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2004 Ajps Accountability and Coercion Is Justice Blind When It Runs for Office

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Accountability and Coercion: Is Justice Blind
when It Runs for Office?
Gregory A. Huber
Sanford C. Gordon

Yale University
New York University

Through their power to sentence, trial judges exercise enormous authority in the criminal justice system. In 39 American
states, these judges stand periodically for reelection. Do elections degrade their impartiality? We develop a dynamic theory
of sentencing and electoral control. Judges discount the future value of retaining office relative to implementing preferred
sentences. Voters are largely uninformed about judicial behavior, so even the outcome of a single publicized case can be
decisive in their evaluations. Further, voters are more likely to perceive instances of underpunishment than overpunishment.
Our theory predicts that elected judges will consequently become more punitive as standing for reelection approaches. Using
sentencing data from 22,095 Pennsylvania criminal cases in the 1990s, we find strong evidence for this effect. Additional
tests confirm the validity of our theory over alternatives. For the cases we examine, we attribute at least 1,818 to 2,705 years
of incarceration to the electoral dynamic.

I

n the United States, only courts can authorize the incarceration of individual citizens. Because appellate
courts review only a tiny fraction of criminal cases,
trial court judges occupy an enormously significant role
in administering criminal justice. There are nearly 5,000
state trial court judges. In 1998, they sentenced almost one
million convicted felons to a total of more than two million years in state jails and prisons (Pastore and Maguire
2002, Tables 1.81 and 5.40–5.44). Prosecutors charge and
juries convict, but trial judges’ sentencing authority ultimately governs how this coercive element of state power
is brought to bear on individual defendants.1

In 39 states, trial judges stand for reelection.2 Do
elections, which ostensibly assure accountability to citizens, degrade judicial impartiality? The near consensus
among legal scholars is that this tradition—particularly in
the form of partisan, competitive contests—is politically
unassailable but insidious in its potential for compromising judicial independence (e.g., ABA 1997, 2000; Croley
1995; Grodin 1988). At the same time, empirical studies
suggest that voters are almost entirely uninformed about
judge behavior (Dubois 1984; Hall 1999; Mathias 1990;
Sheldon and Lovrich 1983) and that trial judges retain
office at high rates (Aspin 1999; Baum 1983). But if this is

Gregory A. Huber is Assistant Professor of Political Science and Institution for Social and Policy Studies, Yale University, PO Box 208209,
New Haven, CT 06520-8209 (gregory.huber@yale.edu). Sanford C. Gordon is Assistant Professor of Politics, New York University, 726
Broadway, 7th floor, New York, NY 10003-9580 (sanford.gordon@nyu.edu).
This is one of several joint papers by the authors on criminal justice institutions and politics; the ordering of names reflects a principle
of rotation. We wish to thank the Institution for Social and Policy Studies at Yale and the Criminal Justice Research Center at The Ohio
State University (where Gordon served as assistant professor of political science in the beginning stages of this project) for their generous
financial support. We also gratefully acknowledge Brandon Bartels, Kevin Eirich, and Shaun Holness for superlative research assistance
and Paul Brace, Larry Baum, Laura Langer, Todd Lochner, Deborah Schildkraut, and three anonymous reviewers for valuable comments.
Earlier drafts of this article were presented in seminars at Columbia, George Washington, Northwestern, NYU, Princeton, and Yale where
we received additional constructive feedback. Finally, we would like to express our gratitude to the staff of the Pennsylvania Commission
on Sentencing for providing us with (and answering questions about) the sentencing data employed in this analysis.
1

Trial judges retain broad discretion over sentencing in nearly all noncapital cases. Defendants can usually appeal these sentences only on
very narrow grounds of law. Also, even though most cases are resolved via plea bargain, the presiding judge must approve the proposed
sentence.
2
There is substantial institutional variation in this regard. Incumbent trial judges run in competitive partisan elections in eight states, in
competitive nonpartisan elections in 21 states, and noncompetitive retention elections in 10 states. (In a retention election, the incumbent
judge’s name appears on the ballot with no opponents listed; she must receive more “yes” than “no” votes to keep her position.) In seven
other states, the legislature, governor, or a judicial nominating commission periodically evaluates incumbent judges for retention.

American Journal of Political Science, Vol. 48, No. 2, April 2004, Pp. 247–263
C

2004 by the Midwest Political Science Association

ISSN 0092-5853

247

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GREGORY A. HUBER AND SANFORD C. GORDON

the case, might not judges feel unconstrained by electoral
pressures?
This article develops and tests a theory specifying
the conditions under which trial judges will alter their
sentencing behavior to improve their electoral prospects.
Monitoring judicial behavior is difficult for voters, so even
a single instance of apparent judicial malfeasance can decisively influence an election. Certain characteristics of the
informational environment surrounding trial judge elections, however, make perceived underpunishment easier
to observe than perceived overpunishment—even though
voters may care about both (Gordon and Huber 2002). If
judges discount the future value of retaining office, they
will take greater pains to minimize the electoral consequences of underpunishment later in their terms. Thus,
the theory predicts unidirectional convergence: Trial judges
will become more punitive as their terms proceed.
Existing studies of electoral incentives predict bidirectional convergence: officials more liberal than their constituencies will become more conservative as election
approaches, while those more conservative will become
more liberal (e.g., Ahuja 1994; Elling 1982; Thomas 1985;
Wright and Berkman 1986). We predict that judges will
become more punitive irrespective of their position relative to their constituents’ preferences. Our theory is not
unique in anticipating unidirectional convergence, which
could also emerge as a consequence of a bias in the selection of judges that produces incumbents uniformly less
punitive than their constituents. Accordingly, we devise
a set of critical tests to distinguish among these different
accounts.
Our empirical analysis focuses on Pennsylvania,
where incumbent trial judges must face voters in noncompetitive retention elections every ten years. Examining
over 22,000 Pennsylvania trial court sentences for aggravated assault, rape, and robbery convictions in the 1990s,
we confirm that sentences for these crimes are significantly longer the closer the sentencing judge is to standing
for reelection. Our results also suggest the superiority of
our theoretical account over others. Finally, we impute a
baseline estimate of the aggregate increase in prison time
that occurs as a consequence of electoral incentives for the
cases we examine. We can attribute at least 1,818 to 2,705
years of additional prison time to this electoral dynamic.

Judicial Behavior and Electoral
Accountability
The method of choosing trial court judges is a matter of
substantial controversy.3 There are obvious democratic
3

See, e.g., Citizens for Independent Courts 2000, Dagger 1993, Price
1996, and Reidinger 1987.

concerns associated with removing voters from the choice
of officials who exercise enormous authority. At the same
time, electing trial judges may compromise other aspects
of judicial integrity. Foremost, elections may tie judges
too closely to the whims of public opinion (Croley 1995).
Elected judges presiding over controversial cases may base
their decisions on the potential political effects of those
decisions instead of legal precepts or an unbiased reading
of the facts of a case.

Representation and the Electoral
Connection: The Bidirectional
Convergence Hypothesis
To our knowledge, no systematic empirical research directly examines the effect of standing for election on the
behavior of criminal court trial judges.4 We build on theoretical and empirical work that conceives of electoral control as an agency problem. In this framework, elections
serve two fundamental roles. First, as selection devices,
they give voters the opportunity to pick agents whose preferences closely mirror their own (Fearon 1999). Limited
information, however, implies that voters will typically
not fully solve the adverse selection problem. To the extent that the preferences of officials diverge from those
of their constituents, elections can serve a second role
as incentive mechanisms, inducing officials to approximate constituents’ preferences (Barro 1973; Downs 1957;
Ferejohn 1986; Mayhew 1974; Miller and Stokes 1963).
In addition to implementing their policy preferences,
officials wish to retain office, either to enjoy its perquisites
or to influence policy in the future. Consequently, the effectiveness of electoral incentives will increase with the
official’s perception of the value of retention. This perception, however, is not static. For several reasons, over
the course of their terms officials will continuously reevaluate the balance between their own preferences and electoral concerns. First, they may discount the future value
of retaining office. At the beginning of their terms, when
the need to secure reelection and retain office is a far-off
prospect, they will place greater weight on implementing
their own preferred policies given their ideologies and the
information available to them. Toward the end of a term,
however, retaining office becomes a paramount concern.
4

Gibson (1980, 365–67) demonstrates that elected trial judges
who have experienced defeat at the polls are more responsive to
the sociopolitical characteristics of their districts than undefeated
ones. Kuklinski and Stanga (1979) examine the effect on aggregate judicial sentencing in different counties of voter support for a
California referendum endorsing less stringent penalties for certain drug crimes. A substantial literature addresses the behavior of
elected state supreme court justices (e.g., Brace and Hall 1997 and
Hall 1987, 1992, 1995).

ACCOUNTABILITY AND COERCION

Second, because elections are only periodic, voter evaluation of candidate performance, if it occurs at all, is likely to
be temporally proximate to each election (Popkin 1991).
As such, officials may ignore constituent preferences when
voters are inattentive. Voters may also simply have short
memories. (In a competitive electoral environment, these
effects are mitigated by a challenger’s ability to audit and
advertise an incumbent’s historical performance.)
Under ordinary circumstances, the incentive effects
of elections and their variation over time imply bidirectional convergence: as election approaches, officials will
moderate their behavior to more closely approximate
the wishes of some pivotal constituent (e.g., the median
voter). In its starkest form, this hypothesis suggests that
officials more liberal than that constituent will drift rightward over the electoral cycle, while more conservative officials will drift leftward. Further, convergence should be
constituency specific: For example, a senator who is conservative relative to the rest of the chamber may still be liberal
relative to her state; bidirectional convergence would predict a rightward shift as election approached (Ahuja 1994;
Wright and Berkman 1986).5

The Electoral Incentives of Trial Judges:
Unidirectional Convergence
The informational and institutional environment in
which trial judge elections occurs differs in fundamental respects from those of other elected officials. Voters
are uninformed about the most basic aspects of
these officials’ behavior and responsibilities (Hall 1999;
Mathias 1990; Sheldon and Lovrich 1983). Exacerbating
this paucity of information in certain institutional settings
is a lack of contextual cues like party labels (DuBois 1984),
because in many states judicial elections are nonpartisan. Further, where judges preserve office via retention
election, there are no challengers to provide voters with
information about incumbent performance (Aspin 1998;
Volcansek 1981). Also, until recently, many states imposed
restrictions on position taking by judicial candidates.
This paucity of information does not necessarily imply that elected trial judges will feel entirely unconstrained
by the pressures of public opinion. Rather, it alters the
manner in which they are constrained. Under conditions
of near absolute voter ignorance, information about the
adverse consequences of a single case, when publicized,
can be decisive in swaying voter opinion against a presiding judge. A Chicago trial judge, for example, lost
5
Elling (1982) and Thomas (1985) discuss convergence to constituency, but their statistical analyses do not measure constituency
preferences.

249
an election bid in 1986 as a consequence of acquitting
a defendant who had allegedly attacked a police officer
(Mount 1988). Our consideration of the availability of information to voters in these settings draws on McCubbins
and Schwartz’s (1984) distinction between types of oversight. Sustained, active “police patrol” oversight by voters
is costly. In the current context, passive “fire alarm” oversight occurs when asymmetrically well-informed actors
such as victims’ rights groups, police officers, and entrepreneurial legislators publicize individual instances of
perceived judicial malfeasance.
In the context of criminal justice, fire alarms when
sounded will nearly always correspond to perceived instances of underpunishment, not overpunishment. Nearly
all convicts claim their punishment is too severe, and
newsworthy cases of wrongful punishment by definition
come to light years after their imposition. Underpunishment, however, is more easily observed. News accounts of
recidivism make voters aware of convicts who committed
additional crimes after (seemingly) brief periods of incarceration. Further, victims’ families and the groups mentioned above have clearly defined incentives to publicize
specific instances of underpunishment. This asymmetry
would motivate even moderate or liberal voters to assume
the worst about defendants and judges.6
Certain stylized facts are sometimes misapplied to
suggest the ineffectiveness or nonexistence of fire alarm
oversight. First, we rarely see fire alarms pulled. A perfect
fire alarm, however, would never be pulled, because the
relevant agent would be deterred from malfeasance by the
mere threat of the alarm. In that case, the fact of voter ignorance in trial judge elections would be a consequence
of trial judge compliance with public opinion, rather than
a cause of judicial autonomy. Likewise, the fact that incumbent trial judges retain office at very high rates is not
by itself evidence of judicial independence from public
opinion. A high retention rate may signal total autonomy or total subservience—it is impossible to tell absent
additional information.
Strong evidence that elected judges do not ignore electoral concerns despite the low probability of loss comes
from judges themselves. Based on a survey of 645 trial
and appellate judges in 10 states with retention elections,
Aspin and Hall conclude, “[T]he behavior of retained
judges is shaped by the existence of retention elections
even though the probability of losing is low” (1994, 315).
At the same time, while judges may be attentive to public
opinion, it is unlikely that they are totally beholden to it.
As with other officials, judges have their own preferences
6
For a different treatment of asymmetric information revelation,
see Canes-Wrone, Herron, and Schotts (2001).

250
over criminal justice issues. Given these preferences and
access to additional information about specific cases that
the public lacks, judges are likely to desire to judge; that is,
to make distinctions among individual defendants based
on their perceived culpability, remorse, or likelihood of
recidivism.
If incumbent judges, like all officials, continuously
reevaluate the balance between the value of office and implementing their own preferences, the balance will shift
increasingly toward the former as election approaches.
Further, the fire-alarm nature of trial judge oversight suggests that because voters typically have access only to information about sentencing perceived as overly lenient,
the judge’s response will be unidirectional convergence. In
other words, our theory predicts that judges will become
more punitive, not more representative, over the course
of their terms.
Comparing our approach with that taken by Hall
(1992) is illuminating. She finds that liberal state supreme
court justices in states with short terms are less likely to
dissent from decisions upholding the imposition of the
death penalty. Her underlying causal story is similar to
ours in its informational basis: dissent reveals ideological extremity because voters can compare dissenters with
their peers. Such comparisons are impossible in the trial
judge environment, however, because each trial judge presides over different cases. Further, a sentence by itself is
generically uninformative because of a dearth of public information about individual trials. Only when police
unions, victims’ rights groups, legislators, and reporters
publicize cases are voters likely to conclude that a decision
was in some sense “incorrect.”
An alternative theory yielding a prediction of unidirectional convergence is preference-based: judges in all
districts may be uniformly more liberal than their constituents, either by training, or, in the eyes of conservative
critics, because of a proclivity for “coddling criminals.”7,8
This “uniform judicial liberalism” argument seems at best
incomplete, however, given the dissatisfaction of policy
liberals with criminal sentencing and the fact that voters
7

Hall (1995) finds evidence that state supreme court justices are
more likely to uphold death sentences in the last two years of
their terms. While she does not assume all justices are more liberal
than their constituents, her prediction rests on a preference-based
causal mechanism: the overwhelming support for the death penalty
among citizens of states included in her analysis. In a related study,
Brace and Hall (1997) find Democratic justices more likely to uphold death penalty convictions in states with short terms lengths.
8
In the 1990s roughly 85% of American respondents to the General
Social Survey answered “not harshly enough” when asked whether
they thought local courts dealt too harshly or not harshly enough
with criminals. Conservatives are only slightly more likely than
liberals to take this position (88% vs. 80%). See also Warr 1995.

GREGORY A. HUBER AND SANFORD C. GORDON

themselves (or their elected representatives) put judges in
office in the first place. An experiment by Roberts and
Edwards (1989) suggests that voters’ seemingly punitive
tendencies are primarily a consequence of their informational environment. When randomly selected respondents were shown a newspaper account of an assigned sentence, they almost uniformly preferred a more punitive
sentence. In contrast, among respondents asked to read a
more detailed account of the courtroom proceedings in
the case, a much smaller proportion believed the assigned
sentence was too lenient. Similar results are reported by
Roberts and Doob (1990). In other words, media coverage of criminal proceedings may explain the perception of
judicial leniency, a perception that would differ if voters
more closely monitored court proceedings.
In the empirical analysis that follows, we develop a set
of empirical tests that distinguish not only between the
bidirectional and unidirectional convergence hypotheses,
but also between a preference-based causal story for unidirectional convergence and our information-centered one.

Data and Method
Pennsylvania’s general jurisdiction trial courts are the
Courts of Common Pleas. We linked information about
sentencing in these courts, state elections, and judges’
backgrounds to create the dataset for our analysis.9 When
a judgeship vacates, replacements are selected via a partisan competitive election. (Mid-term vacancies may be
filled via gubernatorial appointment; the seat is considered open in the subsequent election.) In the primary election, judges compete for one or (87% of the time) both of
the major party nominations. In the general election, the
top vote getter(s) will fill the one or more open seats in
a particular judicial district. Judicial districts correspond
to counties, although in sparsely populated areas some
judicial districts encompass two counties. Once elected,
judges stand for reelection every ten years on the basis
of a noncompetitive retention vote. Importantly, not all
judges in a district are on the same electoral calendar.
Pennsylvania is in an ideal setting for our analysis.
Conventional wisdom concerning different methods of
electing judges suggests that judges will be most divorced
from the electoral connection when they serve long terms
and run in nonpartisan retention elections. If this is the
case, Pennsylvania trial judges operate in an institutional
9
Sentencing data were obtained from the Pennsylvania Commission
on Sentencing, elections data from the Pennsylvania Department
of State, and judges’ backgrounds from the Pennsylvania Manual.
Data on judges’ backgrounds was verified using data reported in
Steffensmeier and Hebert (1999).

251

ACCOUNTABILITY AND COERCION

context that will render them least sensitive to periodic
voter review. At the same time, however, these very institutional conditions are the ones our theory predicts will
produce unidirectional convergence toward punitiveness.
As in all states, the manner in which criminal cases
wind their way through the judicial system in Pennsylvania is enormously complex. Consequently, a full accounting of the intricacies of the criminal justice system and the
interrelated and strategic behavior of each actor in this
system is impractical in the current context. (We point
out some implications of the strategic behavior of prosecutors and defendants in the discussion section.) Here,
we discuss the range of options available to judges once a
defendant pleads guilty or a jury (or judge in a bench trial)
finds a defendant guilty of a misdemeanor or felony.10
Common Pleas judges generally exercise enormous
discretion in imposing sentences. Several constraints exist,
however. All crimes carry with them statutory maximum
sentences, and some have associated mandatory minima
as well. Additionally, the Pennsylvania Commission on
Sentencing (PCS) offers voluntary sentencing guidelines
for most felonies and misdemeanors. Judges are obliged
to take account of PCS instructions, but not to abide by
them.11 The Pennsylvania guidelines work as they do in
many other states: PCS classifies crimes by offense gravity
and defendants by prior record. Given those two variables, a judge can determine the recommended sentencing range by referring to a sentencing matrix. The guidelines expand the recommended penalty range upward or
downward by 12 months in the presence of aggravating
or mitigating factors. Additional matrices exist for separate sentence enhancements such as possession of a deadly
weapon during the commission of a crime.
For a given conviction, sentencing judges in Pennsylvania hand down both a minimum and maximum sentence. In cases involving incarceration, the defendant is
obliged to spend at least the minimum term in prison
before becoming eligible for parole. Subsequently, a state
parole board may or may not grant the defendant parole
up to the release time specified by the judge as the maximum sentence. Overall, the manner in which Pennsylvania incarcerates and releases defendants falls between the
10
As in all state courts, most cases are settled via plea bargain. Prosecutors and defendants in such instances negotiate a settlement,
subject to the approval of the presiding judge, whereupon the defendant pleads guilty to reduced charges or in exchange for a recommendation to the judge by the prosecutor of a reduced sentence.
11
42 Pa.C.S. § 9781 sets conditions for the appeal of an assigned
sentence. If a sentence is within the guideline range, the state or
defendant can appeal only for clerical mistakes or if the “application
of the guidelines would be clearly unreasonable.” If outside the
guideline range, the standard for appeal is reasonableness.

extreme case of fully indeterminate sentencing (in states
where a parole board is granted large discretion to reduce judicially imposed sentences) and fully determinate
sentencing (in states where parole has been abolished).

Analyzing Sentencing Behavior
The details of the Pennsylvania criminal justice system
suggest a need to avoid several pitfalls in our analysis.
First, we must account for a judge’s discretion in a given
case. We restrict attention to a class of felonies for which
judges both always have some discretion in sentencing and
typically assign prison time. There are a number of such
felonies, including rape, sexual assault, arson, robbery,
theft, and possession with intent to distribute Schedule
I and II narcotics. To keep the analysis as simple as possible, we focus our attention on all convictions in which
the highest count was some form of aggravated (felony)
assault, robbery, or rape. These encompass nearly all cases
with high offense gravity scores under the Pennsylvania
guidelines. We have 22,095 observations for discretionary
sentences imposed from 1990 to 1999 according to guidelines issued in 1988, 1994, and 1997.12
As noted above, judges assign two sentences for each
case. The dependent variable in our analysis is the smaller
of these two quantities, measured in months of incarceration. (Summary statistics for model variables appear
in Table 1.) This represents the determinate portion of
the judge’s discretion over sentencing, as defendants must
spend at least the smaller sentence behind bars before becoming eligible for parole.13
By statute, the smaller sentence imposed by the judge
cannot exceed one-half the larger sentence, which itself
cannot be greater than the statutory maximum. Additionally, for certain crimes, the law mandates a minimum
prison sentence. Together, these rules place upper and
lower boundaries on the range of a judge’s sentencing
options, creating a censoring problem. When a judge’s
smaller assigned sentence is the statutory minimum, the
dependent variable is left-censored. She may have preferred an even lower sentence, but was prohibited by
law from imposing it. When a judge’s smaller sentence is
one-half the statutory maximum, the dependent variable
is right-censored; the law prevents her from being more
12
The 1988 guidelines were revised in 1991. We have accounted for
these changes as well as alterations to the criminal code during the
period under study. In a given case, the authoritative guideline is
the one in place when the crime was committed. For example, if a
crime was committed in 1993 and the trial occurred in 1995, the
judge would use the 1991 guidelines, not the 1994 ones.
13
Our results are nearly identical if we examine the larger sentence
imposed.

252

GREGORY A. HUBER AND SANFORD C. GORDON

TABLE 1 Summary Statistics for Model Variables
Variable

Mean

Standard
Deviation

Assigned “Smaller” Sentence (months)
Guideline Minimum Sentence
Guideline Maximum Sentence
1988 Guidelines in Force
1994 Guidelines in Force
Defendant Male (1 = Yes)
Defendant Non-white (1 = Yes)
Defendant Age (years)
Non-negotiated Guilty Plea (1 = Yes)
Negotiated Guilty Plea (1 = Yes)
Deadly Weapon Enhancement (1 = Yes)
Deadly Weapon Use (1 = Yes)
Counts in Conviction
Rape (1 = Yes)
Robbery (1 = Yes)
Electoral Proximity
Judge Conservatism (Estimated)
Judge Age (years)
Judge Male (1 = Yes)
Judge Prosecution Experience (1 = Yes)
Republican Percentage of Vote
for Attorney General

24.83
20.07
32.55
0.54
0.26
0.91
0.66
28.57
0.20
0.45
0.11
0.02
2.17
0.06
0.52
0.44
13.77
53.07
0.78
0.36

28.73
19.22
24.27
0.50
0.44
0.28
0.48
9.06
0.40
0.50
0.31
0.14
2.29
0.24
0.50
0.28
1.35
9.37
0.41
0.48

0
0
6
0
0
0
0
14.73
0
0
0
0
1
0
0
0
10.05
35
0
0

240
120
120
1
1
1
1
88.42
1
1
1
1
90
1
1
1
15.03
83
1
1

0.43

0.15

0.20

0.74

Minimum

Maximum

N = 22,095, except for judge biographical data and judge conservatism, for which N = 21,776 due to missing data.

punitive. OLS regression produces biased coefficient estimates in the presence of censoring. In order to compensate
for censoring problems while retaining the OLS assumption of normally distributed errors, we employ a twolimit tobit model with observation-specific left and right
censoring points (Maddala 1983, 160–62; Tobin 1958).14
Employing this model also allows us to address a second
problem created by the 16% of cases in which no prison
time was imposed. In these cases, defendants were placed
on probation, forced to pay a fine, or given some other
form of limited restrictive punishment. We treat these
cases as left-censored, assuming they represent punishment less than the minimum jail time.15
The next issue we confront is that factors other than
electoral proximity and statutory limits may explain as14
The tobit model assumes the existence of a latent variable representing, in this case, the sentence the judge would prefer to assign.
It is fully observed only when the judge’s sentence falls between the
censoring boundaries, in this case the statutory minimum sentence
and one-half the statutory maximum.
15
This need not imply that nonincarcerative punishments are nonpunishment, only that they are, from the perspective of judges and
their constituents, less punishment than prison time.

signed sentences. A failure to control for these will only
bias our inferences if the omitted variables are correlated with the included ones. This can occur if different
judges—or the same judges at different points in their
electoral cycles—preside over different types of cases. In
other words, the threat of omitted variables is intimately
related to the possibility of nonrandom case assignment,
an issue to which we return below. Accordingly, employing
case- and judge-level controls is a conservative strategy. If
case assignment is nonrandom, these controls minimize
the threat of omitted variables bias. If it is random, they
improve predictive efficiency.
Crimes, defendants, and cases vary independently in
ways that will affect judges’ use of their discretion. The
Pennsylvania Sentencing Commission’s recommended
minimum and maximum sentences provide the ideal
measures to control for the severity of the offense committed and the defendant’s prior criminal record. Guideline
sentences reflect consensus within the state about appropriate punishments and the latitude judges should enjoy
given the defendant’s criminal history and the nature of
the crime. They incorporate an enormous amount of information, including victim age, the crime’s location, and

253

ACCOUNTABILITY AND COERCION

the level of violence.16 As such, they vary considerably
even when one restricts attention to a single crime. Additionally, we employ dummy variables for the applicable
sentence guideline regime (1988, 1994, or 1997).17 As supplementary controls for the nature of particular crimes,
we employ indicator variables that distinguish the type of
crime (rape and robbery—the baseline category is aggravated assault) and whether it involved the possession or
use of a deadly weapon. Finally, we account for the possibility that judges distinguish among defendants based
on demographic characteristics. These include age and
age-squared (because judges may treat young and old defendants more leniently than others), race, and sex.
Second, we control for variation in the disposition
of cases. In 51.5% of the cases in our sample, the defendant was convicted on more than one count. (In only
14% of cases was the defendant convicted on more than
three counts.) Because judges can decide whether to impose sentences consecutively or concurrently and which
counts to issue sentences on, we examine only the sentences associated with the most severe count on which
the defendant was convicted and control for the number
of counts. For most cases, this is the only count accompanied by a sentence (we omit from the sample the handful
of cases in which the defendant was given prison time
only for less severe counts).18 We also include indicator
variables for negotiated and nonnegotiated guilty pleas
(the baseline category is conviction at trial).
Finally, judges have their own sentencing ideology.
Note that in addressing the unidirectional convergence
hypothesis, we are not interested in the primitive preferences of the judges per se except to the extent that they are
needed as controls in our statistical models. Measuring
judicial ideology is difficult, so we take three approaches.
The first is to note that judges’ time-invariant ideological
proclivities cannot be systematically correlated with where
they happen to be in their own electoral cycles. This obviates the need to control for those proclivities. Second,
as a robustness check, we control for characteristics of
16
Alternatively, one may employ as controls the defendant’s prior
record score and the offense gravity score. Because these are ordinal
scales that change between guideline regimes and map nonlinearly
to the guideline sentences, we strongly prefer using the guidelines
themselves. Substituting the former for the latter, however, does
not alter our substantive findings.

the judges as proxies for their punitive tendencies. The
measures we employ are the judge’s age and age-squared,
whether the judge was male or female, and whether
the judge had prosecution experience (see Goldman
1975; Tate 1981).19 Third, as a more comprehensive robustness check, we employ judge-specific fixed effects
(i.e., one dummy variable per judge—425 variables total) to control for all time-invariant characteristics of the
sentencing judge. This approach is the most conservative
because it requires no a priori assumptions about how
judges’ preferences are derived.
Our primary hypothesis concerns the effect of electoral proximity. We code proximity as the number of days
elapsed in the judge’s term at the date of sentencing divided by 3,653. The measure is thus scaled from zero to
one, with zero representing 10 years until the next election,
and one an imminent retention vote (Election Day).20
We expect a positive coefficient on this measure: as proximity increases, so should assigned sentences. One other
variable, whose relevance we explain below, appears in
the summary statistics. It is a measure of district political
conservatism on criminal justice issues. Lacking a perfect
measure, we employ the district Republican share of the
two-party vote in the previous statewide attorney general
race.

Results
The presentation of empirical findings proceeds in two
stages. First, we provide statistical results that confirm
our primary hypothesis. Second, because these results are
consistent with several rival explanations, we devise and
implement a series of critical tests to distinguish the underlying causal mechanism.

Assessing the Unidirectional Convergence
Hypothesis: Initial Results
The unidirectional convergence hypothesis predicts an increase in punitiveness associated with an increase in electoral proximity. Table 2 displays the first round of tobit
estimates. The coefficient estimates in column (1) come
from a regression that includes the electoral proximity
19

The 1994 and 1997 guidelines did not result in unambiguous increases (or decreases) in punitiveness for the cases we study. Rather,
they altered the relative classification of case severity across crimes
(e.g., aggravated assault versus robbery) and within crimes (e.g.,
aggravated assault with significant bodily injury versus simple aggravated assault). Similarly, they revised the scaling of previous
offense history.

We were unable to use judge’s race or religion because it is not
reliably reported. Additionally, it is impossible to identify the partisan affiliation of most Pennsylvania judges. 87% of judges run in
both primaries, and a search of newspaper accounts and judicial
biographies failed to reveal partisanship in all but a tiny handful of
cases. We do not consider this a major concern, because the party
labels of local officials have different meanings in different parts of
the state.

18

20

17

The results do not differ substantially if we confine our analysis
to cases with only a single count.

For midterm appointments, we exclude all cases a judge hears
before her initial competitive election.

254

GREGORY A. HUBER AND SANFORD C. GORDON

TABLE 2 The Effect of Electoral Proximity on Sentencing: Two-Limit Tobit Models

Guideline Minimum
Guideline Maximum
1988 Guideline
1994 Guideline
Defendant Male
Defendant Non-white
Defendant Age
Defendant Age Squared
Non-negotiated guilty plea
Negotiated guilty plea
Deadly Weapon Enhancement
Deadly Weapon Use
Counts in Conviction
Rape
Robbery
Electoral Proximity

(1)
Year Effects

(2)
Year Effects

0.66
(11.18)
0.23
(5.11)
3.29
(2.19)
2.92
(3.27)
8.75
(16.81)
0.43
(1.34)
0.14
(1.69)
−0.0036
(2.99)
−6.40
(14.25)
−6.77
(19.05)
18.93
(25.15)
−1.07
(0.63)
1.68
(9.76)
14.03
(15.28)
6.33
(19.59)
4.29
(7.72)

−19.47
(8.61)

0.67
(11.35)
0.22
(4.97)
3.43
(2.24)
3.11
(3.45)
8.67
(16.59)
0.71
(2.18)
0.15
(1.73)
−0.0037
(3.00)
−6.32
(14.04)
−6.86
(19.16)
18.82
(24.98)
−0.88
(0.52)
1.70
(9.63)
14.01
(15.21)
6.40
(19.61)
3.70
(6.36)
0.27
(1.55)
−0.0025
(1.62)
2.91
(7.45)
0.42
(1.33)
−23.49
(4.65)

−50.90
(3.80)

21.40
(82.42)

21.38
(81.91)

20.55
(179.17)

Judge Age
Judge Age Squared
Judge Male
Judge Prosecution Experience
Intercept
Standard error
Log-likelihood

−79893.83

−78774.01

(3)
Year and Judge Effects
0.67
(16.20)
0.21
(6.36)
2.77
(2.35)
2.51
(3.32)
8.18
(14.80)
2.71
(7.72)
0.14
(1.83)
−0.0034
(3.13)
−5.14
(11.30)
−7.50
(19.61)
17.89
(32.35)
−1.17
(0.95)
1.73
(25.39)
12.81
(18.69)
6.90
(21.19)
2.94
(4.23)

−79034.04

Notes: Dependent variable is the minimum (smaller) sentence assigned by the judge. Absolute values of parameter
t-ratios are in parentheses. Eight year dummies omitted from all columns. 425 judge dummies ommitted from
column (3). N = 22,095 (4,527 left-censored cases, 690 right-censored) for columns (1) and (3). N = 21,776
(4,440 left-censored, 686 right-censored) for column (2). Robust standard errors are employed to estimate t-ratios
in columns (1) and (2). All models significant at the .001 level or better.

ACCOUNTABILITY AND COERCION

variable, the controls discussed above, and eight yearspecific fixed effects whose coefficient estimates we do
not report. The year variables allow us to account for
global changes in sentencing practices over time (e.g.,
those caused by uniform responses to changing state
conditions).
The estimates reported in the second and third
columns confirm our initial model’s insensitivity to
changes in model specification. Column (2) estimates
come from a regression that includes variables from
the first specification plus judge background variables.
Column (3) estimates come from a model that includes
variables from the first specification plus 425 judgespecific fixed effects whose coefficients we do not report.
As stated above, this last specification permits us to control
for all static characteristics of the sentencing judge (e.g.,
ideology).21
Before proceeding to our test of the primary hypothesis, we examine the parameter estimates for the control variables. The results are without exception consistent with our expectations and prior research on criminal
sentencing (e.g., Adelstein 1978; Albonetti 1997; Bushway
and Piehl 2001; Curran 1983; Landes 1971; Miethe and
Moore 1985; Zingraff and Thompson 1984) and suggest
the validity of our specification and coding. Increases in
the guideline sentences lead to increases in actual sentences. A nonmonotonic relationship exists between age
and length of incarceration. (Per the estimates from the
first specification, 20 year-old defendants can expect to see
the most prison time.) Men receive longer sentences than
women, and the specification in column (1) suggests that
all else equal, judges hand down sentences 13 days longer
for nonwhite defendants than for their white counterparts.22,23 One of the strongest predictors of additional
21

We believe this fixed-effect approach is asymptotically consistent,
since the number of convictions will approach infinity faster than
the number of judges (which is fixed) and years (see Heckman and
MaCurdy 1980). In the current setting, consistency appears to be
only a theoretical issue. Fixed-effects OLS (whether restricted to
uncensored observations or for all cases) produces nearly identical
results.
22

Throughout, we report the effect of changes in independent variables on the latent rather than on the observed dependent variable.
Because it reflects the sentence a judge would hand down in the
absence of statutory constraints, this quantity is the more easily
interpretable of the two. To calculate for a particular observation
the estimated effect of a change in an independent variable on the
observed dependent variable, multiply its coefficient by the probability the observation is in the censoring region (Greene 2000, 909).
Evaluated at the data sample means and based on the current set of
estimates, that probability is approximately 0.68.
23
The effect is larger and significant in columns (2) and (3). We
consider this to be disturbing evidence of sentencing disparity, an
important topic but one beyond the scope of this article.

255
punishment is possession of a deadly weapon. Once one
controls for possession of a weapon, however, using it
does not significantly add to the sentence. (This is not
surprising because using a weapon typically increases the
classified severity of the crime, in turn raising the guideline minimum sentence—which is already controlled for.)
We also point out an interesting finding concerning
the disposition of cases. The negative coefficient on the
negotiated plea variable provides information about the
way that plea-bargaining typically occurs (Taha 2001). A
positive coefficient would suggest that the dominant form
of negotiation between prosecutors and defendants concerns charge reduction: a defendant might plead guilty to
a lesser charge and receive a penalty that, while stiff for the
reduced charge, is nonetheless lighter than the penalty for
the higher count. The negative coefficient that we observe
across specifications suggests that negotiation typically
concerns the length of the sentence that the prosecutor
recommends to the judge given a particular charge, more
often than on the charge itself.
Next we consider the effect of electoral proximity. It
is important to consider how one should interpret a null
finding for this variable. A failure to detect unidirectional
convergence is consistent with three accounts of judicial
behavior. First, it might demonstrate judicial autonomy.
Judges may behave in a manner totally independent of
the preferences of their constituents and sentence as they
see fit. Second, a null finding could indicate judicial subservience: judges may prioritize the desires of their constituents throughout the electoral cycle. Finally, it could
indicate bidirectional convergence, wherein some judges
become more conservative as election nears while others
become more liberal, leading to zero net effect.
We need not confront this indeterminacy, however.
In all specifications, the parameter estimate for electoral
proximity is positive and highly statistically significant
(one can reject the null hypothesis at above the 0.001
level in all three specifications). All else equal, the sentence imposed by a judge whose election is imminent is
likely to be about three to three-and-one-fourth months
longer (depending on specification) than if the judge were
recently elected or retained. A standard deviation shift in
electoral proximity raises an assigned sentence by about
25 to 36 days. The magnitude of the result is substantial.
The median sentence in the sample is about 12 months.
Consequently, a standard deviation increase in electoral
proximity produces a 7 to 10% increase from the median
sentence, while a change from zero to one produces an
increase of 24 to 37%.
An even more useful measure of the impact of electoral proximity can be derived by imputing an estimate
of the aggregate increase in prison time stemming from

256

GREGORY A. HUBER AND SANFORD C. GORDON

judges’ desire to secure reelection. Assume that on the
first days of their terms, judges feel completely unconstrained by the electoral consequences of their sentencing
decisions. For each sentencing decision in our dataset, we
can calculate an estimate of the sentence the judge would
have imposed had she just been elected or retained, and
compare that with an unconstrained prediction. Adjusting for statutory constraints on sentencing, the coefficient
estimates in column (1) suggest that the proximity effect
augmented sentences for the cases in our dataset by 2,705
years (+/−681), or 5.9% of total prison time.24 For two
reasons, this is a conservative estimate. First, even a judge
serving her first day in office may feel somewhat constrained by the future electoral consequences of her actions. Given lifetime tenure, she might sentence even less
punitively. Second, these figures correspond only to the
cases in our Pennsylvania dataset, which comprise only a
fraction of total convictions in the state.

Distinguishing the Underlying
Causal Mechanism
Findings of unidirectional convergence constitute preliminary evidence in favor of our informational theory. However, an alternative causal mechanism may have generated
these estimates. As discussed above, unidirectional convergence is consistent with an alternative account (“uniform judicial liberalism”) in which all judges are more
lenient than their constituents. Also, bidirectional convergence may be at work, but with a sufficiently large
proportion of judges to the left of their constituents to
lend the appearance of unidirectional convergence (“lopsided bidirectional convergence”).
To distinguish our informational story from these
accounts, we conduct a series of critical tests. If lopsided
bidirectional convergence generated our finding, then we
would anticipate that at least some judges would become
more lenient over the course of their terms. Our theory, by
contrast, predicts that no judges will become more lenient.
The most punitive judges will simply exhibit minimal or
no change during their terms, because their sentences are
already sufficiently punitive to minimize the risk of a fire
alarm being pulled. The approach we adopt to distinguish these accounts modifies the one suggested by Segal,
Songer, and Cameron (1994). In a study of appellate court
jurisprudence, they first conduct a logit analysis of judges’
votes on time-invariant judge characteristics, employing
24
Parameter estimates from column (2) suggest a total sentence
augmentation of 2,313 years (+/−698); estimates in column (3)
suggest 1,818 years (+/−845). Simulated 95% confidence intervals
are in parentheses.

the linear prediction from the model as a judge’s ideology score. They then employ these scores in subsequent
analyses of appeals court decisions.
Our approach differs in several respects. First, the
theoretically relevant quantity in our estimator is the interaction of ideology and electoral proximity. If our theory
is valid, then judges of all ideological stripes should have
nonnegative proximity effects. Second, they employ a vector of judge characteristics appropriate for the study of
federal appellate judges. In contrast, we employ the trial
judge characteristics discussed in the previous section.
Further, while they employ the ideology of the appointing
president as a component of judicial ideology, our need
to distinguish the incentive and selection effects of elections makes the inclusion of a district ideology measure
inappropriate for this test. (Such a measure is appropriate
for a separate test, discussed below.) Third, a two-stage
approach will tend to produce biased standard errors because the linear prediction used in the second stage is a
stochastic regressor. We therefore estimate the model using both the two-stage and a full information maximum
likelihood (FIML) approach.25 Parameter estimates from
each model are displayed in Table 3.
The second specification employs county fixed effects
as additional controls for unexplained heterogeneity. Note
the similar results across specifications: the conditional
effect of electoral proximity given an ideology score of
zero is positive in each, although statistical significance is
reduced slightly in the FIML estimation. Also, the coefficient on the interaction with the ideology score is consistently negative, implying that the proximity effect is reduced for more punitive judges. If lopsided bidirectional
convergence is at work, however, then the effect of electoral proximity on more punitive judges should not only
be smaller—it should be negative. For the estimates for
columns (1) and (2), the most punitive judge has an ideology score of 15.03. Substituting, we find that the net proximity effect for that judge is positive 2.72 or 2.76 months
25

We thank an anonymous reviewer for the initial idea. A judge’s
age, sex, and prosecutorial experience were used to construct our
proxy measure of judicial preferences (e.g., Goldman 1975; Tate
1981). See also supra, note 19. In the two-stage approach, stage one
consisted of running a tobit model predicting judicial sentences including the judge data and additional control variables (The results
reported here are robust to alternative statistical specifications). We
then used the observed coefficients on the judge variables to construct the ideology measure: Judge Conservatism = −0.4058058 ∗
judge age −0.0035203 ∗ judge age squared + 2.944905 ∗ judge
male + 0.3898156 ∗ prosecution experience. The FIML estimator works as follows: Letyi∗ be the latent punishment variable, z i a
vector of judge-specific characteristics, and x i a vector of other variables (including electoral proximity). The latent regression model,
estimated as a tobit, is yi∗ = xi ␤ + z i ␥ + ␰ proximity i (z i ␥ ) + εi ,
with ␰ the relevant interaction coefficient. Code is available upon
request.

257

ACCOUNTABILITY AND COERCION

TABLE 3 Judicial Preferences and Electoral Proximity: Two-Limit Tobit Models
(1)
Year Effects
2-Stage
Guideline Minimum
Guideline Maximum
1988 Guideline
1994 Guideline
Defendant Male
Defendant Non-white
Defendant Age
Defendant Age Squared
Non-negotiated guilty plea
Negotiated guilty plea
Deadly Weapon Enhancement
Deadly Weapon Use
Counts in Conviction
Rape
Robbery
Electoral Proximity

0.67
(11.38)
0.22
(4.94)
3.43
(2.24)
3.10
(3.43)
8.66
(16.58)
0.71
(2.19)
0.15
(1.73)
−0.0037
(3.00)
−6.34
(14.11)
−6.86
(19.20)
18.79
(24.93)
−0.88
(0.52)
1.69
(9.64)
14.01
(15.21)
6.42
(19.67)
13.44
(2.39)

(2)
Year and County
Effects, 2-Stage
0.67
(11.43)
0.23
(5.23)
3.91
(2.55)
3.21
(3.56)
8.18
(15.91)
2.85
(8.32)
0.11
(1.32)
−0.0032
(2.60)
−5.47
(11.62)
−7.85
(20.57)
18.14
(24.04)
−0.83
(0.49)
1.75
(9.56)
12.91
(14.18)
6.78
(20.76)
14.68
(2.62)

Judge Age
Judge Age Squared
Judge Male
Judge Prosecution Experience
Judge Conservatism
Judge Conservatism ∗ Electoral Proximity
Intercept
Standard error
Log-likelihood

(3)
Year Effects,
FIML
0.66
(15.54)
0.22
(6.52)
3.48
(2.88)
3.13
(4.06)
8.65
(15.21)
0.71
(2.17)
0.15
(1.86)
−0.0037
(3.30)
−6.33
(14.72)
−6.88
(19.59)
18.80
(33.56)
−0.95
(0.76)
1.69
(24.71)
14.03
(20.04)
6.39
(19.31)
16.65
(1.64)
0.58
(1.87)
−0.0053
(1.90)
3.79
(5.97)
0.87
(1.71)

1.20
(6.52)
−0.71
(1.77)
−30.54
(9.92)

0.71
(3.76)
−0.79
(1.97)
1.94
(0.19)

−0.69
(2.43)
−32.54
(3.76)

21.38
(81.91)

21.01
(80.54)

21.32
(178.16)

−78773.69

−78377.44

−78850.52

Notes: Dependent variable is the minimum (smaller) sentence assigned by the judge. Absolute values of parameter t-ratios are in
parentheses. Eight year dummies omitted from all columns. 66 county dummies omitted from column (2). N = 21,776 (4,440 left-censored
cases, 686 right-censored). Robust standard errors are employed to estimate t-ratios in columns (1) and (2). All models significant at the
.001 level or better.

258
(depending on specification). In the FIML estimation, the
most punitive judge has an ideology score of 20.34. The estimated net proximity effect for that judge is 2.5 months.
If even the most conservative judge in the sample becomes
more punitive over the course of the term, then lopsided
bidirectional convergence cannot explain our findings.
It is possible, however, that judges are all more liberal
than their constituencies. If uniform judicial liberalism
generated our findings, then it should be the case that the
effect of electoral proximity will be largest in the most
conservative districts: Liberal judges would have to traverse a greater ideological distance when sentencing in
order to appeal to their constituents. If our informational
story is correct, however, the effect of electoral proximity
should be largest in the most liberal districts. On average,
judges will reflect the preferences of their constituents
with some error. All will face similar incentives to become
more punitive, but the judges coming from the most conservative districts will be punitive to begin with, and will
consequently have less distance to traverse.
The uniform judicial liberalism account, in other
words, predicts a positive coefficient on the interaction between electoral proximity and district conservatism, while
our informational account predicts a negative coefficient.
Initial estimates, employing our measure of district conservatism (Republican vote share in the previous statewide
attorney general election), are displayed in columns (1)
and (2) of Table 4. As anticipated by our informational
theory, the coefficient on the interaction is negative and
statistically significant in both specifications.26
To make our results more interpretable, we display
the net effect of electoral proximity in months (and its
95% confidence interval) as a function of district conservatism in the top two panels of Figure 1. Viewed across
judicial districts, the average Republican vote share in an
attorney general race was 58.1%. In a district one standard
deviation more liberal than the average, a judge facing an
imminent retention vote will sentence 2.21 to 2.66 months
longer than one who has just been elected or retained. At
the same time, in a county one standard deviation more
conservative than average, the proximity effect is −3.37
to −5.1 months.
This last finding is troubling at first glance. Our theory predicts that no judges should become more lenient
over their electoral cycles, yet the model implies that
judges in a number of counties will do just that. This
apparent evidence against out theory, however, is an artifact of the model’s specification. As is evident from the
26
As a robustness check, we also employed a more traditional measure of conservatism: the Republican margin in the two-party vote
for President. The results were nearly identical.

GREGORY A. HUBER AND SANFORD C. GORDON

top panels of Figure 1, the specification of the interaction
effect is linear, which forces the proximity effect to be negative for some values of district conservatism. A more flexible approach is to employ a nonlinear interaction specification such as the quadratic, as we do in columns (3) and
(4). The lower panels of Figure 1 display the estimates of
the proximity effect given the more flexible specification.
These plots confirm our theory’s predictions: in liberal
districts, the effect of electoral proximity is large and statistically significant, while in moderate to conservative
districts, it is statistically indistinguishable from zero. At
no point is the effect negative and significant.
To summarize, all judges, even the most punitive, increase their sentences as reelection nears, demonstrating
that our finding is not attributable to bidirectional convergence with a preponderance of lenient judges. Similarly,
the proximity effect is largest in the least punitive counties,
thereby ruling out the possibility that uniform judicial liberalism explains the observed relationship. Overall, these
tests provide strong support for our informational model.

Discussion
Four plausible objections may be raised against our findings. First, perhaps judges simply “learn” to become more
punitive as they grow older and more experienced. We
offer two responses. First, the model estimates reported
in column (2) of Table 2 control for judge age. Second,
we reestimated the models reported in Table 2 accounting for the number of years a judge has been on the bench
(and that quantity squared). The proximity effect remains
positive and statistically significant, although collinearity
reduces the magnitude of the coefficient to between 1.51
and 2.35, depending on specification.
We also considered whether the proximity effect
changes from term to term. On the one hand, there are reasons to suspect that judges will respond to impending electoral review less after they have been through the process
at least once. Judges’ terms in Pennsylvania last 10 years,
and the median judge in our dataset first achieves her position at age 45. Half of all judges, then, decide whether to
run for retention a second time at age 65 or older. Since retirement is a likely option, the value of retaining the office
may have declined by that point. Additionally, judges learn
over time what they must do to be retained. A comfortable retention margin the first time around may prompt
a decrease in concern about appearing soft on crime. On
the other hand, these same effects may actually magnify
the electoral proximity effect. Judges who have won retention before may recognize that only what they do late in
their terms is noticed and consequently become even less

259

ACCOUNTABILITY AND COERCION

TABLE 4 Constituent Preferences and Electoral Proximity: Two-Limit Tobit Models
(1)
Year Effects
Guideline Minimum
Guideline Maximum
1988 Guideline
1994 Guideline
Defendant Male
Defendant Non-white
Defendant Age
Defendant Age Squared
Non-negotiated guilty plea
Negotiated guilty plea
Deadly Weapon Enhancement
Deadly Weapon Use
Counts in Conviction
Rape
Robbery
Electoral Proximity
Republican Percentage of Vote
for Attorney General
Republican Percentage of Vote
for Attorney General Squared
Republican Percentage of Vote for Attorney
General ∗ Electoral Proximity
Republican Percentage of Vote for Attorney
General Squared ∗ Electoral Proximity
Intercept
Standard error
Log-likelihood

0.65
(11.12)
0.23
(5.13)
4.06
(2.70)
2.98
(3.33)
8.75
(16.93)
1.70
(5.22)
0.17
(2.01)
−0.0040
(3.27)
−6.24
(13.93)
−6.99
(19.73)
18.49
(24.49)
−0.97
(0.57)
1.71
(9.85)
14.01
(15.31)
6.75
(20.76)
19.75
(10.73)
30.45
(15.97)

−36.55
(9.58)

−34.71
(13.94)
21.31
(82.17)
−79762.75

(2)
Year and County
Effects
0.65
(11.17)
0.24
(5.41)
3.63
(2.41)
2.84
(3.21)
8.30
(16.23)
2.85
(8.41)
0.13
(1.53)
−0.0034
(2.80)
−5.34
(11.40)
−7.60
(20.10)
17.94
(23.83)
−0.94
(0.56)
1.75
(9.73)
12.99
(14.34)
6.89
(21.26)
17.16
(9.26)
0.67
(0.15)

(3)
Year Effects
0.65
(11.11)
0.23
(5.18)
3.75
(2.49)
2.82
(3.16)
8.67
(16.79)
1.68
(5.16)
0.17
(2.04)
−0.0040
(3.30)
−6.25
(13.99)
−7.03
(19.88)
18.27
(24.22)
−0.82
(0.49)
1.69
(9.68)
13.94
(15.22)
6.77
(20.85)
32.75
(6.26)
12.23
(0.92)
21.02
(1.42)

(4)
Year and County
Effects
0.65
(11.12)
0.24
(5.48)
3.41
(2.27)
2.73
(3.09)
8.29
(16.20)
2.87
(8.45)
0.13
(1.49)
−0.0034
(2.76)
−5.26
(11.23)
−7.55
(19.96)
17.81
(23.68)
−0.87
(0.53)
1.75
(9.67)
13.05
(14.39)
6.92
(21.34)
33.59
(6.40)
9.45
(0.64)
−6.84
(0.41)

−30.19
(7.87)

−104.53
(4.20)

−116.90
(4.66)

19.25
(2.10)
20.97
(81.14)
−79424.8

78.27
(2.84)
−30.61
(8.36)
21.28
(82.22)
−79733.28

100.45
(3.60)
−23.34
(1.52)
20.96
(81.25)
−79412.66

Notes: Dependent variable is the minimum (smaller) sentence assigned by the judge. Absolute values of parameter t-ratios are in parentheses.
Eight year dummies omitted from all columns. 66 county dummies omitted from columns (2) and (4). N = 22,095 (4,527 left-censored cases,
690 right-censored). Robust standard errors are employed to estimate t-ratios in all columns. All models significant at the .001 level or better.

260

GREGORY A. HUBER AND SANFORD C. GORDON

FIGURE 1 The Net Effect of Electoral Proximity as a Function
of Constituent Preferences

Net Proximity Effect (Months)

(1) Linear Interaction

(2) Linear Interaction, Controls for County

20

20

15

15

10

10

5

5
0

0
-5

0.2

0.3

0.4

0.5

0.6

-10

-15

-15

0.4

0.5

0.6

0.7

(4) Nonlinear Interaction, Controls for County

20

20

15

15

10

10

5

5
0

0
-5

0.3

-5

-10

(3) Nonlinear Interaction
Net Proximity Effect (Months)

0.2

0.7

0.2

0.3

0.4

0.5

0.6

0.2

0.7

0.3

0.4

0.5

0.6

0.7

-5
-10

-10

-15

-15

Republican Attorney General Vote Share

Republican Attorney General Vote Share

punitive early on (if they so desire). Thus, the net proximity effect—the difference between a judge’s sentencing
just after retaining office and just before facing the voters again—might actually increase because some veteran
judges’ early term sentencing is even less punitive.
We reproduced the specifications in Table 2, this time
including a measure of how many terms a judge has served
and an interaction of this quantity with the proximity
variable. We continue to find a statistically significant
electoral proximity effect, but this effect declines somewhat in a judge’s subsequent terms. The coefficient on
electoral proximity becomes larger, ranging from 3.91 to
6.22, while the coefficient on the interaction between term
and proximity receives a negative coefficient that ranges
between −.46 and −1.28. (We also find that the number
of terms a judge serves leads to larger sentences in the
column (1) and (2) specifications [1.47 and 1.79 months
per term, respectively, both statistically significant] and
a statistically insignificant and negative effect [−.66] in
the column (3) specification.) These results confirm that
electoral proximity is not strictly a first-term effect, although the magnitude of the effect does appear to decline
somewhat in later terms.
A second concern may be raised about our measure
of district punitiveness, which we employ to reject the
uniform judicial leniency hypothesis. This measure, the
Republican vote share in the last statewide attorney general’s race, is highly correlated with one other salient feature of judicial districts: the number of judges voters are
asked to review (the correlation is −0.88 for the cases

in our dataset).27 In districts with fewer judges, voters
might have an easier time monitoring judges throughout
the course of their entire terms via active “police-patrol”
oversight.28 If this is the case, our finding concerning district punitiveness might actually be caused by variation in
the ease of voter monitoring. To eliminate this alternative
explanation for the findings reported in Table 4, we reestimated those models including the number of judges in
a district and that number squared plus these quantities
interacted with electoral proximity. With the inclusion of
these additional variables, we still find that the proximity
effect is largest in the most liberal districts. We also find
that the proximity effect is larger in districts with more
judges.
Third, any nonrandom assignment of cases to judges
may bias our results. Whether or not different judges hear
systematically different cases, however, will not create the
observed proximity effect unless individual judges hear
different types of cases at different points during their
terms and we did not control for this variation. Before
considering case assignment methods directly, it is important to remember that all of our statistical models account
for variation in case seriousness, judicial discretion, case
27

All other static features of counties that might create unobserved
heterogeneity are controlled for in our judge fixed-effects specification. Additionally, the estimates reported in columns (1) and (2)
of Table 2 are robust to the inclusion of county fixed effects.
28
Alternatively, in districts with many judges, a judge might believe
that a “bad” decision would be drowned out by other news or
unlikely to be attributed to her at election time.

261

ACCOUNTABILITY AND COERCION

disposition, and defendant characteristics directly. To be
sure that no additional assignment-related factors were
influencing our results, we investigated how cases are actually assigned. In small counties with only one or two
judges, this is not a concern. However, selection may play
a role in large counties such as Philadelphia or Allegheny.
We contacted the Administrative Office of the
Philadelphia Courts to inquire about case assignment
methodology. In Philadelphia, cases are divided into three
pools: homicides, other major cases (which encompass
those that we consider), and minor (“list room”) cases.
During their first two to three years on the bench, judges
are generally restricted to list room cases. After that period, judges are randomly selected to trials, with slightly
reduced selection probabilities afforded to historically
slow judges with large open caseloads.29 As an additional
supplementary test, we therefore reran the models reported in Table 2 for all judges in Philadelphia after discarding cases heard by judges in their first three years of
their first term.30 The proximity coefficient remains large
and statistically significant.
Finally, one might believe that the electoral proximity effect is incorrectly attributing to judges the strategic
behavior of other officials in the criminal justice system.
Prosecutors, for instance, might become more punitive
as their reelection nears. The nature of judicial elections
in Pennsylvania, however, allows us to reject this explanation. In a given district, a prosecutor serves a fixed
four-year term. Judges, however, serve ten-year terms and
within a district judges are on different electoral calendars.
In other words, if prosecutors did ratchet up their efforts
to secure more punitive sentences in a given year, this
would not correspond to higher values of the proximity
measure because judges serve longer terms and judges are
in different places in their electoral cycles. Also, our case
disposition controls and year fixed effects would capture
any uniform changes in how cases are handled across time.
Finally, we can directly control for the effect of prosecutor behavior in our analysis within Philadelphia County
reported above. There is only a single elected prosecutor in Philadelphia, and the year-effects will control for
variation in her effort to secure different sentences over
time. With these controls in place, the proximity effect for
judges persists.
Finally, suppose prosecutors and defendants anticipated a judge’s electoral concerns and altered their court29
We have confirmed that there is no correlation between case seriousness (measured using the guideline minimum sentence) and
electoral proximity after the first three years of a judge’s first term.
30
The findings for Philadelphia County are also robust to the inclusion of the judge experience measures discussed in this section.

room strategies accordingly. Defense attorneys might seek
to delay sentencing until after an election, whereas prosecutors might seek to accelerate it. If defense tactics in this
regard dominate the sequence, this would bias against our
findings, as judges would have fewer cases with which to
demonstrate punitiveness toward the ends of their terms.
If prosecutor tactics dominate, this would contribute to
our finding, but not reject our basic story. Such anticipative action would still constitute evidence that judges
take electoral considerations into account. Electoral effects might also filter into the plea bargaining between
defendants and prosecutors, with prosecutors able to extract higher sentences from defense counsel when cases
are before a judge whose reelection is near. This would
again confirm our finding—bargaining about sentencing
takes place in the shadow of a judge’s increasing punitiveness as reelection nears. Insofar as the other factors that
influence bargaining are unlikely to vary systematically
over the course of a judge’s term, they cannot explain our
results.

Conclusion
Our analysis provides insight into two important areas of
concern for political scientists: the state’s use of coercion
and the nature of representation. Judges assign sentences
to convicted criminals, determining in part how governments use their authority to deny liberty. We provide evidence that judges become significantly more punitive the
closer they are to standing for reelection. In Pennsylvania, for the time period and crimes we analyze, we can
attribute more than two thousand years of additional incarceration to this dynamic. This may imply judges sentence too harshly near elections, or too leniently early in
their terms. In either case, it implies a downside to electoral control of judges. The power to incarcerate is applied
on a case-by-case basis, and we can attribute substantial
inconsistency in the exercise of this power to the electoral
connection.
Critics of judicial election might be tempted to seize
on this result to justify removing judges from direct citizen
review. It is not clear, however, that the same phenomenon
would not occur with any other form of periodic review—
for example, by governors or special commissions. Moreover, there may be larger costs associated with removing
judges from such review. The electoral connection may
have pernicious effects on consistency, but for some, this
may be an acceptable side effect of ensuring that judges’
decisions are at least partially representative of citizen
preferences.
Our research also provides insight into the relationship between citizens and elected officials. Elected judges

262
in Pennsylvania are bound by the (weak) threat of losing
office, and alter their behavior accordingly. We can thus
say with near certainty that at least in this case, elections
are not simply a method of selecting “good types” (Fearon
1999). Further, our analysis suggests an important point
about information flows in electoral environments where,
under ordinary circumstances, voters know almost nothing about officials’ behavior. Because voters are more
likely to learn about perceived instances of underpunishment than overpunishment, reelection-minded trial
judges might take steps to sentence more harshly than
they would if they were not bound by periodic review. Our
statistical tests demonstrate that it is this mechanism, and
not a bias in selection that makes judges unusually liberal
relative to their constituents, that generates the observed
sentencing variation.
This research sets the stage for more extensive inquiry into the comparative politics of judicial selection
(cf. Brace and Hall 1995). Even in the low information
setting created by nonpartisan retention elections, and
despite the ten-year terms that afford judges significant
distance from electoral review, Pennsylvania trial judges
appear to respond to the potential electoral consequences
of sentencing leniently by becoming more punitive as reelection approaches. At the very least, we can conclude
that the retention method does not remove politics from
the sentencing process.
No method of selection is perfect, but at present we
know little about the trade-offs associated with mechanisms other than the one studied here. We wish to build
on this project to compare across term length, informational environment (competitive versus noncompetitive,
partisan versus nonpartisan), immediate political principals (voters, governors, legislatures), and court (general
jurisdiction versus appellate). Parsing out the effects of
this variation requires additional theoretical and empirical work.
This, of course, is not an easy task. Gathering data
about the behavior of trial court judges is time consuming and expensive. Understanding the restrictions
(formal and informal) placed on judicial discretion is
similarly complicated. Comparative analysis of electoral
systems is made possible, however, by the enormous institutional variation afforded by the American states, which
serve in this regard as institutional “laboratories,” to borrow Louis Brandeis’ well-known metaphor. This variation permits us to test theoretically derived claims about
responsiveness, representation, and fairness in different
settings while holding fixed the broad contours of the legal system. Further, differences in the methods employed
to select trial judges will contribute to our understanding
of how the techniques used to choose and subsequently
evaluate other elected officials influence their behavior.

GREGORY A. HUBER AND SANFORD C. GORDON

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