urged adoption of sentencing guidelines that would permit only narrow judicial discretion; the letter is reprinted at
8 Fed. Sentencing Rep. 196 (1995). See also 8 Fed. Sentencing Rep. 199 (1995) (reprinting
letter dated November 9, 1994, from Judge Stephen S. Trott to the new chairman of the Sentencing Commission, explaining that experience under the Guidelines had caused him to conclude that ‘‘the cure is worse than the disease’’).
5
Before the passage of the Guidelines, these ranges were the only statutory upward bound
on sentencing. Under the Guidelines, they continue to serve as a upward bound on the possible length of a sentence—even if the Guidelines would otherwise mandate a longer sentence.

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sentence length for otherwise comparable caseloads of defendants assigned
to different judges in the same district. We compare estimates of interjudge
disparity before and after implementation of the Guidelines.6 In our preferred specification, the dispersion in the judge’s effect on sentence length
is represented by the variance of a judge-specific random variable in a statistical model of prison sentence length. Existing econometric random effects models for count data (such as the number of months of prison sentence length) are extended in several ways. A zero-inflated negative
binomial model is developed in order to account explicitly for the fact that
many cases end in dismissal or acquittal or have a sentence that involves
no prison time at all. A parametric model of the random effect allows the
judge effects to be correlated over time and allows a convenient interpretation of the dispersion in terms of a Gini coefficient—or twice the expected
absolute difference in sentence length between two judges in the same district office relative to the office mean.
While noting that other kinds of disparity may have been exacerbated by
the Guidelines and there may be unwarranted uniformity in sentencing under the Guidelines, we conclude that interjudge disparity in nominal sentencing is less pronounced in the Guidelines era than it was in the era of
discretionary sentencing.
II. Defining Interjudge Disparity
The enabling legislation and legislative history of the Sentencing Reform
Act refer to reducing unwarranted disparity as ‘‘the major premise of the
sentencing guidelines.’’ 7 Neither in statute nor legislative history did Congress define or explain what constituted ‘‘unwarranted disparities among
defendants with similar records, who have been found guilty of similar
criminal conduct.’’ 8 As the Senate Report accompanying the Sentencing
Reform Act noted, ‘‘The key word in discussing unwarranted sentence disparities is ‘unwarranted.’ ’’ 9
To avoid confusion, we distinguish between three distinct types of sentencing variation: proportionality, disproportionality, and disparity. Proportionality, under our definition, is sentencing variation among a set of deci6
The post-Guidelines era differs from the pre-Guidelines era in two significant respects:
the Guidelines themselves (which apply to all crimes committed after November 1, 1987)
and statutory minimum sentences (which Congress has enacted with regularity since the mid1980s and which apply to a significant portion of federal prosecutions).
7
S. Rep. No. 225, 98th Cong., 1st Sess. 52 (1984), reprinted in 1984 U.S.C.C.A.N. 3182,
at 3235.
8
28 U.S.C. § 991(b)(a)(B).
9
S. Rep. No. 225, supra note 7, at 161, reprinted in 1984 U.S.C.C.A.N. 3344.

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sion makers in the criminal justice system that is justified by relevant
differences among offenders and their crimes. Conventionally, these differences include various characteristics of the criminal offense (such as the
amount of harm caused) and of the criminal offender (such as prior criminal
record). Its converse, disproportionality, is any variation in sentencing outcomes for a given set of decision makers that is not attributable to relevant
sentencing factors; in this sense, disproportional variation is akin to what
many previous commentators have referred to as disparity. In contrast, we
define disparity as variation in sentencing between the sets of hypothetical
decision makers that could potentially be involved in the disposition of an
offender’s case. Under this approach, disparity can be thought of as the
variation in sentence that would result if a single offender were processed
through the criminal justice system by every possible combination of sentencing decision makers.
Our definition of disparity is centered on the sentencing decision maker
rather than on characteristics of the offense or the offender. Thus, for example, the fact that sentences for equal amounts of crack cocaine and powdered cocaine are dissimilar is not disparity under our definition. The crack/
powder difference is either proportional variation or disproportional variation, depending on one’s judgment as to whether the difference in the type
of cocaine is relevant to the proper amount of criminal punishment. Similarly, some have argued that the Sentencing Guidelines may have increased
overall penalty variation among offenders because, before the passage of
the Guidelines, judges could consider the reputational consequences and the
loss of potential earnings suffered by white-collar offenders.10 Under our
definition, this type of variation is not ‘‘disparity.’’ It is, rather, a form of
disproportionality (or proportionality, depending upon one’s views about
whether reputational and earnings consequences should be considered by
sentencing judges). We have adopted a definition of ‘‘disparity’’ that considers solely that variation caused by the identity of the decision maker; the
concern about ‘‘white-collar inequity,’’ on the other hand, refers to variation in total punishment among different classes of offenders. The definitions of disparity, proportionality, and disproportionality that we have
adopted permit us to distinguish variation that is attributable to the identity
10
John R. Lott, Jr., Do We Punish High Income Criminals Too Heavily? 30 Econ. Inquiry
583 (1992); Jonathan M. Karpoff & John R. Lott, Jr., Why the Commission’s Corporate
Guidelines May Create Disparity, 3 Fed. Sentencing Rep. 140 (1990). For example, Karpoff
and Lott argue that the market imposes significant penalties on corporate and white-collar
offenders that are not accounted for under the Guidelines. These critics argue that the Guidelines increase ‘‘disparity’’ because judges, hamstrung by the Guidelines, are unable to equalize total punishment (including reputational sanctions) among equally culpable offenders.

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of the decision makers in the criminal justice system from variation in sentences based on differences between criminal cases (that may or may not
be justified depending on one’s theory of the purposes of sentencing).
We measure only interjudge disparity and do not attempt to gauge potential disparity at other stages in the sentencing process or potential disproportionality. We limit our inquiry for several reasons. First, the difficulties are
formidable in rigorously measuring disparity in other stages in the process,
despite its likely presence.11 Second, in focusing on the variation attributable only to disparity between judges rather than on disproportionality we
avoid the inevitably contentious issue of the purpose of sentencing itself.
Finally, interjudge sentencing disparity has generated more concern than
disparity at any other stage of the sentencing process.
Concern about interjudge sentencing disparity is not hard to understand.
Attorney General Robert H. Jackson pithily expressed the intuitive unfairness of interjudge disparity: ‘‘It is obviously repugnant to one’s sense
of justice that the judgment meted out to an offender should depend in large
part on a purely fortuitous circumstance; namely the personality of the particular judge before whom the case happens to come for disposition.’’ 12
Prior to the promulgation of the Sentencing Guidelines, a federal judge’s
sentencing discretion was enormous and virtually unreviewable. As the last
actor in the determination of the offender’s formal sentence, the judge was
in a position either to remedy or to exacerbate any disparity in the earlier
stages of criminal prosecution. In addition, the judge has by far the most
visible role in the sentencing process, formally announcing the polity’s exaction of punishment. Variation in law enforcement, charging, and probation practices are far less visible.
By the early 1970s, considerable intellectual enthusiasm for the idea of
reducing sentencing disparity developed as part of a wave of general efforts
to attack indeterminate sentencing.13 The theory that punishment was designed to rehabilitate the offender had become discredited, and both parole
and interjudge disparity came under attack. Perhaps the most influential
11
Under our definition, disparity may exist in law enforcement, prosecution, probation,
and parole stages of criminal justice system. For example, one prosecutor may charge a defendant in such a way that he would face a mandatory minimum of 10 years, while another
prosecutor would prosecute that same defendant in a way that would result in a sentence of
5 years. Law enforcement disparity may involve the manner of investigation, such as the
amount of drugs offered in a reverse sting. Probation officers may take different approaches
to presentence reports and may implement parole policies differently.
12
U.S. Attorney General, Annual Report 5–6 (1940).
13
See Andrew von Hirsch, Doing Justice (1976); Norval Morris, The Future of Imprisonment (1974); Kenneth Culp Davis, Discretionary Justice (1969).

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critic of judicial sentencing discretion was Marvin E. Frankel, himself a distinguished judge in the Southern District of New York.14 Frankel argued
that the range of choice provided to the sentencing judge was ‘‘terrifying
and intolerable for a society that professes devotion to the rule of law’’ and
that it should be ‘‘unthinkable in a ‘government of law, not of men.’ ’’ 15 He
wrote, ‘‘[I]ndividualized justice is prima facie at war with such concepts, at
least as fundamental, as equality, objectivity, and consistency in the law.’’ 16
Frankel’s anecdotal arguments appeared to be confirmed by an experimental study that he helped to organize in the district courts comprising the
Second Circuit. The organizers of the study distributed identical presentence reports to 50 district court judges; each judge was asked to impose
sentences for each case. Sentencing ranges varied widely, in one case from
20 years in prison and a $65,000 fine from the most severe judge to 3 years
in prison from the most lenient judge. Moreover, the disparity was not attributable to either a handful of judges or outliers in each case but appeared
throughout the range of sentences.17
The Second Circuit study’s finding of substantial sentencing disparity
was repeated in other studies.18 Commentators also cited prison unrest 19 and
racial and class discrimination 20 as problems deriving from the exercise of
14
Marvin Frankel, Lawlessness in Sentencing, 41 U. Cin. L. Rev. 1 (1972); Marvin Frankel, Criminal Sentences: Law without Order (1973).
15
Frankel, Criminal Sentences, supra note 14, at 5.
16
Id. at 10.
17
Anthony Partridge & William B. Eldridge, The Second Circuit Sentencing Study: A
Report to the Judges 1–3, 9 (1974). The study also noted that neither experience with the
Eastern District of New York’s practice of sentencing councils—whereby a judge confers
with two other judges before sentencing—nor time on the bench seemed to increase the likelihood that a particular judge’s sentence would be consistent with that of her colleagues.
18
See William Austin & Thomas A. Williams III, A Survey of Judges’ Responses to Simulated Legal Cases: Research Note on Sentencing Disparity, 68 J. Crim. L. & Criminology
306 (1977) (47 district court judges reviewed and sentenced five hypothetical cases; wide
disparity in sentence lengths noted); Whitney North Seymour, 1972 Sentencing Study for the
Southern District of New York, 45 N.Y. St. B. J. 163 (noting gross sentencing variations in
actual cases, not controlling for particular case attributes); Beverly Blair Cook, Sentencing
Behavior of Federal Judges: Draft Cases, 42 U. Cin. L. Rev. 597 (1973).
19
Sentence disparity was thought to increase prison unrest. James V. Bennett, a former
director of the Federal Bureau of Prisons, explained: ‘‘The prisoner who must serve his excessively long sentence with other prisoners who receive relatively mild sentences under the
same circumstances cannot be expected to accept his situation with equanimity. The more
fortunate prisoners do not attribute their luck to a sense of fairness on the part of the law but
to its whimsies. The existence of such disparities is among the major causes of prison riots,
and it is one of the reasons why prisons so often fail to bring about an improvement in the
social attitudes of their charges.’’ J. Bennett, Of Prisons and Justice, S. Doc. No. 70, 88th
Cong., 2d Sess. 319 (1964).
20
Joseph C. Howard, Racial Discrimination in Sentencing, 59 Judicature 121 (1975–76);
Tom Wicker, Judging the Judges, N.Y. Times, February 6, 1976, at A29; Alec Hopkins, Is

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judicial discretion in sentencing. Critics from the political Right expressed
dissatisfaction with the perceived leniency of sentencing judges and parole
officials.21 Both liberals and conservatives argued that sentencing disparity
compromised the ideal of equal treatment under law. By the early 1980s,
there had developed across the ideological spectrum a consensus that dramatic changes in the sentencing process were needed to reduce sentencing
disparity stemming from the exercise of judicial discretion.
III.

Guidelines as a Mechanism for Reducing
Interjudge Disparity

The result of this political consensus was the enactment of the Sentencing Reform Act of 1984. The primary sponsors of the legislation were Senator Edward M. Kennedy, the liberal Massachusetts Democrat, and Senator
Strom Thurmond, the conservative North Carolina Republican; President
Reagan hailed the bill when he signed it in October of 1984.
The act created a Sentencing Commission charged with developing and
implementing a system of binding Sentencing Guidelines. At the same time,
beginning in the mid-1980s, Congress enacted a series of laws that mandated high minimum sentences for certain crimes—including for nearly all
narcotics offenses, which now constitute some 40 percent of all prosecutions in federal court. The Sentencing Reform Act itself also contained a
variety of mandates, such as the requirement that repeat offenders receive
sentences ‘‘at or near’’ the statutory maximum, which have also contributed
to a substantial increase in the overall severity of federal criminal sentences.
The centerpiece of the Guidelines is a grid containing 258 boxes (termed
the ‘‘Sentencing Table’’). The grid’s horizontal axis (‘‘Criminal History
Category’’) adjusts severity on the basis of the offender’s past conviction
record. The vertical axis (‘‘Offense Level’’) reflects a base severity score
for the crime committed, as further adjusted for those aspects of the crime
that the Guidelines deem relevant to sentencing. The Guidelines, through
a complex set of rules requiring significant expertise to apply, instruct the
There a Class Bias in Criminal Sentencing? 42 Am. Soc. Rev. 176, 176–77 (1977); Frankel,
Criminal Sentences, supra note 14, at 23–24.
21
See Jonathan D. Casper, Determinant Sentencing and Prison Crowding in Illinois, 1984
U. Ill. L. Rev. 231, 236–37 (explaining that ‘‘[c]onservatives and law enforcement interests’’
desired determinate sentencing because ‘‘parole boards seemed often to release prisoners
who continued to pose a danger to society’’ and judges seemed ‘‘reluctant to send ‘marginal
defendants’ to prison’’); J. Edgar Hoover, The Dire Consequences of the Premature Release
of Dangerous Criminals through Probation and Parole, 27 F.B.I. L. Enforcement Bull. 1
(1958); see also Reform of the Federal Criminal Laws: Hearings on S. 1437 before the Subcommittee on Criminal Laws and Procedures of the Senate Committee on the Judiciary 95th
Cong., 1st Sess., 8580, 8995 (1977) (statements of Sen. Lloyd Bentsen and Ronald L.
Gainer).

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sentencing judge on how to calculate both ‘‘Criminal History Category’’
and ‘‘Offense Level.’’ The box at which these two factors intersect then
determines the range within which the judge may sentence the defendant.
As required by the Sentencing Reform Act,22 the sentencing range in each
box is small, the highest point being 25 percent more than the bottom point.
This 25 percent range represents one source of discretion retained by judges
under the Guidelines.
The only other form of lawful sentencing discretion is authority to ‘‘depart’’ from the Guidelines. This authority is formally limited, however, to
two circumstances. The first is that in which the defendant has provided
substantial assistance in the prosecution of others,23 in which event the
judge may pronounce a sentence that departs downward from the Guideline
range—with the important caveat that the prosecutor must first agree, in the
words of the Supreme Court, to ‘‘authoriz[e] the district court to depart.’’ 24
If the prosecutor does make the appropriate motion for departure, the court
may depart below not only the Guidelines range but also below any applicable statutory minimum sentence.25 The second situation in which a judge
may depart, up or down, from the Guideline range is where the judge is
able to demonstrate on the record that there are factors or circumstances
present in the case at hand that have not been ‘‘adequately’’ factored into
the Guidelines’ sentencing rules by the commission and make the case
‘‘atypical.’’ The Sentencing Commission has admonished that it expects the
exercise of this departure power to be ‘‘rare.’’ 26
In a 1996 survey, however, 73 percent of district judges indicated that

22

28 U.S.C. § 994(b)(2).
Substantial Assistance to Authorities (Policy Statement) U.S.S.G. § 5K1.1; see also 28
U.S.C. § 994(m).
24
Melendez v. United States, 116 S. Ct. 2057, 2061 (1996).
25
See Limited Authority to Impose a Sentence below a Statutory Minimum 18 U.S.C.
3553(e).
26
Grounds for Departure (Policy Statement) U.S.S.G. § 5K2.0. The Sentencing Guidelines
themselves also identify a few, preferred bases for departure; for example, the instructions
on calculation of the defendant’s criminal history ‘‘score’’ advise that the judge should depart
up or down depending upon whether the defendant’s record of convictions overestimates or
underestimates his criminal history. In Koon v. United States, 518 U.S. 81, 116 S. Ct. 2035
(1996), the U.S. Supreme Court held that federal courts of appeals should generally review
the decision of the district judge to depart from the Guidelines under an abuse of discretion
standard, rather than review the district court’s application of the sentencing guidelines de
novo. The Court also noted, ‘‘We do not understand it to have been the congressional purpose [for the Guidelines] to withdraw all sentencing discretion from the United States District
Judge. Discretion is reserved within the Sentencing Guidelines, and reflected by the standard
of appellate review that we adopt.’’ Id. at 2053. It will be interesting to see whether this
decision leads to an increase in departures and/or interjudge sentencing disparity in the future.
23

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they felt mandatory guidelines were not necessary to direct the sentencing
process, and ‘‘they strongly prefer a system in which judges are accorded
more discretion than they are under the current guidelines.’’ 27 In recent
years, judges have departed downward on the basis of substantial assistance
to authority in nearly 20 percent of all cases sentenced under the Guidelines
and have departed (upward or downward) due to ‘‘atypicality’’ in another
10–12 percent of cases.28 In many other cases, the defense and the prosecution stipulate to the ‘‘facts’’ that are relevant to sentencing under the Guidelines or stipulate even to a particular Guideline sentencing range; in these
cases, there may be no departure as a formal matter, but it may be difficult
to determine whether the Guidelines have been faithfully implemented.29
For these various reasons, the ultimate ability of the Guidelines to control
interjudge disparity is an open question.
IV.

Measuring Changes in Disparity

As we have noted, our definition of disparity is centered on the sentencing decision maker rather than on characteristics of the offense or the offender. In order to measure interjudge disparity as we have defined it, one
must observe the sentencing outcomes of similar cases assigned to different
judges. Previous researchers have attempted to do this in three main ways.
First, simulated cases with a common set of facts have been distributed
to judges who then provide a sentence. The influential Second Circuit sentencing study, and a similar study conducted nearly a decade later by the
U.S. Department of Justice (1981),30 used this approach. It is quite difficult,
however, for a simulation to reconstruct the full depth of information available to a judge in a real case. Moreover, there is no assurance that judges

27
Molly Treadway Johnson & Scott Gilbert, The U.S. Sentencing Guidelines: Results of
the Federal Judicial Center’s 1996 Survey (1997). Earlier surveys of federal judges had indicated even less satisfaction with the Guidelines. See Don J. DeBenedictis, The Verdict Is In,
79 A.B.A. J. 78 (1993) (reporting that in poll conducted by ABA, nearly half of federal
judges wanted to completely abolish the Guidelines). As one of the present authors has noted,
over half of all active federal judges were appointed since the Guidelines went into effect,
and these judges may be more satisfied with the Guidelines than judges who were appointed
in the era of discretionary sentencing. See Stith & Cabranes, supra note 4, at 5–6, 143–44.
28
See U.S.S.C., Sourcebook of Federal Sentencing Statistics 39 (1997) (showing also that
use of substantial assistance departures has increased markedly over time, from less than 5
percent in 1989 to nearly 20 percent in 1994, 1995, and 1996).
29
See Francesca D. Bowman, Probation Officers Advisory Group Survey, 8 Fed. Sentencing Rep. 303 (1996) (chief probation officers in two-thirds of federal districts responding to
survey report that pleas of guilty are often accompanied by an agreement that includes Guideline stipulations or calculations).
30
John Bartolomeo et al., Sentence Decision-Making: The Logic of Sentence Decisions
and the Extent and Sources of Sentence Disparity (1981).

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approach simulation studies with the seriousness and deliberation that they
would bring to a real case with a real defendant and real victims.31
Second, the variation among cases with common observable characteristics has been measured, with the residual variation among these observable
similar cases attributed to the judges. A fundamental problem with this type
of analysis is the difficulty in distinguishing between disparity, disproportionality, and proportionality.32 A 1991 study by the Sentencing Commission, for instance, compared similar cases from a pre-Guidelines year
(1985) and a post-Guidelines period of 2 years (1989–90).33 The analysis
conducted by the commission compared the range of sentences and mean
sentence for each of these categories under the Guidelines to corresponding
measures from the pre-Guidelines period. The evaluation categorized cases
according to factors deemed relevant by the Sentencing Guidelines and
hence concluded that ‘‘unwarranted disparity’’ existed if and only if there
was deviation from the Guidelines. The commission’s finding of less disparity post-Guidelines was simply a confirmation that post-Guidelines sentences are more likely to be in accordance with the Guidelines. This study
illustrates the general problem with this measurement strategy—to compare
‘‘similar’’ cases, a study must rely upon an inevitably controversial theory
of what constitutes proportional and disproportional variation. Moreover,
variation because of unobserved differences in the cases (proportionality)
cannot be readily distinguished from variation because of the decision makers in the system (disparity).
In the third approach, caseloads randomly assigned to judges have been
31
In the Second Circuit survey, the judges were mailed the case packets over the course
of 6 weeks, responding with proposed ‘‘sentences’’ by return mail. In addition to lack of
face-to-face contact with the defendant and lack of advocacy by the parties, there was no
simulation of the presentencing procedural history of the cases, especially that relating to
plea bargaining. Nor was there any discussion of parole in the study or whether judges should
sentence in ‘‘real time’’ or compensate for the effect of parole. One scholar who led a reanalysis of the data of the Second Circuit study has reported that ‘‘much of the seeming difference in sentences . . . was simply a function of different understandings as to . . . how long
the judge thought the defendant would actually serve.’’ Milton Heumann, Empirical Questions and Data Sources: Guidelines and Sentencing Research in the Federal System, 6 Fed.
Sentencing Rep. 15 (1993) (summarizing research by Stanton Wheeler et al., Sitting in Judgment: The Sentencing of White-Collar Criminals (1988)). See also Jon O. Newman, A Better
Way to Sentence Criminals, 63 A.B.A. J. 1562 (1977) (suggesting that disparity in sentencing
in the Second Circuit study was increased because of different assumptions about actions of
the parole board); Jon O. Newman, Foreword: Parole Decision-Making and the Sentencing
Process, 84 Yale L. J. 810, 812 (1975); Shari S. Diamond & Hans Zeisel, Sentencing Councils: A Study of Sentencing Disparity and Its Reduction, 43 U. Chi. L. Rev. 109 (1975).
32
See text accompanying notes 9–11 supra.
33
U.S. Sentencing Commission, The Federal Sentencing Guidelines: A Report on the Operation of the Guidelines System and Short-Term Impacts on Disparity in Sentencing, Use
of Incarceration, and Prosecutorial Discretion and Plea Bargaining 288, 292, 296, 299 (1991).

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deemed to be comparable, and the average sentencing outcomes for these
caseloads compared, with differences attributed to the judges. We adopt this
third approach and examine the average sentences of cases to which judges
were randomly assigned within a particular federal district office to assess
whether there was more disparity in these averages before or after implementation of the Federal Sentencing Guidelines.34
To make the following discussion of measurement methodology more
concrete, consider a simple example of a district in which cases are randomly assigned to two judges, Judge Harsh and Judge Lenient. In measurement of interjudge disparity, we focus on the difference between judges
within a time period (D t ) in the mean of prison sentences for each judge
(θ) relative to the mean level of prison sentence length in the district as
shown in (1).
Dt ⫽

θh ⫺ θl
.
E[θ]

(1)

In evaluating the effect of the Guidelines on interjudge disparity, we examine the magnitude and statistical precision of the change in this disparity
measure before and after the Guidelines (time periods 1 and 2), denoted as
∆D in (2).
∆D ⫽ D 2 ⫺ D 1 .

(2)

This empirical strategy is the most straightforward, but it has several important implications.
First, the null hypothesis that interjudge disparity is the same in both periods (∆D ⫽ 0) can be tested directly.35 This is conceptually distinct from
34
A methodology similar to ours was first used by Frederick Gaudet, George S. Harris, &
Charles W. St. John in Individual Differences in the Sentencing Tendencies of Judges, 23 J.
Crim. L. Criminology 811 (1933); and Frederick Gaudet, The Differences between Judges
in the Granting of Sentences of Probation, 19 Temp. L. Q. 4 (1946). More recently, it has
been used by Joel Waldfogel in Aggregate Inter-Judge Disparity in Sentencing: Evidence
from Three Districts, 4 Fed. Sentencing Rep. 151 (1991); Joel Waldfogel, Inter-judge Disparity in Federal Sentencing: Evidence from Three Federal Districts 1984–90 (1992) (unpublished manuscript on file with authors); Abigail Payne, Does Inter-judge Disparity Really
Matter? An Analysis of the Effects of Sentencing Reforms in Three Federal District Courts,
17 Int’l J. Law & Econ. 337 (1997); Paul Hofer, Kevin Blackwell, & Barry Ruback, The
Effect of the Federal Sentencing Guidelines on Inter-judge Sentencing Disparity (1998) (unpublished manuscript, U.S. Sentencing Commission).
35
Note that the hypothesis is about the change in overall disparity and not about changes
in behavior by particular judges over time. For example, if the two judges simply reversed
roles between the two periods, then there would be a change in θ h and θ l but no change in
∆D, the expected disparity from the point of view of the defendant. Waldfogel, Inter-judge
Disparity in Federal Sentencing, supra note 34, tests for a change in disparity by comparing
a model in which the judge means are restricted to be the same over time and one in which
they are allowed to vary. This is implicitly a test of changes in the behavior of individual
judges and not of overall disparity.

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statistical tests that rely on a null hypothesis of no disparity. Assume, for
example, that the judge means were the same in both periods and the hypothesis of no disparity was rejected in period 1. Suppose that the null hypothesis of no disparity were accepted in period 2, because of a smaller
sample size or increased variance in the distribution of sentence length. Under these assumptions, a false inference that there was a change in interjudge disparity may be drawn when there was in fact no change.36
Second, the disparity measured by ∆D is variation relative to the mean of
sentences in all cases. This has the desirable property of being an inequality
measure that is scale invariant. For example, simply multiplying all sentences by a constant factor (say, to make sentences stiffer in the later period) will not affect the magnitude of ∆D. Defendants who are acquitted or
whose cases are dismissed are assigned a sentence length of zero, because
cases (and not convictions) are randomly assigned to judges and because
only complete caseloads are comparable between judges rather than just
convictions.
Third, the judges compared in the two periods are the same. This allows
isolation of changes in behavior of the same individuals and avoids convolution with the potentially different sentencing patterns of other judges who
heard cases in only one of the periods.37
To move beyond the illustrative statistical model in (1) and (2), we now
discuss features of models suitable for estimation with data on multiple
judges. We begin with the model in (3) based on the Gini coefficient, where
g is the expected difference of J judge means relative to twice the overall
mean.
g⫽

1
J( J ⫺ 1)

J

J

j⫽1

k⫽1

冱冱

  θj ⫺ θk  
.
2E[θ]

(3)

If the true judge means θ were known, this would be an attractive measure.
Unfortunately, the fact that θ is measured with sampling error results in an
upward bias in the sample estimates of g, substantially complicating matters. One way to see this immediately is to examine the special case where
the true judge means are all the same. In a finite sample of cases, the esti36
Analyses based on percentage of variation explained or on F-tests for equality of judge
means to evaluate the impact of the Guidelines—as used by Payne and Hofer, Blackwell, &
Ruback, supra note 34—are vulnerable to these potentially confounding factors.
37
Because the behavior of the same judges is examined over time, the judges are necessarily older in the later periods. Experience may affect behavior, perhaps bringing judges closer
together over time as they observe each other’s work. We do not expect these changes to be
substantial over short periods of time, however, such as the consecutive 2-year periods that
are used in the empirical analysis.

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283

mated means will not be exactly the same, so g will always be estimated
to be some positive number when the true value is zero. This bias from
sampling error is an inherent feature of this and many other simple estimation strategies that summarize the dispersion of estimated parameters.38 Another disadvantage of these methods is that standard errors on changes in
dispersion of estimated means are analytically intractable—as with the Gini
coefficient—or have poor finite sample properties—as with analysis of
variance methods.39
These estimation concerns lead us to develop a parametric model to estimate interjudge disparity. Instead of summarizing the distribution of imprecisely estimated judge means, we adopt a strategy that incorporates the estimation of the judge effects directly in a statistical model of the underlying
distribution of sentence lengths. As a point of departure, we consider the
negative binomial model that has been used previously in econometrics and
that is part of a larger class of Generalized Linear Models well known in
statistics.40 This type of count data model is attractive for this application
because it accounts explicitly for the fact that the data are nonnegative integers. Introducing a random variable into this model that corresponds to the
judge assigned to the case allows us to directly estimate parameters that
capture the dispersion of this random variable or the variance of the ‘‘random effect’’ due to the judge.
We extend the negative binomial random effects model in several ways.
38
The intuition behind this bias is that we do not actually know which judge is truly more
harsh and which truly more lenient. By using the absolute difference, we always infer that
the one with the higher average sentence length is harsher. In repeated sampling, the truly
harsher judge may have a lower mean sentence length in some samples even though the mean
sentence length is higher on average. These misclassified instances, where the true difference
between the harsh and more lenient judge is negative but measured as positive, are the source
of the bias. When the true means are close together and the variance of the underlying distribution is large so that the means are imprecisely estimated, this type of misclassification may
occur frequently even though the estimates of the means themselves are unbiased. Similar
intuition applies to other dispersion measures like the variance.
39
A related alternative to the Gini coefficient would be estimation of the variance of a
random judge effect if the judge effects are cast in a variance components model, as discussed by Shayle Searle et al., Variance Components 168–226 (1992). When the data are
not normal, the asymptotic distribution of the variance of the random effect depends on
fourth moments. Our Monte Carlo experiments performed using data distributed like actual
sentencing data found that the asymptotic approximation for the standard error on changes
between periods in the between-judge component of the variance was far too dispersed to be
useful, with 2 SDs covering the truth nearly 100 percent of the time, as opposed to the predicted 95 percent coverage.
40
The negative binomial model in particular is well suited for the ‘‘overdispersed’’ nature
of the sentence length data relative to the more traditional Poisson model. See Jerry Hausman, Bronwyn Hall, & Zvi Griliches, Econometric Models for Count Data with an Application to the Patents-R&D Relationship, 52 Econometrica 909 (1984); A. Colin Cameron &
Pravin Trivedi, Regression Analysis of Count Data 27–37 (1998).

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First, we separate the likelihood into two parts, allowing an additional
‘‘zero-inflation’’ parameter for the probability of receiving no prison sentence.41 Second, the mean of the random effect is allowed to differ by covariates, so that we can measure dispersion relative to each district mean.
Third, a lognormal distribution is used for the random effect, which allows
a convenient interpretation of the dispersion of the random effect as a Gini
coefficient, the expected absolute difference in average sentence length between judges in the same district.42 Finally, the random effects are allowed
to be correlated over time, and the extent of the correlation can be directly
estimated.
Let Y denote the number of months of a prison sentence. For judge j in
period t, there are a total of N tj realizations of y itj . To model the distribution
of sentence lengths in cases heard by a judge, we use a negative binomial
distribution with parameters m and p, augmented with an extra parameter d
that affects the probability that y itj ⫽ 0. The joint likelihood function L Tj for
cases heard by a judge in T periods is given in equation (4), where Γ⵺ is
the gamma function.
L Tj ⬅ Pr( y 11j , . . . , y NTjTj   J ⫽ j )
T

⫽

N tj

兿兿
t⫽1 i⫽1

w t Γ(m t ⫹ y itj )
[d t ⫹ p tjmt ]1(y itj ⫽0) [p mtj t (1 ⫺ p tj ) y itj ] 1( yitj ⬎0) .
Γ(m t )Γ(y itj ⫹ 1)

(4)

The density of the zero-inflated negative binomial is normalized to one by
setting w t ⫽ (1 ⫹ d t )⫺1.
When p is defined as a particular function of m, d, and a judge-specific
parameter θ, the mean sentence length for judge j in period t depends only
on the judge effect θ as in (5).

冢

p tj ⬅ 1 ⫹ θtj

⫺1

冣

(1 ⫹ d t )
mt

⇒ E(Yitj  T ⫽ t, J ⫽ j ) ⫽ θ tj .

(5)

41
This augmentation has been previously developed for the Poisson model. See John Mullahy, Specification and Testing of Some Modified Count Data Models, 33 J. Econometrics
341 (1986); Diane Lambert, Zero-Inflated Poisson Regression, with an Application to Defects
in Manufacturing, 34 Technometrics 1 (1992); Shiferaw Gurmu, Paul Rilstone, & Steven
Stern, Semiparametric Estimation of Count Regression Models, 88 J. Econometrics 123
(1999).
42
Hausman, Hall, & Griliches, supra note 40, parameterizes the random effect with a beta
distribution, which results in a likelihood function that has a particularly simple form for a
single period but is not easily extended to allow correlation in the random effects across
periods. Multivariate normal random effects for the Poisson model have been explored by
Siddhartha Chib, Edward Greenberg, & Rainer Winkelman, Posterior Simulation and Bayes
Factors in Panel Count Data Models, 86 J. Econometrics 33 (1995).

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285

Since we are interested in the distribution of the judge effects, we directly
model the distribution of θ. For the complete data in any one period (T ⫽
1), the likelihood L 1 is obtained by integrating out θ (the judge ‘‘random
effect’’) using a lognormal density function with mean µ t and standard deviation σ t , denoted as f 1 in equation (6).
J

L1 ⫽

兿冮
j⫽1

∞

L 1j (θ 1j ) f 1 (θ 1j   µ 1 , σ 1 )dθ 1j .

(6)

0

For any single district office, the number of judges is relatively small (2–
21), and there are a reasonably large number of cases per judge (N tj ⱖ 30).
Thus, estimates of σ correspond to the dispersion about the overall office
mean in consistent estimates of average sentencing for an observed small
sample of judges.43 Data from multiple district offices are pooled for efficiency of estimation. We allow the mean of the judge effects to differ by
office, since cases are assigned randomly within district offices but not between offices. Denoting X as a set of indicators for each office, we let µ t ⫽
Xβ t .
In order to account for correlation of judge effects across two periods,
we also formulate a model in which the likelihood L 2 for two periods uses
joint lognormal density function with correlation coefficient ρ, denoted as
f 2 in equation (7).
J

L2 ⫽

∞

兿冮 冮
j ⫽1

L 2j (θ 1j , θ 2j )f 2 (θ 1j , θ 2j   µ 1 , σ 1 , µ 2 , σ 2 , ρ)dθ 2j dθ 1j .

(7)

0

A primary interest in this study is measures of interjudge disparity in sentencing. Denote γ as the Gini coefficient of concentration of the judge
means derived from (6) or (7), as opposed to g in (3), which is computed
using the estimated judge means. Using the properties of a lognormal parametric form for θ, the Gini coefficient measuring relative disparity in average sentence length between judges in two periods depends only on the two
43
To see the implication of this, consider a simple example. Say that an office has a superpopulation of potential judges with f 1 (3.5, 0.1) and receives two judges h and l, and θ h ⫽ 36
and θ l ⫽ 30. The standard deviation of log(θ) in this sample of actual judges in the district
is 0.091. This estimation strategy will identify the dispersion in the actual small sample,
0.091, and not the dispersion in the superpopulation of potential judges, 0.1. In general, the
dispersion in a small sample will be less than the superpopulation from which it is drawn.
In a simulation of 100,000 samples of judge effects from a lognormal distribution f 1 (3.5, 0.1),
the average standard deviation of the log was 0.056 for a sample of two judges, 0.080 for
four judges, and 0.096 for 22 judges. This implies it is important that the number of judges
within a district office are the same when making comparisons between time periods using
this methodology.

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variance parameters of the random effect. A change in γ can be computed
as in equation (8), where Φ is the cumulative normal distribution function.

γ 2 ⫺ γ 1 ⫽ 2Φ

冢 冣

冢 冣

σ2
σ1
⫺ 2Φ
.
√2
√2

(8)

When data from multiple offices are pooled and µ includes indicators for
each office, then γ measures the overall dispersion in judge means relative
to their own district office mean. Furthermore, since γ is the expected absolute difference between two judges relative to twice the overall mean, it
has the straightforward interpretation of interjudge disparity as a percentage
difference relative to the overall level of sentence length.
One simple hypothesis to explain changes in interjudge disparity over
time is that the types of offenses within a judge’s caseload are changing
over time. We would like to distinguish between changes in the behavior
of judges and changes in the types of cases to which they are assigned.
What would trends in interjudge disparity look like if judges had been assigned caseloads with the same shares of offense types every year? One
way to answer this question is to statistically adjust by reweighting the
caseloads. For example, the adjusted average sentence length for a judge in
1982–83 and 1992–93 might take the average in each period for drug cases
and for nondrug cases and compute a weighted average using the same
weights in both periods. In this paper, we use a set of weights for each district office based on the shares of offense types within that office in 1986–
87. Denote N 86-87 as the total number of cases in a district office during
1986–87. Let superscript z refer to a type of offense, so that N zjt is the number of cases assigned to judge j in time period t for offense type Z. Weights
w ijt are then defined in equation (9).
w ijt ⬅

冢

冣 冢 冣冢 冣

1
1 ⫹ dt

N z86-87
N 86-87

N jt
.
N zjt

(9)

For results in the next section that use weighting for offense type comparability over time, we change the weights w in equation (4), using w ijt from
(9) instead of w t ⫽ (1 ⫹ d t )⫺1.
In this paper, we focus on disparity in the overall average prison sentence
length, so we note that disparity in the overall average is heavily influenced
by cases with long sentence lengths. If there are differences in disparity by
type of offense, the offenses with longer sentences will have a large effect
on disparity in the overall average. To see this, say that Judge Harsh sentences a fraud offender to 11 months and a violent offender to 63 months,

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287

while Judge Lenient sentences a fraud offender to 9 months and a violent
offender to 57 months. The Gini coefficient between these two judges for
the fraud cases is 0.1 and for the violent cases is 0.05. The Gini coefficient
for the overall average of 33 and 37 is 0.057, which is indicative of the
weight given to the offense type with the larger average sentence length.44
V.

Data Description

In order to implement the measurement strategies outlined in the previous section, we minimally required data on the universe of cases filed
within various districts and on the judge, disposition, and prison sentence
length in the case. A special extract was prepared for this research by the
Statistics Division of the Administrative Office of the U.S. Courts that included a previously unavailable nonidentifying code that was used to group
together cases heard by the same judge.45
In order to create a dataset of cases randomly assigned to judges, we excluded judges who did not hear a full caseload (and therefore were unlikely
to have fully participated in the randomization). This selection rule was
based on the number of cases heard.46 Under random assignment, the caseload should be approximately balanced across judges. On the basis of this
44
To enhance the comparability between results for the overall mean and those for accounting for offense types, we use direct weighting in equation (9) so that the estimates are
sensitive to the sentence length in the same way as the estimates for the unweighted data.
Another way to account for offense types would be to include covariates directly in the
model, such as including indicators for offense types in µ. If there were differences in disparity by offense type, this strategy would instead essentially weight by the number of cases
for each offense type without regard to the average sentence length for that offense type—
complicating the comparison between estimates adjusted to account for offense types and
unadjusted estimates.
45
The data used in this paper are the same as the Cases Terminated files of the Administrative Office of the U.S. Courts (AOUSC), with documentation available from the Federal
Justice Statistics Program data in the National Archive of Criminal Justice Data, except that
the judge code is not suppressed as it is in the public-use file. By agreement with the
AOUSC, we cannot provide any information that would result in the disclosure of data about
specific judges. Therefore, we do not report the identity of specific district offices used in
this analysis.
46
In order to be included in a sample for analysis, a judge had to have been assigned a
proportion of cases within a certain range of the maximum assigned to any judge in that
office in any 1-year period. A chi-square test statistic was then computed for the null hypothesis that the cases were distributed between with equal probability in the final sample of cases
used for analysis. The p-values from this test should be uniformly distributed between zero
and one. The size of the range used was 3.9 standard errors of the maximum proportion,
which was calibrated so that the median was 0.50 for the 304 test statistics for offices and
periods used in the final sample. It appears the most judges excluded by this rule either were
not in the district for the entire period or were likely on senior status and consistently receiving a reduced caseload. The identity of the judges is masked in our data, however, so senior
status cannot be directly verified.

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logic, we constructed a sample in which judges were deemed to be ‘‘active’’ in a particular year.47 In order to have a sufficient number of cases to
consistently assess the sentencing patterns over time, cases were dropped
from the sample if the assigned judge had fewer than 30 cases within a 2year period. Since random assignment is usually done within each of several offices in any district, we restricted our data to offices that had at least
two judges. When judges were assigned cases in more than one office, cases
were included only for the office from which the judge was assigned the
largest number of cases. Since judges are randomly assigned to cases, but
the cases may have more than one defendant, we randomly selected one
defendant from each case.
A central premise of this analysis is that cases are randomly assigned to
judges. We marshal two types of evidence in support of our claim that random assignment was used in the districts included in our analysis. A primary source of evidence regarding randomization is the distribution of offense types among the caseloads of each judge. For example, the proportion
of drug cases, embezzlement and fraud cases, violent and firearms cases,
and other crimes should be the same for each judge in a district office except for sampling error. Differences in these proportions form the basis for
the chi-square test of independence of the offense types and the judges. We
performed these chi-square tests for each district office for judges with at
least eight cases during 25 6-month periods from July 1981 to December
1993. Under random assignment, we would not only expect that 95 percent
of these tests would have chi-square test statistics less than the .95 critical
value, but that the test statistics for the various time periods would be uniformly distributed over the (0,1) interval with an average p-value of 0.5. A
statistical exclusion rule based on this logic was used to identify districts
unlikely to have used random assignment throughout the 25 periods, where
districts with a mean p-value below a threshold (the fifth percentile of the
mean of 25 uniform random variables, .405) were excluded. Districts were
also excluded if there were not at least two active judges in eight or more
6-month periods both before and after implementation of the Guidelines.
As a second source of information on random assignment, we drew upon
interviews with the court clerks in the districts. We conducted 40 interviews
47
The exact time periods cover one calendar year, with the following exceptions. To increase the sample size for the two earliest periods, the 1982 period is actually from July 1981
to September 1982, and the 1983 period is from October 1982 to December 1983. The 1988
period includes November 1987 through January 1989, including cases from the initial promulgation of the Guidelines through the ruling on their constitutionality. (In Mistretta v.
United States, 488 U.S. 361 (1989), the U.S. Supreme Court upheld the constitutionality of
both the Sentencing Guidelines and the commission in the face of challenges under the nondelegation doctrine and the separation of powers.)

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sentencing disparity
TABLE 1
Quantiles of p-Values from Chi-Square Tests of
Independence between Judges and Offense Types
Quantile

.10

.25

.50

.75

.90

p-value

.09

.23

.47

.76

.92

Note.—Six hundred six chi-square statistics were computed for
26 offices and for up to 25 6-month periods. Quantiles of p-values
are weighted by number of cases in that office and time period.
The offense types were grouped into four categories: drug, violent
and weapons, embezzlement and fraud, and other cases.

ourselves and also utilized a similar investigation by researchers at the U.S.
Sentencing Commission.48
The statistical exclusion rule based on the mean p-value of chi-square
test for independence of offense types identified all four offices that had
consistently had at least two active judges but were reported to have used
nonrandom assignment of cases according to the qualitative research, as
well as 19 other offices. For the 26 offices included in the analysis, we present quantiles of the p-values from the chi-square tests of independence of
judges and offense types in Table 1. The mean of the 606 test statistics is
0.49, and they are distributed fairly uniformly from zero to one.
The resulting sample used for estimation includes 77,201 cases, 27 percent of the total universe of over 285,000 cases from July 1981 to December 1993. About half the cases are excluded because an office does not have
at least two judges who consistently had cases assigned to them throughout
the period. Roughly another one-quarter of cases are excluded because they
were assigned in an office that did not appear consistently to use random
assignment of cases to judges throughout the time period under study. Both
the regional composition and the offense types are similar in the estimation
sample and in the universe of all cases.
In our analysis, we focus on comparison of interjudge disparity for 2year periods before and after promulgation of the Guidelines. Descriptive
48
The particular methods used to assign cases to judges vary between districts. In some
districts, judge’s names are drawn from a deck of cards—sometimes shuffled in the dark
and/or sealed with wax to prevent tampering. In others, envelopes with the judges’ names
are placed in a box or circular hopper that is spun before the clerk pulls an envelope out of
the box. In the 1990s, many districts have adopted computer software to implement the random assignment. Also, in order to more evenly distribute potentially lengthy cases, random
assignment is sometimes stratified by projected length of the case. Paul Hofer at the U.S.
Sentencing Commission also provided information about case assignment practices based on
interviews conducted during his own research and from interviews previously conducted by
the Federal Judicial Center as part of the FJC Time Study (on file at the Federal Judicial
Center). Letter from Paul Hofer to Jeffrey R. King, December 4, 1997.

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TABLE 2
Descriptive Statistics of Prison Sentences in Months
1982–83 1984–85 1986–87 1988–89 1990–91 1992–93

Percentages:
% 0 months (acquittals)
% 0 months (dismissals)
% 0 months (convictions)
% 1–24 months
% 25–48 months
% 49–96 months
% 97–540 months
Summary statistics:
Mean
SD
Sample sizes:
Offices
Judges
Cases

3
13
32
26
12
9
6

2
13
35
25
11
8
6

2
11
33
24
11
10
8

2
10
27
29
11
12
9

2
10
28
27
9
12
11

1
10
24
28
12
14
11

24
50

24
53

29
57

32
60

36
66

38
67

23
139
11,997

26
148
12,007

26
154
12,575

25
157
13,689

26
161
13,604

26
159
13,329

Note.—Data are from Cases Terminated files of the Administrative Office of the U.S. Courts. For
sample creation details, see Section V.

statistics for the 2-year periods from 1982 to 1993 are given in Table 2.
The percentage with zero sentence length in our data include zeros for acquittals and dismissals, which have declined slightly as a share of all cases
over time. The distribution of sentence length shifted toward higher sentences throughout the 12.5-year period covered by these data as mandatory
minimums and Guidelines took effect over time.
VI.

Results

On the basis of our interviews and statistical tests, we are fairly confident
that the offices included in our sample used random assignment of cases to
judges. Since the caseloads should therefore be comparable, differences in
the average sentence length of these caseloads can be attributed to judges
themselves. This section reports the results of the methods outlined in Section IV above.
In Figure 1, we graph estimates of interjudge disparity for 2-year time
periods from 1982 to 1993 using the data described in Table 2. The triangles in Figure 1 are Gini coefficients computed from the absolute difference
of the judge means, based on g from equation (3) using the average of estimates for each district office weighted by the number of cases in that office.
The circles in Figure 1 are from the dispersion in the random effect of the
zero-inflated negative binomial model for each single period, based on estimates using equation (6) transformed into the Gini coefficient γ. The

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 Figure 1.—Interjudge disparity for all judges

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changes over time in g and γ are quite similar, with a peak in 1984–85,
followed by a decline that accelerates from 1986–87 through 1988–89 and
a leveling off thereafter. As discussed in Section IV above, the estimates of
g are biased upward by sampling error. Estimates of the magnitude of the
bias depend on the assumptions used to model the judge means.49 The estimates of γ account for sampling variability by explicitly modeling the underlying distribution of sentence lengths and the distribution of judge
means, formalizing the intuition that larger deviations of a judge from the
district office mean are increasingly likely to be caused by sampling error.
The point estimates of g are approximately 0.07 greater than γ for each time
period. Based on the model of γ, the sampling error bias in g appears to be
fairly constant over time.50 Our main interpretation of these results is that
the same temporal dynamics of interjudge disparity are apparent in measurements of both g and γ. This increases our confidence that our results
about changes in disparity over time are not highly sensitive to the modeling strategy.
For the remainder of this section, we focus on estimates of γ from the
random effects model so that we can account for sampling error bias, assess
the statistical precision of changes between periods, and estimate the correlation of judicial sentencing patterns between time periods. To first verify
that the model defined in equations (4)–(7) is an appropriate model for
these data, we compare observed cell probabilities for the pooled data from
1986–87 with predicted values from a simple two-part negative binomial
model, assuming that δ, γ, and θ are constant across all cases. The actual
distribution and predicted distribution are presented in Table 3. The model
49
One model is that the true judge means are identical within each office. To simulate the
bias when the true g is zero, we created data where each judge was randomly matched with
the sentencing outcomes of N jt cases from the district office. An alternative model is that the
estimated judge mean is an unbiased estimate of the true mean. Treating the observed distribution as the true distribution, an estimate of the bias can then be computed from the difference between the mean of the bootstrap estimates and the original estimate. We computed
bootstrap estimates of the bias for this model by drawing bootstrap samples for each judge
from the observed distribution of sentencing outcomes for that judge. In 1986–87, for example, the estimated g was .154. In 500 replications, the bias was estimated to be .122 from
the true mean zero simulation and .038 from the bootstrap procedure. The middle ground
between these two models would allow differences in the judge means while incorporating
the intuition that an estimated judge mean particularly different from the district office mean
is more likely to have come from an unusual sample of cases (rather than treating these extremes as unbiased estimates of the true mean for that judge).
50
Note that the bias in absolute measures of disparity, such as the variance or the mean
absolute deviation, is increasing over time as the underlying variance of the data is increasing. The mean of the data is also increasing over time, however, so that ratio of the standard
deviation to the mean in Table 2 has actually decreased slightly over time, implying slightly
less bias for relative disparity measures in later periods. A counteracting factor, however, is
that the true means appear to be closer together in later periods, which increases the bias as
discussed in note 40 supra.

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TABLE 3
Observed versus Predicted Cell
Probabilities of Three
Parameter Model
Months of
Prison Term
0
1–12
13–24
25–48
49–96
97–192
193–540

Observed

Predicted

.464
.154
.088
.107
.106
.059
.020

.464
.135
.084
.110
.113
.072
.020

Note.—Estimates are based on equation
(4), assuming that the three parameters d, m,
and p are constant across all cases, using
pooled data for 1986–87.

has been constructed to fit zero exactly and does a reasonable job of representing the rest of the distribution—even though the large amount of data
results in a chi-square statistic (χ 2 ⫽ 66) that rejects the hypothesis that the
model exactly fits the data. Of course, the model does not account for the fact
that within the cells of Table 2 the data are clustered at particular months
(6, 12, 18, . . . ) rather than distributed smoothly across all months, but the
model fits the basic features of the data quite well. Allowing θ to vary across
the judges when maximizing the likelihood in (7) requires evaluating J double integrals for every function evaluation in nonlinear optimization, but
these can be computed efficiently after an appropriate transformation of
variables using Gaussian quadrature based on Hermite polynomials.51 Standard errors for γ, the Gini coefficient in (8), are computed using a numerical
approximation to the Hessian and the delta method.52
The estimates of γ for Figure 1 were estimated separately for each period
based on equation (6) and data for all judges available in the period. The
Gini coefficient estimates peak in 1984–85 and fall by .019 in 1986–87 and
again by .031 in 1988–89 before largely leveling off. While not statistically
51
The weights and abscissae used were from the 16-point Gauss-Hermite rule in Gwynne
Evans, Practical Numerical Integration 308 (1993); 25-point and 40-point rules were also
tried and resulted in almost identical point estimates. (Estimation programs in MATLAB are
on file with the authors.)
52
In order to assess the usefulness of these asymptotic approximations for inference in
finite samples, we conducted Monte Carlo simulations in which the true parameters of the
model were known. The asymptotic standard errors reported in the paper appear to be slightly
too small, with the confidence interval of 1.96 times the standard error including the truth
about 90 percent of the time as opposed to the asymptotic prediction of 95 percent coverage.

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significant, these results also suggest that interjudge disparity may have
been decreasing prior to 1986–87—an issue that we discuss further below.
Taking the average over the three periods from 1988 to 1993 as our postGuidelines measure, interjudge disparity fell from .085 to .054 from 1986–
87 to 1988–93, a decrease of .031 with a standard error of .010. The
changes are more pronounced than the mixed results of previous researchers.53 On the basis of these results, the expected difference between two typical judges is twice the Gini coefficient—about 17 percent in 1986–87 and
about 11 percent in 1988–93.
Since overall sentence lengths are rising over time, a given percentage
difference in interjudge disparity implies a larger absolute difference in
months of prison sentence length. Multiplying the percentage difference by
the overall average sentence length in each period from Table 2 expresses
our measure of interjudge disparity in terms of months. For 1986–87 when
the mean sentence length was 29, the expected interjudge difference was
4.9 months, which fell to 3.9 months in 1988–93 when the mean sentence
length was 35.54
53
Waldfogel, Inter-judge Disparity in Federal Sentencing, supra note 34, analyses three
districts (CT, SDNY, NDCA) from 1984–90 and finds an increase in interjudge disparity in
two of the three districts during 1988–90, although no standard errors for these estimates are
reported. Payne, supra note 34, analyses three districts (EDNY, SDNY, EDPA) from 1980–
91. For property crimes, she finds that interjudge disparity declines for one of three districts.
For drug crimes, she finds declines for all three districts. Payne emphasizes that the fraction
of variation explained by mean judge effects is small relative to the total variation. This is
true and tells us that there are many additional factors that drive differences in sentences, but
it does not lead us to conclude that interjudge disparity itself is small or unimportant. Just
as with other empirical relationships, such as the amount of variation in wages that is explained by differences in education levels, the fact that the percentage of explained variation
is small is often less important than the magnitude of the coefficients associated with the
variable of interest, such as differences in average wages between education levels or (as we
believe in this case) with differences in average sentences between judges. Hofer, Blackwell, & Ruback, supra note 34, compare 1984–85 to 1994–95 using the same 42 judges in
nine district offices in the part of their analysis most comparable to ours. They also focus on
percentage of variation explained and report that the partial R 2 drops from 2.32 in 1984–85
to 1.08 in 1994–95. As pointed out in Section IV, there are several methodological differences between our analysis and those by Waldfogel, Payne, and Hofer, Blackwell, & Ruback.
Most important, we measure the magnitude of interjudge disparity directly and provide a
confidence interval to assess the statistical precision of the estimate of the change before and
after the Guidelines, so the null hypothesis of no change can be tested. Our data are also
more complete, covering 26 district offices for up to 12.5 years. In addition to the advantages
of sample size and representativeness, our data have been constructed with criteria selecting
districts using random assignment of cases to judges that appears to be more stringent. Of
the 13 districts in these three studies, only three had procedures and caseloads that appeared
to us to consistently use random assignment in the time periods under study here and were
included in our analyses.
54
The conversion of percentage differences into months depends in part upon the treatment of acquittals and dismissals. Cases (and not convictions) are randomly assigned to
judges, and we use all cases assigned in computing our estimates. An argument can be made

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Figure 2.—Interjudge disparity for the same judges over two periods

Between 75 and 86 percent of judges in any single 2-year period were
also in the sample during the following period. To ensure that results are
not simply being driven by changes in the composition of judges, we also
analyze changes based on the same judges in both periods. The lines in Figure 2 connect estimates of disparity between consecutive 2-year periods,
based on estimates of γ from equation (7). The changes over time are very
similar to those reported in Figure 1. The decrease in interjudge disparity
before and after the promulgation of the Guidelines is sharper when comparing the same judges over time, as the γ falls by more than half between
1986–97 and 1989–90 from .090 to .039, a decrease of .051 with a standard
error of .013. The estimates from 1988–93 range from .055 to .059 to .046,
that acquittals and dismissals are independent of the judge assigned to the case, based on
the logic that judges have much more discretion over sentencing for convicts than for other
dispositions. Statistical tests for independence analogous to those for offense types described
in Section V indicate that the combined fraction of acquittals and dismissals is roughly balanced across judges. Under true independence, the mean p-value of the 606 chi-square statistics (testing for independence of judge and acquittal/dismissal) should be .5, and the actual
value is .46. Inclusion of acquittals and dismissals appears to have a negligible effect on the
estimates of the Gini coefficient, since this is roughly equivalent to rescaling the judge means
by a constant factor. If we were to use the mean sentence for convictions (33 in 1986–87
and 39 in 1988–93) instead of the mean for all cases, the results would be an expected difference of 5.7 months in 1986–87 and 4.4 in 1988–93.

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TABLE 4
Share of Cases by Offense Type
1982–83 1984–85 1986–87 1988–89 1990–91 1992–93

Drug
Violent and weapons
Embezzlement and fraud
Other

.21
.16
.26
.37

.25
.14
.28
.33

.27
.14
.31
.28

.32
.15
.28
.25

.30
.18
.29
.23

.33
.17
.26
.24

Note.—Shares based on data described in Table 2.

and these differences are indistinguishable from sampling error. The most
conservative estimate, not shown in Figure 2, compares the same judges in
1986–87 to those in 1989–90, omitting 1988 to allow a transition period
for adjustment to the new regime and because legal challenges to the
Guidelines were not resolved until January 1989. This estimate shows that
γ falls from .083 to .067, a decrease of .016 with a standard error of .013.
This estimate is conservative in the sense that it is a smaller change than
that from 1986–87 to 1988–89 and that our other estimates of disparity for
years after the Guidelines other than 1989–90 are all lower than .067. We
conclude from measures using the same judges that the expected difference
between two judges (twice the Gini coefficient) decreased from 17–18 percent in 1986–87 to 8–13 percent in 1988–90. This range using the same
judges in both periods brackets a decrease from 17 to 11 percent reported
above for all judges based on Figure 1 for 1986–87 to 1988–93.
Another factor changing over time is the mix of offenses in the overall
caseload. Table 4 shows that the overall share of drug offenses increased
from .21 to .33 from 1982–83 to 1992–93, while the share of ‘‘other’’ offenses (such as forgery) fell from .37 to .24. If the disparity in sentencing
drug cases was always lower than disparity for other cases, then we might
observe a decrease over time in measured overall interjudge disparity that
was caused by a change in the caseload coming before judges. In an attempt
to separate out changes in judicial behavior from changes in the types of
cases, we compute weighted results, replacing w t in (4) with w ijt defined in
(9). These weights statistically adjust so that the shares of offense types in
the overall distribution for each judge in each time period are equal to the
share for their district office in 1986–87. The four offense types used are
violent and firearms, drug, embezzlement and fraud, and other cases. The
choice of a base period does not affect trends over time but does affect the
levels of the estimates; 1986–87 is chosen to address the counterfactual in
which the Sentencing Guidelines were later adopted but the mix of offense
types did not change.
The unweighted results using w t from Figure 2 are reproduced in the first

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sentencing disparity
TABLE 5
Changes over Time in Gini Coefficient Estimates of
Interjudge Sentencing Disparity
Weighted for Offense Type
Comparability

Unweighted
1982–83

1984–85

.079
(.009)

.107
(.008)

1984–85

1986–87

.102
(.009)

Change

1982–83

1984–85

.092
(.008)

.102
(.009)

Change

1984–85

1986–87

Change

.092
(.009)

⫺.010
(.012)

.097
(.009)

.080
(.008)

⫺.017
(.011)

1986–87

1988–89

Change

1986–87

1988–89

Change

.090
(.008)

.039
(.010)

⫺.051
(.013)

.079
(.008)

.042
(.010)

⫺.038
(.012)

1988–89

1990–91

Change

1988–89

1990–91

Change

.055
(.010)

.057
(.008)

.057
(.008)

.053
(.009)

⫺.004
(.014)

1990–91

1992–93

Change

1990–91

1992–93

Change

.059
(.008)

.046
(.010)

⫺.012
(.012)

.045
(.008)

.041
(.011)

⫺.004
(.014)

.028
(.011)

.002
(.013)

Judges

Change
.011
(.012)

118

126

133

128

120

Note.—Estimates are for Gini coefficients γ (with standard errors in parentheses) from equations (7)
and (8) using data summarized in Table 2. Unweighted estimates are based on w t in (4), while weighted
estimates are based on w ijt from equation (9). As described in the text, the weights statistically adjust each
judge’s caseload over time to reflect the district office’s mix of offense types in 1986–87. The four offense types used are drug, violent and weapons, embezzlement and fraud, and other.

three columns of Table 5, weighted results using w ijt are shown in columns
4–6, and the number of judges active in the consecutive 2-year periods is
shown in column 7. In addition to making the shares of offense types comparable over time, weighting equalizes the shares of offense types within a
period. The magnitudes of the weighted point estimates of interjudge disparity are slightly lower than the unweighted estimates, because of the correction for variability due to the fact that the shares are similar but not exactly equal when cases are assigned randomly.55 The point estimates differ
slightly, but the overall pattern of results is quite similar for the unweighted
results and those weighted for comparability over time. For example, the
55
Since the data are weighted to reflect the 1986–87 case mix within each district office,
the roughly 10 percent reduction in the magnitude of point estimates for the 1986–87 period
is not due to changes in the offense mix over time. Instead, it reflects the fact that different
offense types are weighted exactly equally in modeling the overall distribution for each
judge, instead of the approximate equality of random assignment.

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weighted estimate of γ in 1986–87 is .079 and falls to 0.042 in 1988–89,
implying that the expected difference between two judges fell from 16 percent to 8 percent.
Our main interpretation of these results is that changes in interjudge disparity are not due to changes in the types of offense in the overall caseload.
The aspect of the results that appears to be most sensitive to changes in
specification is the change in disparity from 1984–85 to 1986–87. In all
specifications, disparity appeared to be stable or increasing through 1986.
For example, the weighted estimates for using the same judges in 1983–84
and 1985–86 (not shown in Table 5) were .088 and .092. Decreases in disparity appear to be concentrated during 1987–89, but there are not enough
cases per judge to more precisely identify the timing of the changes.
Our preliminary research on disparity for particular offense types suggests that the decrease in interjudge disparity is concentrated within the violent, weapons, and drug crimes. Estimation for particular offense types substantially reduces the number of cases per judge in each period, however,
and Monte Carlo simulations suggest that the methods used in this paper
are substantially less reliable when there are fewer than 30 cases per judge
used in the estimation. In future research we intend to pool additional years
of data and model the dispersion in judge means as a parametric function
that is changing over time, in order to obtain reliable estimates for various
offense types.
Regarding the correlation of the judge effects, we find that the behavior
of judges appears to be fairly consistent over time prior to the Guidelines.
Table 6 reports the correlation of judge effects between time periods. Prior
to 1986–87, this measure is greater than .70.56 There is some evidence that
the consistency of judicial sentencing patterns declined thereafter, but the
results are mixed. It is increasingly difficult to reliably estimate the correlation between two periods when the variance of the random effect is small
in both periods. In comparisons for 2-year periods subsequent to those reported in Table 6, the correlation varies from .44 to ⫺.24. However, the
standard errors are at least .21, and we cannot draw any credible conclusions from these very imprecise estimates in the later periods.
Finally, we return to the question of causality. Were these changes over
time in interjudge sentencing disparity caused by the Federal Sentencing
Guidelines? Clearly, the largest change in disparity occurs between 1986–
87 and 1988–89, which corresponds to the effective date of the Guidelines
56
For context, note that the consistency in public behavior over time is even greater
among representatives in the U.S. Congress, where the correlation in indices of voting patterns is 0.78 to 0.95 (depending on the index) when examining the voting by the same representative separated in time by two terms. See John Lott & Stephen Bronars, Time Series
Evidence on Shirking in the U.S. House of Representatives, 76 Pub. Choice 125 (1993).

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sentencing disparity
TABLE 6
Correlation of Judge Effects
between Time Periods
1982–83 and 1984–85
1983–84 and 1985–86
1984–85 and 1986–87
1985–86 and 1987–88
1986–87 and 1988–89
1988–89 and 1989–90

.73
(.09)
.70
(.09)
.75
(.07)
.22
(.14)
.68
(.13)
.34
(.17)

Note.—Estimates of ρ (with standard errors in parentheses) are from maximum likelihood estimation of equation (7), using data
summarized in Table 2.

in November 1987. Disparity from 1988–93 has remained at levels lower
than observed from 1982 to 1987. While this timing is suggestive, the
Guidelines applied only to offenses committed after November 1, 1987. Because of the lag from commission of offense to case filing and because of
constitutional challenges to the Guidelines, about half of the cases filed in
1988 and 1989 were not sentenced under the Guidelines.57 We suspect that
the 1986 enactment of mandatory minimum sentences for drug offenders
(which applied only to crimes committed after October 1, 1986) may have
substantially contributed to the decrease in disparity after 1986.58
57
Our data record only date of case filing and termination, and not date of offense or use
of the Guidelines in sentencing. As shares of cases filed in 1988–89, .3 were terminated in
1988, .43 in 1989, and .27 in 1990 or later. The U.S. Sentencing Commission, Annual Report
39 (1990), tabulates the fractions of terminated cases sentenced under the Guidelines to be
.18 in 1988, .55 in 1989, and .70 in 1990. As a rough estimate of Guideline application, we
use the shares of cases filed as weights to infer that the average fraction of Guidelines application was about 48 percent for cases filed in 1988–89.
58
Before the Sentencing Guidelines were even promulgated, Congress enacted the Anti-Drug
Abuse Act 1986, Pub. L. No. 99-570, 100 Stat. 3207, which provided an array of mandatory
minimum penalties for narcotics offenses and violent crimes. Most significantly, the act ‘‘set up
a new regime of non-parolable, mandatory minimum sentences for drug trafficking offenses that
tied the minimum penalty to the amount of drugs involved in the offense.’’ U.S. Sentencing
Commission, Special Report to Congress: Mandatory Minimum Penalties in the Federal Criminal
Justice System 8 (1991). These mandatory minimum sentences were severe for all drugs, but
especially for offenses involving crack cocaine, and they applied to nearly all drug offenses
prosecuted in the federal courts. Because statutory changes in sentencing law are not applied
retroactively to crimes before the enactment of the statutes and because there is a substantial
delay between the commission of a crime and sentencing, the effect of mandatory minimums
(like the Sentencing Guidelines) phases in gradually over several years.

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VII. Discussion
By focusing our analysis on the nominal length of prison sentences, we
have not considered interjudge disparity in the length of time actually
served in prison. It is possible that parole policies in the pre-Guidelines period reduced interjudge sentencing disparity in the time actually served by
an offender. The Sentencing Reform Act eliminated parole, so parole cannot affect time served in cases sentenced under the Guidelines.
For defendants who were sentenced to terms of imprisonment prior to the
Sentencing Guidelines, parole authorities actually determined the date of release from prison and, thus, the time actually served by the offender. These
determinations were based upon the Parole Guidelines, which were similar
in function to the Sentencing Guidelines. Like the Sentencing Guidelines
that were modeled after them, the heart of the Parole Guidelines was a grid
of boxes that indicated actual sentence length based on the offender’s prior
record and the seriousness of the offense. Since this determination was independent of, and subsequent to, the offender’s sentencing, the Parole
Guidelines may have substantially mitigated interjudge disparity in nominal
sentences. None of the influential studies that indicated widespread disparity in the pre-Guidelines era considered the effect of the Parole Guidelines
in reducing interjudge time-served disparity. In future research, we intend
to examine interjudge disparity in time served.
Despite this caveat, we believe our focus on disparity in nominal sentences is appropriate. First, as we have related above, interjudge sentencing
disparity was a critical impetus to the passage of the Guidelines, and reducing it was a central goal of the still-controversial Sentencing Guidelines.
Second, interjudge sentencing disparity is an interesting phenomenon apart
from its ultimate outcome on an offender’s sentence. The actual ceremony
of sentencing has an expressive function that is important independent of
the actual time served. The sentencing is the moment at which the community publicly expresses its disapproval of the offender’s action. The prosecutor and defense counsel offer a few words, offered more for the victim,
the defendant, their friends and family, and any press than for the judge.
The defendant is asked to speak, if she wishes, to accept responsibility, to
ask for forgiveness, or to say nothing. Finally, the judge formally articulates
a measure of the defendant’s offense against the community.
That different judges publicly express different measures of justice for
the same offenses is therefore both interesting and troublesome, even if the
offenders ultimately serve the exact same sentence. Frankel cited the fact
that some judges sentenced draft evaders to the maximum sentence while
other judges imposed almost no prison time for defendants who broke the
law in adherence to principle.59 This disparity is notable because it shows
59

Frankel, Criminal Sentences, supra note 14, at 29.

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that two judges, each purportedly expressing the will of the community, differ dramatically in their representation of the proper sentence for a particular crime. As Frankel noted, ‘‘It is not directly pertinent here whether either
category of judge is right,’’ 60 but the fact of their disagreement is pertinent.
The disagreement undermines the expressive function of sentencing by suggesting that a sentence is not so much a measure of the offense to the community as simply the personal judgment of the judge.
Despite the importance that the progenitors of the Guidelines placed on
interjudge sentencing disparity and our focus on it in this paper, it would
be a mistake to equate interjudge sentencing disparity with ‘‘unwarranted
sentencing disparity’’ and consider our findings a simple vindication of the
Sentencing Guidelines. We note, first, that we have sought to measure only
disparity among judicial participants in sentencing. There are, of course,
other sources of sentencing disparity in the federal criminal justice system.
As many commentators have noted, considerable disparity exists in charging policies at various U.S. Attorney’s offices,61 in the policies of law-enforcement personnel, and in the manner in which the probation officer conducts an independent investigation of the offense.62 The Guidelines did
nothing to address these sources of disparity.
60

Id.
Officially, offenders are to be charged with the most serious offense that can be proved
at trial with certain limited exceptions. In practice, however, charging policies vary widely.
See Ilene H. Nagel & Stephen J. Schulhofer, A Tale of Three Cities: An Empirical Study of
Charging and Bargaining Practices under the Federal Sentencing Guidelines, 66 S. Cal. L.
Rev. 501; Ahmed Taha, The Effect of the Federal Sentencing Guidelines on the Disposition
of Criminal Cases (1998) (unpublished manuscript, U.S. Department of Justice) (provides
evidence that prosecutors filed less serious charges against the average defendant, defendants
pleaded guilty to charges that were closer to the charges prosecutors filed, more defendants
initially pleaded guilty); Joe Brown, Quo Vadis? What Congress and the Department of Justice Should Do in Response to the Justice Department’s Analysis of Non-Violent Drug Offenders with Minimal Criminal Histories, 7 Fed. Sentencing Rep. 25, 26–27 (1994) (former
U.S. Attorney criticizes disparity among federal prosecutors in use of 5K1.1 motions and in
charging to avoid mandatory minimums: ‘‘popular way to avoid mandatory sentences entirely [is] by charging a telephone count under 21 U.S.C. § 843(b), which does not involve
a mandatory sentence’’); Robert H. Edmunds, Jr., Guidelines Sentencing and Department of
Justice Policies under the Reagan-Bush Administrations, 6 Fed. Sentencing Rep. 306 (1994)
(noting that in the district in which he was U.S. Attorney, the Middle District of North Carolina, an illegal alien who was convicted of reentry after deportation could expect a ‘‘term of
years’’ while in a California border district, illegal immigrations were common and the aliens
would receive far lighter sentences). There is an enormous range in policies among U.S. Attorney’s offices for making a motion for downward departure on the basis of substantial assistance (§ 5K1.1 motion), which allows a judge to sentence below the Guidelines range. In the
District of Connecticut, any § 5K1.1 motion must be approved by a committee including the
U.S. Attorney for the district. The § 5K1.1 departure rate in the district was 8.5 percent in
1994. In contrast, judges in the Eastern District of Pennsylvania departed downward on
§ 5K1.1 grounds in 49.3 percent of cases in 1994.
62
Gerald H. Heaney, The Reality of Guidelines Sentencing: No End to Disparity, 28 Am.
Crim. L. Rev. 161, 200 (1991) (role of probation officers varies widely by district; one federal defender describes probation as more adversarial than prosecution).
61

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Moreover, the reduction in the exercise of judicial discretion resulting
from the Sentencing Guidelines and the imposition of mandatory minimum
sentences increased the impact of any disparity at these earlier stages in the
criminal process. Reduced discretion for judges at the end of the process
magnifies the importance of decisions made by the prosecutor, probation
office, and law enforcement officials. Since the sentence will be determined
by what is proven by a preponderance of the evidence under the Guidelines,
the prosecutor exerts far more influence over the sentence than she did preGuidelines. Similarly, the offender’s sentence will directly reflect any disparity between probation officers, because they are the ‘‘Guidelines experts’’ who initially advise the judge of the facts of the case and how the
Guidelines apply to these facts. Under the Guidelines, law enforcement officials also wield more influence over final sentences. Many Guidelines sentences (including narcotics sentences and sentences for all crimes with
monetary losses) depend upon the measurable quantities involved in the offense. In many investigations of such crimes, governmental authorities exert
substantial control over the quantity that will be used to calculate the defendant’s sentence under the Guidelines. For instance, in narcotics investigations, the undercover agent often determines the amount of drugs either purchased from or sold to a putative defendant. Her decision as to the quantity
to attempt to buy or sell from the target offender will play a large role in
determining the ultimate sentence under the Guidelines.63
By giving prior actors (law enforcement officials, probation officers, and
prosecutors) more influence over the ultimate sentence, the Guidelines provide opportunities for these earlier actors to pursue their own agendas that did
not exist pre-Guidelines. If these prior actors vary in their willingness to engage
in manipulative tactics aimed at achieving a higher or lower Guidelines sentence for particular defendants, prosecutorial sentencing disparity will actually
have been increased by the Guidelines. Pre-Guidelines, any disparity resulting
from these practices was comparatively less because the judge and the parole
board exercised overwhelming control over the sentence.
In addition, mean sentence length has substantially increased under the
Guidelines. Critics of this increase may argue that any reduction in judicial
sentencing disparity was achieved primarily by reducing the frequency of sentences that, pre-Guidelines, were relatively lenient64 and that the result is a
plethora of long sentences disproportionate to the crime and the offender. In
this respect the Guidelines may be contrasted with a regime that successfully
reduced disparity without dramatically increasing sentence length.
63
See, for instance, United States v. Giles, 768 F. Supp. 101 (S.D.N.Y.), aff’d, 953 F.2d
636 (2d Cir. 1991), cert. denied, 503 U.S. 949 (1992).
64
This result may reflect legislative intent. Sponsors of Sentencing Reform Act included
both liberals primarily concerned with disparity in sentencing and conservatives primarily
concerned with leniency in sentencing.

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303

Finally, we note that there are other consequences of the Guidelines besides their effect on sentencing disparity and sentence length. Judges have
complained that the Guidelines rules themselves are as arbitrary as any exercise of judicial discretion may have been prior to the Guidelines and that
their arbitrariness and their extraordinary complexity have made the sentencing process incomprehensible and inaccessible to victims, defendants,
and the general public.65
VIII. Conclusion
Our study indicates that the Guidelines (and concomitant statutory minimum sentences) have been successful in reducing interjudge nominal sentencing disparity. To the extent that this was the central goal of the Sentencing Reform Act of 1984, Congress successfully achieved this goal. The
Guidelines have reduced the net variation in sentence attributable to the
happenstance of the identity of the sentencing judge. The expected difference in the sentence lengths of two judges receiving comparable caseloads
was 16 to 18 percent in the pre-Guidelines period of 1986–87. Comparing
interjudge disparity before and after the Guidelines, we find that this measure declined substantially, with estimates of the expected difference ranging between 8 and 13 percent during 1988–93.
Unfortunately, the very success of the Guidelines in reducing interjudge
disparity by constraining judicial discretion may have exacerbated the impact
and the degree of disparity at earlier stages of the criminal justice process,
through the elimination of parole and the severe reduction in the judiciary’s
ability to compensate for interactor disparity earlier in the criminal justice process. Also, although our empirical results show large changes in interjudge
nominal sentencing disparity, we have not measured disparity in time served.
Disparity in time served and disparity among decision makers earlier in the
criminal justice process are both subjects in need of further research.
We conclude by noting that elimination of disparity is only one objective
of a just sentencing system. Other commentators have argued that the present regime has purchased a reduction in interjudge sentencing disparity at
the price of undue severity in sentences, undue uniformity of those sentenced,66 and unwarranted complexity.67 Even if disparity from all sources
65

See Stith & Cabranes, supra note 4, at 78–103.
See Lott, supra note 10; Karpoff & Lott, supra note 10. These critics have argued that
the Guidelines have wrongly eliminated sentencers’ ability to consider the reputational effects of a conviction for white-collar and corporate offenders. They argue that as a result of
this inability to consider significant extralegal sanctions, variation in total penalties (incarceration, fines, reputational penalties, and lost earnings) has increased.
67
Albert Alschuler, The Failure of Sentencing Guidelines: A Plea for Less Aggregation,
58 U. Chi. L. Rev. 901 (1991); Stephen Schulhofer, Assessing the Federal Sentencing Process: The Problem Is Uniformity, Not Disparity, 29 Am. Crim L. Rev. 833 (1992); Daniel
Freed, Federal Sentencing in the Wake of the Guidelines: Unacceptable Limits on the Discretion of Sentencers, 101 Yale L. J. 1682 (1992).
66

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(judges, prosecutors, law enforcement agents, probation officers, and so on)
could be eliminated, the result would not necessarily be a just or fair sentencing system. In particular, implementation of the Sentencing Guidelines
and statutory minimum sentences have led to complaints of undue uniformity in sentencing. If a sentencing regime fails to take account of characteristics of the offense or of the offender that are believed to be relevant to a
just sentence, then its results may be unwarranted even if there is no measurable disparity because of the identity of particular decision makers.
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