Preference Heterogeneity of the Judiciary
and the Composition of Political Jurisdictions
Claire S.H. Lim∗
Cornell University
Bernardo Silveira†
WUSTL
James M. Snyder, Jr‡
Harvard University §
December 23, 2014
Abstract
We study the influence of judges’ race and party affiliation on sentencing decisions
in Texas state district courts, using data on approximately half a million criminal cases
from 2004 to 2013. Contrary to several studies on the influence of decision-makers’
race and political orientation, we find precisely-estimated effects that are near zero, conditional on geographic factors such as voter preferences. Despite these results, we find
substantial cross-judge heterogeneity in sentencing harshness. To assess the influence of
cross-judge heterogeneity on sentencing disparity within and across counties, we exploit
the unique overlapping structure of Texas state district courts, where different judicial
districts partially overlap with one another. Using this structure, we evaluate whether
having larger judicial districts that share a pool of judges—rather than small districts
with lone judges—mitigates the cross-country disparity in sentencing harshness.
Keywords: Court, Criminal Sentencing, Race, Party, Political Jurisdictions
JEL Classification: H1, H7, K4
∗ Department
of Economics, 404 Uris Hall, Ithaca, NY 14853 (e-mail: [email protected])
School of Business, Campus Box 1133, One Brookings Drive, St. Louis, MO 63130-4899 (e-mail:
[email protected])
‡ Department of Government, 1737 Cambridge St, Cambridge, MA 02138 (e-mail:
[email protected])
§ We thank Andrew Daughety, Nate Hilger, Christine Jolls, Jennifer Reinganum, Maya Sen, and seminar and
conference participants at Princeton, U.Chicago, Emory, ALEA and NBER for their comments and suggestions.
† Olin
1
1
Introduction
The influence of race on the behavior of public officials, adjudicators and other decision
makers has long been an important issue in the social sciences. Several recent papers find
that race exerts a significant influence on law enforcement (Antonovics and Knight (2009)),
criminal trials (Anwar et al. (2012)), as well as sports refereeing (Price and Wolfers (2010)).1
Political orientation has also been found to have an important effect (e.g., Lee et al. (2004);
Ferreira and Gyourko (2009); Bar and Zussman (2012); Ashenfelter et al. (1995)). In this
paper, we study the influence of judges’ race and party affiliation on their behavior in Texas
state district courts, using data on approximately half a million criminal sentencing decisions
from 2004 to 2013.
The Texas state district court system is an ideal context to study this issue for two reasons. First, it has a large number of judges (457 judges as of 2013) who perform comparable
tasks, as well as a large number of political jurisdictions (254 counties and 457 judicial districts), making the empirical analysis more reliable than data from most other states would.2
Second, judges in Texas are selected through partisan elections.3 Unlike many states where
judges are appointed by the governor or elected through nonpartisan elections in which party
affiliation is not disclosed on the ballot, voters in Texas directly elect judges through party
primaries and general elections with party affiliation on the ballot. Thus, Texas is one of the
states in which judges are most likely to be selected based on their political backgrounds.
1 Racial
bias has also been significantly studied in many other contexts such as labor market discrimination
of workers (e.g., Becker (1971) and Bertrand and Mullainathan (2004)).
2 This feature is largely due to the size of the state. However, large states do not necessarily have a large
number of jurisdictions. For example, California only has 58 judicial districts.
3 In the U.S., all federal court judges are appointed by the president and life-tenured. At the state court level,
there exists a variety of selection systems. In twenty-one states, trial court judges are appointed, mostly by
the governor. In twenty-two states, trial court judges are selected through non-partisan elections, an electoral
process where candidate compete without party affiliation on the ballot. In twelve states, judges are selected
through partisan elections, an electoral process that is identical to that of major public offices such as U.S.
congress. In partisan elections, each party selects its candidates through party primaries. Then, nominees from
each party compete in general elections. For details, see Lim et al. (forthcoming), Lim and Snyder (2014) as
well as the American Judicature Society website on judicial selection systems: http://www.judicialselection.us/
2
That is, if judges’ party affiliation influences their decisions at all, Texas is among the most
likely places where we would observe it. Likewise, finding little influence of judges’ political orientation on their decisions in Texas may imply that such influence is also likely to be
small in states that use gubernatorial appointment or nonpartisan elections to select judges.
We find that the influence of judges’ race and party affiliation on sentence length is negligible. First, the mean difference in sentencing harshness across judges of different races is
less than one percent of the approximate range of judges’ discretion in criminal sentencing,
conditional on geographic factors4 such as voter preferences.5 Second, the match between
judges’ and defendants’ race also has a negligible effect. Specifically, sentencing harshness
increases by less than one percent of the approximate range of discretion when judges and
defendants are of different races. Judges’ party affiliation also has a negligible influence
on sentencing. The difference between Democratic and Republican judges in sentencing
harshness is less than one percent of discretion, conditional on geographic factors. Most
of these estimates are precisely estimated, and their 95-percent confidence intervals include
only negligible effects of race and party affiliation.6
Despite these null effects, we find substantial heterogeneity in sentencing harshness across
judges. To explore its sources, we conduct three analyses. First, we decompose variation in
sentencing harshness into county-specific and judge-specific factors. Second, we investigate
how the variation in sentencing harshness across judges is related to political and socioeconomic characteristics of counties and judicial districts they serve. Third, we investigate
4 By
“conditional on geographic factors,” we mean conditional on county-year fixed effects. County-year
fixed effects capture anything that can influence sentence lengths at the county-level, including factors that
vary over time. Examples are voters’ preferences, district attorneys’ electoral cycles and variation in the pool
of criminal cases.
5 The precise range of judges’ discretion we use in measurement of sentencing harshness is the difference
between the 90th and 10th percentiles of sentenced jail time within a group of cases that have identical primary
offenses and are sentenced in the same year. Our measure is described in detail in Section 3.
6 Even without conditioning on geographic factors, the relationships between judges’ race and sentencing
harshness and between party affiliation and sentencing harshness are small (mostly less than five percent of
the range and less than two percent of the range, respectively) and statistically insignificant, which we find in
additional analyses we describe below.
3
the relationship between judges’ sentencing harshness and their race, gender, party affiliation
and career history, unconditional on geographic factors.
To explore the consequences of judges’ heterogeneity in sentencing, we also simulate a
situation in which the geographic jurisdictions of courts are enlarged. This helps us evaluate
how cross-judge heterogeneity influences sentencing disparity within and across counties.7
If judges pursue consistency across different geographic areas, and if many counties share
the same set of judges, then the cross-county disparity in sentencing harshness may not be
large even when judges vary substantially in sentencing harshness. Thus, if judges pursue
consistency, making political jurisdictions large, i.e., making many geographic units share
the same set of judges, would reduce sentencing disparity across different areas. On the other
hand, if judges adjust their decisions to the preference of localities, then the composition of
political jurisdictions may not significantly influence the consistency in the application of
law across localities. Rather, it may be more desirable to make political jurisdictions small
and allocate only a small number of judges to reduce cross-judge disparities and enhance
consistency in sentencing within each political jurisdiction.
For these analyses, we exploit the unique overlapping structure of Texas state district
courts, where judicial districts composed of different sets of counties can partially overlap
with one another within the same county. This structure allows us to separately analyze the
influence of political and socio-economic characteristics measured at two levels: the localities (counties) where cases are prosecuted and the political jurisdictions (judicial districts)
7 Understanding
the influence of judge heterogeneity on sentencing disparity across geographic areas may
help us to understand public policy issues such as prison overcrowding and crime rates. Sentencing disparity
across geographic areas may lead to variation in prison population. Variation in prison population may in turn
lead to variation in crime rates. Levitt (1996, 2004) argues that an increase in prison population significantly
reduces crime, and the increase in prison population in the 1990s is one of the most important factors that
explain the dramatic decline in crime rates that occurred for the same period. Levitt (1996) uses prison overcrowding litigation to estimate a causal effect of prison population on crime rates. He lays out two intuitive
theoretical mechanisms for the influence of prison population on crime rates. The first mechanism is an incapacitation effect: criminals are prevented from committing additional crimes while being held in prison. The
second mechanism is a deterrence effect: the increased threat of punishment discourages potential criminals
from committing crimes they otherwise would find attractive.
4
of the judges deciding the case. We then compare the magnitudes of the effects of these two
sets of variables to assess the role played by each one of them in shaping judges’ sentencing
behavior.8 We also use this structure to compare within-judge cross-county variation in sentencing decisions with aggregate cross-county variation. We attribute the difference between
the two measures of variation to judges’ pursuit of consistency.
Our findings are at odds with a vast array of empirical papers by legal scholars, political
scientists and economists, which have found that individual characteristics of judges do affect their decisions.9 A possible explanation for our different findings is that most previous
analyses employed data from the U.S. Supreme Court or the federal appeals courts, whereas
we examine state district court cases. Because of the importance of precedential decisions in
the U.S. common law system, upper court judges play an important role in shaping policy.
District court judges, in contrast, may be thought of as performing a largely bureaucratic
task.10 In this sense, the contrast between our results and those of previous papers on the
determinants of judicial behavior is analogous to that between studies examining upper and
8 This
analysis is partly motivated by the literature on federalism. In discussions on federalism, it is often
assumed that a political jurisdiction is the unit of policy decisions. However, in practice, political jurisdictions
are often only a unit for selecting public officials. Many public officials have discretion to use different policies
for sub-units of their political jurisdictions. For example, state public utility regulators are selected at the
state level. But, when it comes to rate reviews for electric utilities, they have discretion to treat individual
electric utilities differently. That is, they can take different positions for different utilities (markets) in the same
state. Likewise, policing budgets are determined at the city level, but the deployment of police across different
neighborhoods may be decided based on the distribution of crime rates. The setup that we study (state courts)
is a limit case where public officials can vary decisions easily for every issue within the same jurisdiction.
9 George (2001) offers a very informative summary of the early literature. Several papers find evidence
that the political alignment of appellate court judges and Supreme Court justices (usually measured by the
party of the appointing President) is an important determinant of their decisions. See Segal and Cover (1989)
for an example. The evidence of early studies on race effects is less clear but recent papers indicate that the
judges’ race plays a relevant role in very specific, racially related cases such as those involving voting rights
and discrimination (See Cox and Miles (2008) for an analysis of voting rights appellate court cases and Chew
and Kelley (2008) for a study of workplace racial harassment cases. Both papers find that African-American
judges are more likely than their non-African-American peers to make decisions favoring the plaintiff.).
10 Interestingly, in spite of our null effects findings concerning judges’ race and political alignment, we
document substantial cross-judge heterogeneity in sentencing behavior. This result suggests that, even in the
relatively bureaucratic context of trial courts, judges vary considerably in their legal thinking and have a nontrivial degree of discretion. That the decisions of trial judges are not completely pre-determined by exogenous
factors, such as sentencing guidelines and the characteristics of the case, reinforces the importance of studying
their behavior.
5
lower-level officials outside of the judicial system. For example, there is a strong consensus
that the behavior of U.S. Congressmen is highly partisan (e.g., Poole and Rosenthal (1984),
Snyder and Groseclose (2000), Lee et al. (2004)). On the other hand, Ferreira and Gyourko
(2009) document null effects of mayor’s party affiliation on the size of city government, the
allocation of local public spending, and crime rates.11
Our findings also differ from another set of studies that document significant influence of
decision-makers’ race in contexts other than judicial behavior (e.g., Antonovics and Knight
(2009), Price and Wolfers (2010), and Anwar et al. (2012)).12 This discrepancy suggests that
the influence of race may critically depend on decision-makers’ expertise, the nature of their
tasks. Anwar et al. (2012) find that the racial composition of the jury pool substantially influences the racial disparity in conviction rates. Specifically, having even one black person in
the jury pools almost completely eliminates the difference in conviction rates between black
and white defendants. Unlike jurors, judges are professionally trained and have acquired
significant experience in law. Finding little racial influence in judges’ decisions implies that
expertise may significantly reduce racial bias.
Price and Wolfers (2010) find that NBA players tend to receive more fouls when referees
are of different races. While NBA referees make split-second decisions, criminal sentencing
decisions require judges to spend a substantial amount of time in reviewing the case at hand.
Moreover, although NBA referees are experts and are professionally reviewed, their decisions are admittedly less consequential than those of judges handling felony cases. Thus, the
contrast between Price and Wolfers (2010) and our result indicates that racial bias may in11 Ferreira
and Gyourko (2009) largely attribute their finding of null effects to the Tiebout competition between localities. Though the mechanism behind null effects of party in our study is not precisely Tiebout
competition, an analogous incentive may influence judges’ decisions. Unlike in appellate courts, at the district
court level there exist a large number of judges handling highly comparable cases. An implicit comparison
among judges may prevent their racial and political identities from saliently affecting their decisions.
12 The results in these studies all show that preference-based discrimination affects decision making. There
are also studies on racial bias that show very different results. For example, Knowles et al. (2001) show that
law enforcement officer behavior in motor vehicle searches is consistent with statistical discrimination, but not
with preference-based discrimination.
6
fluence experts’ decisions more in a setting where decisions are less deliberate and relatively
unimportant.
Previous papers using data from federal district courts have documented minimal effects
of judges’ race and political orientation on their sentencing behavior.13 We regard our study
as complementary to these. Texas District Court judges are elected in partisan elections, as
opposed to their counterparts from federal courts, who are appointed for life by the President.
The former group of judges thus faces much stronger incentives than the latter to respond
to the preferences of voters and interest groups from their districts. Whether these different incentives magnify the effects of race and party affiliation on the sentencing behavior
of elected judges is an empirical question that our paper begins to address. It is also worth
noticing that the vast majority of criminal cases in the United States are under state jurisdiction.14 The importance of state trial courts for the workings of the U.S. criminal justice
system thus makes studying the behavior of state judges interesting on its own.
Our paper is also related to Abrams et al. (2012), who also examine heterogeneity in sentencing patterns across state trial courts judges. They focus on variation across judges in their
different treatment of African-American and white defendants, and find evidence that judges
vary in their propensity to assign jail sentences to convicted defendants across different races.
Interestingly, they find no significant differences in the distributions of jail sentence lengths
across judges, whereas we are able to document such differences. A potential explanation
for the different findings is that they employ data from a single county (Cook County) comprising cases decided by 70 judges. Our data set consists of cases decided in 254 counties
by judges from 457 different courts, which allows us to observe considerably more variation
in the decision patterns across judges. Similarly to us, Abrams et al. (2012) also find that the
13 Ashenfelter
et al. (1995) analyze civil rights and prisoner cases. Schanzenbach (2005) and Yang (2013)
examine criminal cases.
14 In 2012 a total of 553,843 inmates were admitted to state jails or prisons to serve a sentence of at least one
year. The corresponding number for federal jails and prisons, which handle inmates convicted in the federal
justice system and in the District of Columbia, was 55,938. See Carson and Golinelli (2013) for details.
7
heterogeneity in judges’ propensities to assign jail sentences cannot be explained by their
race.
The rest of the paper is organized as follows. In Section 2, we introduce the institutional
background of Texas state district courts. In Section 3, we describe the data. In Section 4,
we present and discuss our analyses. In Section 5, we conclude.
2
Institutional Background
Texas state district courts are trial courts of general jurisdiction.15 District court judges handle felony crime cases, as well as well as civil cases in which the disputed amount exceeds
200 dollars. Judges tend to have significantly more discretion in criminal than in civil cases.
Unlike in civil cases, in which outcomes are mostly decided by the jury, criminal sentencing is primarily under the discretion of judges once defendants are convicted by the jury.16
Hence, we focus on criminal sentencing.
The Texas state district court system is composed of 457 judgeships. The term of district court judges is four years. They are selected through partisan elections, an electoral
process identical to that of the governor and state legislators. State parties hold primaries to
select their candidates for judicial elections. Then, nominees from each party compete in the
general election.
Each judge constitutes one judicial district. Thus, there exist 457 judicial districts. Each
judicial district is composed of one or more counties, and does not divide a county. Since
15 In
most U.S. states the court system is organized in three tiers: supreme, appellate, and district (circuit,
trial) courts. The structure of Texas state court is analogous to this standard structure, with the only difference
that the highest court is divided between the supreme court and the court of criminal appeals. For details, see
http://www.courts.state.tx.us/
16 The division of discretion between judges and the jury in Texas is slightly different from other states. Texas
is one of the five states (together with Arkansas, Missouri, Oklahoma and Virginia) that allow jury sentencing.
In Texas, defendants can choose to be sentenced by the jury, and judges cannot override the jury’s decision.
Although in principle this raises an issue in the econometric specification of sentencing decisions, we abstract
from this issue because in practice jury sentencing is a negligible proportion of cases.
8
there are 254 counties in the state, multiple judicial districts overlap over the same county.
Figure 1 shows the structure of Texas state district courts.17
Table 1: Jurisdictional Overlap Patterns
Number Number of
of Areasa Counties
Jurisdictional Overlap Patterns
Single County & Multiple Courts
No Courts Serve Another County
Single County & Single Court
B
Court does not serve another county
Multiple Counties & Multiple Courts
C
Identical Jurisdictions
D Multiple Counties & Single Court
Multiple Counties & Multiple Courts
E
One separate Jurisdiction
Multiple Counties & Multiple Courts
F
Many Separate Jurisdictions
Total
A
Number of
Courts
28
28
273
15
15
15
6
23
13
26
76
26
13
39
54
11
73
76
99
254
457
Source: “Complexities in the Geographical Jurisdictions of District Courts,” available at
http://www.courts.state.tx.us/courts/pdf/JurisdictionalOverlapDistrictCourts.pdf
a Areas are the smallest units that form a partition of the entire state.
Table 1 shows six different patterns of overlap between judicial districts. Pattern A is
a case where multiple judges serve a county, and they do not serve other counties. This
pattern appears in urban counties with large populations such as Harris County, which has
the City of Houston, and Dallas County, which has the City of Dallas. Pattern B is a case
in which a single judge serves a single county. Pattern C is a case in which multiple judges
serve an identical set of multiple counties. Pattern D is a case in which one judge serves
many counties, which typically have small populations. Patterns A, B, C, and D are common
geographical structures of state court districts that are not unique to Texas.
In Patterns E and F, judges who serve different sets of counties overlap partially with one
another. An example of Pattern E is Nueces and adjacent counties. There are eight judges
17 The
map in Figure 1 is available at http://www.courts.state.tx.us/courts/pdf/sdc2009.pdf
9
H
H
C
C
P
P
J
J
R
R
B
W
B
W
W
W
394
L
L
L
L
M
L
L
H
P
C
E
T
83
U
M
161 238
M
T
Y
A
H
C
S
R
H
B
R
C
I
M
H
S
S
G
Source: Chapter 24, Government Code
S
S
H
S
K
C
C
C
W
C
N
F
M
K
E
M
J
F
111
W
Z
L
365 218
D
M
Z
B
T
C
W
H
J
L
K
G
C
H
L
W
381
D
H
B
J
K
G
D
C
R
A
V
T
D
B
M
B
E
N
F
W
C
N
S
G
D
R
R
A
C
J
C
135
V
L
M
278
F
H
F
M
V
H
W
M
L
M
130
W
329
A
W
D 62
L
C
G
U
F
B
S
C
H
T
S
S
J
163
O
J N
1-A
273
S
PRESIDIO
JEFF DAVIS
143
121
PECOS
109
CRANE
ECTOR
70
ANDREWS
109
GAINES
OCHILTREE
100
CARSON
72
UPTON
MIDLAND
142
118
BEXAR (27)
-------------------037 045 057 073
131 144 150 166
175 186 187 224
225 226 227 285
288 289 290 379
386 399 407 408
436 437 438
TRAVIS (17)
-------------------053 098 126 147
167 200 201 250
261 299 331 345
353 390 403 419
427
63
259
91
DIMMIT
293
ZAVALA
38
UVALDE
REAL
198
KIMBLE
MENARD
STARR
79
HIDALGO
BROOKS
DUVAL
229
JIM
WELLS
24
CAMERON
WILLACY
KENEDY
105
197
NUECES
258
BRAZORIA
75
C
H
FORT BEND (6)
--------------------240 268 328 387
400 434
MONTGOMERY (7)
--------------------009 221 284 359
410 418 435
GALVESTON
1
SABINE
128
ORANGE
JEFFERSON
HARDIN
TYLER
88
E
S
123
E
SHELBY
E
H
P
J
R
B
C
P
J
R
L
B
W
W
C
B
P
C
E
A
G
D
O
C
T
H
L
L
L
H
S
U
H
R
C
C
V
S
M
S
K
D
K
D
M
H
G
R
D
N
F
L
S
S
E
M
K
T
N
F
S
K
C
C
C
W
H
L
M
K
H
K
D
Z
U
R
K
M
C
R
T
J
H
F
W
L
F
S
M
C
J
D
M
A
B
H
B
J
L
W
K
F
414
M
H
G
B
W
K
C
N
S
G
D
A
V
L
F
L
M
R
425
421
K
D
J
N
J
M
W
G
M
W
A
B
F
H
M
W
G
M
L
R
F
U
C
A
N
C
G
L
P
J
S
O
J N
O
02/02/2012
H
T
S
S
J
S
J N
Texas Legislative Council
C
A
P
H
M
420
R
G
B
H
S
S
356
T
P
H
M
C
B
N
12R114
B
S
T
C
412
H
H
M
W
A
R
G
L
P
R
G
M
F T M
C
S
W
B
S
T
C
300
H
H
H
U
T
C
R
369
M
L
D
F
S
F
321
W
W
A
V
422
K
V
H
L
D
R
H
L
H
F
W
A
W
C
C
B
R
L
C
F
H
F
B
R
C
C
B
R
K
W
R
N
L
G
J 413 E
T
D
C
A
377
R
V
L
F
L
M
F
E
C
G
397
D
B 426
C
W
B
B
T
C
H
S
W
C
N
S
W
K
K
D
B
G
G
415
P
C
B
M
K
G
H
H
B
L
E
J
C
J
H
B
L
W
B264
M
H
170
J
T
D
C
W 395
B
428
T
C
S
P
H
W
M
G
H
H
B
C
P
B
D
B
E
L
P
J
C
K 433
C
L
S
S
E
Y
A
A
M
J
K
B
M
C
L
W
S
G
B
M
Z
B
K
M
M
C
C
S
T
B
W
Z
406
L
F
D
M
S
E
Y
A
W
S
G
B
Z
W
B
K
M
M
C
C
S
T
B
W
U
R
K
S
E
M
391
R
T
H
K
350
J
H
F
S
S
K
C
C
C
W
H
C
T
C
C
H
M
D
G
R
O
O
M
I
S
I
S
V
G
G
C
B
F
B
F
A
C
H
H
R
C
C
H
H
H
A
B
G
B
G
441
M
D
M
T
P
R
320
S
M
D
T
U
M
H
P
C
E
358
L
L
H
S
385
M
T
Y
A
H
C
D
L
B
G
C
P
R
O
D
251
S
M
D
H
P
P
Y
W
W
HARRIS (59)
-------------------011 055 061 080
113 125 127 129
133 151 152 157
164 165 174 176
177 178 179 180
182 183 184 185
189 190 208 209
215 228 230 232
234 245 246 247
248 257 262 263
269 270 280 281
295 308 309 310
311 312 313 314
315 333 334 337
338 339 351
C
L
JEFFERSON (7)
-------------------058 060 136 172
252 279 317
H
GALVESTON (6)
-------------------010 056 122 212
306 405
CHAMBERS
LIBERTY
SAN
JACINTO
POLK
TRINITY
D
O
159
O
G
145
PANOLA
ANGELINA
N
A
C
4
RUSK
GREGG
K
E
E
HARRIS
MATAGORDA
CAMERON (7)
-------------------103 107 138 197*
357 404 444 445
R
O
CASS
MARION
5
BOWIE
115
71
124 HARRISON
MONTGOMERY
WALKER
NUECES (7)
-------------------028 094 105* 117
148 214 319 347
SAN
ARANSAS
PATRICIO
CALHOUN
VICTORIA
23
E
2
HOUSTON
FORT BEND
WHARTON
JACKSON
LAVACA
REFUGIO
GOLIAD
KLEBERG
36
BEE
AUSTIN
COLORADO
FAYETTE
DE WITT
BRAZOS
85
12
LEON
3
7
SMITH
ANDERSON CH
MADISON
WASHINGTON
155
LEE
21
82
BURLESON
MILAM
20
ROBERTSON
402
CAMP
76
TITUS
RED RIVER
6
WOOD UPSHUR
HENDERSON
294
VAN
ZANDT
RAINS
HOPKINS
8
LAMAR
DELTA
FREESTONE
77
NAVARRO
13
KAUFMAN
86
196
HUNT
LIMESTONE
FALLS
BASTROP
CALDWELL
KARNES
LIVE OAK
MCMULLEN
26
BELL
27
19
GUADALUPE 25
GONZALES
22
WILSON
ATASCOSA
ZAPATA JIM HOGG
49
WEBB
BEXAR
81
66
HILL
40
ELLIS
MCLENNAN
WILLIAMSON
TRAVIS
HAYS
COMAL
52
382
COLLIN
GRAYSON FANNIN
DENTON
COOKE
235
15
DALLAS (32)
-------------------014 044 068 095
101 116 134 160
162 191 192 193
194 195 203 204
254 255 256 265
282 283 291 292
298 301 302 303
304 305 330 363
COLLIN (9)
-------------------199 219 296 366
380 401 416 417
429
ROCKTARRANT DALLAS WALL
BOSQUE
CORYELL
BURNET
BLANCO
KENDALL
LA SALLE
FRIO
MEDINA
BANDERA
KERR
33
LLANO
220
HAMILTON
LAMPASAS
MILLS
SAN SABA
35
PARKER
43
WISE
271
MONTAGUE
TARRANT (23)
-------------------017 048 067 096
141 153 213 231
233 236 297 322
323 324 325 342
348 352 360 371
372 396 432
DENTON (7)
-------------------016 158 211 362
367 393 431
355 JOHNSON
HOOD
266
SOMER- 18
ERATH
VELL
PALO
PINTO
29
JACK
CLAY
97
COMANCHE
GILLESPIE
MASON
CONCHO
MCCULLOCH
COLEMAN BROWN
42
TAYLOR CALLAHAN EASTLAND
JONES
SHACKELFORD STEPHENS
HIDALGO (11)
---------------------092 093 139 206
275 332 370 389
398 430 449
MAVERICK
KINNEY
EDWARDS
SUTTON
30
WICHITA
BAYLOR ARCHER
46
90
THROCKHASKELL MORTON YOUNG
KNOX
FOARD
RUNNELS
TOM GREEN
51
COKE
NOLAN
32
FISHER
STONEWALL
39
SCHLEICHER
IRION
VAL VERDE
CROCKETT
112
REAGAN
STERLING
HOWARD
132
SCURRY
KENT
KING
50
WILBARGER
HARDEMAN
CHILDRESS
MOTLEY COTTLE
HALL
MITCHELL
GARZA
GLASSCOCK
MARTIN
WHEELER
100
CROSBY DICKENS
FLOYD
110
DAWSON BORDEN
LYNN
GRAY
COLLINGSARMSTRONG
DONLEY WORTH
LUBBOCK
64
HALE
TERRELL
106
YOAKUM TERRY
WARD
BREWSTER
REEVES
LAMB
154
HOCKLEY
286
COCHRAN
BAILEY
LOVING WINKLER
LUBBOCK (5)
-------------------072* 099 137 140
237 364
47
84
LIPSCOMB
31
HUTCHINSON
ROBERTS HEMPHILL
RANDALL
POTTER
MOORE
SHERMAN
PARMER CASTRO
SWISHER BRISCOE
287
DEAF SMITH
222
OLDHAM
69
HARTLEY
DALLAM
HANSFORD
January 2012
State District Courts
Figure 1: Structure of Texas State District Courts
G
253
L
P
A
N
J
O260
J N
S
CULBERSON
P
H
217
411
T
149
H
H
M
W
A
T
H
S
S
344
C
B
C
A
N
276 M
F T M
C
102
R
G
L
P
R
P
307H
G
S 188
173
114 R
H
87
F
B
S
239
H
205
272G
506
B
K
F
M
W
T
C
HUDSPETH
W
A
W
H
S
349
A
U
M
C
202
B
F T M
C
R
241
W
H 392
V
354 R
W
R
C
B
L335
M
F
J
C
W
G2nd L25th
K
K
B
C
H
54
J
146
W
B
L
C
G
59
249 378
D
C
K
H
L
D
R
B
B 361 G
R
L
N
267
L
EL PASO
W
N
S
G
G
277
T
C
H
S
207
156
A
M
J
K
H
B
L
E
P
W
M
L
M
423 F
B
368
K
K
B
F
E
R
H
F
336
439
C
G
D
M74
H
B169
J
H
S
B
T
D
C
P
W
M
274 C
H
W
B
J
C
P
B
B
M
C
L
S
S
E
S
Y
A
W
78
G
B
U
R
K
S
M
C
C
S
T
B
W
216K
M
C
R
T
104
J
H
K
F
H
S
C
B
H
343
D
M
A
B
B
E
L
P
J
C
EL PASO (15)
-------------------034 041 065 120
168 171 205* 210
243 327 346 383
384 388 409 448
Z
341
W
L
F
D
Z
K
L
M
C
424
S
E
Y
A
W
89
S
G
B
M
B
K
M
M
C
C
S
T
B
W
U
R
K
M
C
R
T
326
J
H
K
F
H
S
T
S
K
C
C
C
W
H
L
M
K
E
119
K
D
M
D
G
N
F
T
C
223
R
O
K
D
L
H
340
H
M
D
G
B
V
G
C
F
A
C
H
316
C
I
M
H
S
S
V
G
C
F
B
B
G
242
D
L
B
G
C
P
R
O
D
108
S
M
D
H
T
U
P
P
C
E
C
A
R
O
LUBBOCK (5)
<------ number of districts wholly within the county
-------------------072* 099 137 140 <------ asterisk indicates a multicounty district
237 364
Key
E
E
S
H
244 318
M
T
Y
A
H
D
L
B
C
G
C
P
P
R
181
O
D
H
H
FRANKLIN
S
MORRIS
M
SAN
AUGUSTINE
JASPER
D
NEWTON
H
GRIMES
WALLER
10
who serve Nueces County (district 28, 94, 117, 148, 21, 319, 347, and 105). One of these
judges (district 105) also serves Kenedy and Kleburg Counties. An example of pattern F is El
Paso and adjacent counties. There are fourteen judges who serve El Paso County (district 34,
40, 41, 65, 120, 168, 171, 205, 210, 243, 237, 346, 383, and 384). One of these judges (district 205) also serves two other counties (Culberson and Hudspeth). Another judge (district
394) does not serve El Paso, but serves counties that are linked to El Paso through district
205. The judge in district 394 serves five counties (Brewster, Culberson, Hudspeth, Jeff
Davis, and Presidio). As described in Section 1, this unique overlapping patterns helps us to
(1) assess the importance of localities (counties) versus political jurisdictions in shaping the
sentencing behavior of the judges; and (2) evaluate how cross-judge heterogeneity influences
sentencing fairness within and across counties.
3
Data
We obtained criminal sentencing data from the Texas Department of Criminal Justice. The
data set includes all felony crime cases that resulted in the conviction and incarceration of
defendants from years 2004 to 2013, approximately 440,000 cases. The data set contains
key information regarding each case, including the name, gender, race, ethnicity, and birth
date of the defendant, all of the convicted offenses in the case and their severity, the location
(county) and the date of crime, sentence length, information related to probation and parole,
and the judicial district where the defendant was convicted and sentenced. By linking the
judicial district of conviction in the sentencing data with court administrative data on the
match between judicial districts and judges, we identify the judge that handled each case.
We supplement the sentencing data with three auxiliary data sets. First, since our raw
sentencing data does not contain defendants’ criminal history, we obtained criminal records
of defendants from the Texas Department of Public Safety. We computed the number of
11
prior felony convictions and violent felony convictions for each defendant that appears in
our sentencing data.
Second, we obtained judges’ party affiliation, their tenure (number of years in office) and
their electoral proximity (the number of days remaining until their next election) using data
on elections of judges in Texas.18 We also obtained judges’ career history from the American
Bench, a directory of all U.S. judges. We use total legal experience prior to being a judge,
experience in private law practice and in prosecution—all of which are measured in number
of years.
Third, we include political and demographic characteristics of counties and judicial districts. For political characteristics, we use the average Democratic vote share of all the
non-judicial elections held in the state, also acquired from the election data. We call this
Democratic Vote Share (DVS) and use it to measure the ideology of each judges’ electorate.
We also use the turnout rate in the most recent presidential election. For demographic characteristics, we include population size, area, income, employment, as well as the share of the
following groups in the total population: religious adherents, females, younger than 20, older
than 65, blacks, whites, Hispanics, urban, people with high school education and people with
more than high school education. We also include variables related to crime rates: total number of convictions, the share of those convictions involving violent crimes and drug-related
crimes, the total number of crimes reported to the police and the share of reported crimes
that were violent. They are obtained from the U.S. census data and are computed both at the
county-level and judicial district-level. Summary statistics of these variables as well as the
normalized measure of sentencing harshness described below are presented in Table 2.
Measuring Sentencing Harshness Each judge handles multiple cases at any one point in
time. The sets of cases vary across judges even when cases are randomly assigned. Thus,
18 This
data set on elections of judges is analyzed in Lim and Snyder (2014).
12
Table 2: Summary Statistics
Variable
Mean
S.D. Min
Panel A: Defendant Characteristics
31.9
10.7
17
0.2
0.4
0
Max
Age
87.1
Female
1
Race
White
0.3
0.5
0
1
Black
0.3
0.5
0
1
Hispanic
0.3
0.5
0
1
Previous Felony Convictions
1.1
1.6
0
20
Previous Violent Crime Convictions
0.1
0.3
0
5
Panel B: Sentencing Outcomes
Sentenced Jail Time (days)
1754
3650
30 73059
By crime category
Aggravated Assault
2460
3443
60 36525
Burglary
1526
2078
60 36525
Drug possession
913
1390
30 36525
Drug trafficking
2305
2973
90 36525
Fraud, Forgery and Embezzlement
578
951
45 36525
Larceny
553
1010
30 36525
Motor Vehicle Theft
420
487
30
9131
Homicide
19148 14205 121 73059
Other Violent
1933
3031
90 36525
Other Offenses
1420
2138
60 36525
Robbery
3571
4245
60 36525
Sexual Assault
6784
8351 121 36525
Weapon offenses
1487
1591 180 36159
Normalized Harshness
0.31
0.33
0
1
Panel C: Judge Characteristics
Tenure (years)
10
7
0
31
Republican
0.60
0.49
0
1
Career History
Total Legal Experience
18.51
8.06
5
42
Private Law Practice
11.17
9.91
0
41
Prosecution
4.38
6.00
0
25
Race
Black
0.02
0.14
0
1
Hispanic
0.15
0.36
0
1
Panel D: Political and Demographic Characteristics of Counties
Share of Race
White
0.6
0.21 0.03
0.93
Black
0.07
0.07
0
0.34
Hispanic
0.32
0.23 0.02
0.97
Democratic Vote Share (DVS)
0.31
0.14 0.02
0.86
# Obs
437509
437836
437836
437836
437836
437375
435564
437497
19009
45084
105130
33935
24174
42442
10146
4531
27017
81259
22925
12654
9191
436677
2533
387
350
300
297
421
421
2121
2121
2121
2121
Note: In Panels A and B, the unit of observation is individual criminal case. In Panel C,
it is judge by year for tenure, and judge for other variables. In Panel D, it is county by
year. Summary statistics for district-level characteristics and other county-level characteristics are omitted.
13
using the length of sentenced jail time as a measure of sentencing harshness may lead us
to confound variation in judges’ sentencing harshness and variation in the set of cases assigned.19 To minimize the influence of cross-judge heterogeneity in the sets of cases, we
construct a measure of normalized harshness of sentencing, Harshness, in which the sentence
length is normalized with respect to the 10th and 90th percentiles incarceration sentences in
the set of cases resolved in the same year and with the same primary offense. We classify
primary offenses using the National Crime Information Center (NCIC) Offense Codes (nciccd) included in the data. NCIC codes provide more detailed information about the nature
of offenses compared with other commonly used classification codes such as the Uniform
Crime Reporting rule by the Federal Bureau of Investigation or classification by the National
Judicial Reporting Program. In our data, primary offenses are classified into 39 categories
using NCIC codes.20 The measure of sentencing harshness we employ is defined as
Harshness =



0



if Sentence < p10,
Sentence−p10
p90−p10




 1
if p10 < Sentence < p90,
(1)
if Sentence > p90,
where p10 and p90 are 10th and 90th percentiles in the group of cases that have the NCIC
code of the same primary offense and sentence year.21 We use 10th and 90th percentiles
rather than the minimum and the maximum to avoid the influence of outliers on our measure.
Similarly to what happens in the trial courts of most U.S. states, the vast majority of
19 Including
fixed effects for crime categories in regression analysis does not resolve this issue because the
mean jail time is not the only outcome that varies across crime categories. The range of jail time specified by
the penal code also varies considerably across crime categories.
20 NCIC
Offense
Codes
are
available
in
the
following
website:
http://wirecordcheck.org/help/ncicoffensecodes.htm
21 In cases in which the defendant received the death penalty or a life sentence was the maximum sentence,
we top-code the sentence as 200 years (death penalty) and 100 years (life sentence). We conducted numerous
robustness checks with this top-coding. Changes in this top-coding do not affect our results in a meaningful
way because homicides resulting in either the death penalty or a life sentences are only a very small proportion
of the cases that judges handle.
14
cases in Texas district courts are resolved by plea bargain.22 Thus our measure of sentencing harshness largely captures the outcome of a bargaining process involving the judge, the
district attorney’s office, the defendant, the defense attorney, among others. But, insofar as
settlement negotiations take place in the shadow of a trial, plea-bargained sentences still reflect the harshness of the judge responsible for the case. Moreover, our baseline analyses
include county-year fixed effects, which filter out any influence of district attorneys or their
reelection incentives. Previous research also indicates that the expected harshness of the
judge at trial does indeed affect sentencing in settled cases.23 Our findings are fully consistent with these existing results. We provide evidence that the assigned sentences observed
in our data (i.e., to a very large extent plea-bargained sentences) are strongly influenced by
the judges deciding the case. Moreover, we show evidence that the effect attributed to any
given judge tends to be relatively constant across the counties over which such a judge has
jurisdiction. That our estimated judge-specific effects do not seem to vary with the counties
where the cases are prosecuted provides further support for the interpretation that they indeed reflect the sentencing behavior of the judges, rather than the influence of prosecutors or
other agents involved in the plea negotiations. It is also worth noting that, with very few exceptions, the empirical research on the sentencing behavior of trial judges in criminal cases
has extensively employed data on plea-bargained sentences.24
Randomized Case Assignment An important advantage of using court cases to study the
influence of racial and political bias in decision-making is that cases are randomly assigned
22 95.70%
of all criminal convictions statewide in 2013 were resolved by a guilty plea or a plea of nolo
contendere. In 2012 this share was 96.85%. Shares for other years were similarly high. We obtained these
statistics from the Court Activity Reporting and Directory System, on the website of the Texas Office of Court
Administration.
23 See for example LaCasse and Payne (1999) and Boylan (2012).
24 Recent examples include Huber and Gordon (2004), Gordon and Huber (2007), Abrams et al. (2012).
Silveira (2012) proposes a structural approach for explicitly dealing with the plea bargaining process in the
empirical analysis of criminal cases. However, such a framework is out of the scope of this paper since it
requires information on case disposition that we do not have in our data.
15
across judges. In Texas district courts, cases are randomized at the county level, taking into
account overall caseloads and vacancies in the schedule of judges.25
To check for the degree to which counties followed the principle of randomization in
case assignment, we conduct Pearson’s χ2 -test for the independence between each of several
key variables and judge assignment. The variables are: the crime category of the primary
offense, the crime severity of the primary offense, a dummy indicating that the primary offense was violent, the race of the defendant, the gender of the defendant, and a dummy
variable indicating that the defendant was under age 30. We use thirteen crime categories:
aggravated assault, burglary, drug possession, drug trafficking, fraud, forgery and embezzlement, larceny, motor vehicle theft, homicide, robbery, sexual assault, weapon offenses, other
violent offenses and other non-violent offenses.
The chi-square tests show that randomization in case assignment clearly fails in some
county-years. For some variables, such as race and gender of the defendant, the balance
across judges appears to be relatively good. For race, the p-value of the chi-square statistic
is less than .05 about 7.6% of the time and the p-value is less than .10 about 13.7% of the
time. For gender, the p-value of the chi-square statistic is less than .05 about 9.2% of the
time and less than .10 about 15.5% of the time. Thus, for these variables the null hypothesis
of random assignment is rejected only a bit more often than we would expect by chance.
For other variables the deviations from random assignment are more frequent. Consider,
for example, the dummy variable indicating a violent offense. For this variable the p-value
of the chi-square statistic is less than .05 about 19.7% of the time, so the the null hypothesis
of random assignment is rejected almost 4 times as often as we would expect by chance.26
25 As described in Section 2, judges in a given county may have different sets of counties to serve.
As a result,
judges in the same county may have very different caseloads at any given point of time. For example, suppose
that Judges A and B serve County X and only Judge B also serves Counties Y and Z. To make caseloads
balanced across judges, County X should assign considerably fewer cases to Judge B than to Judge A. Thus,
there can be considerable variation in the number of cases assigned to each judge from a given county. However,
even in such cases, the principle in case assignment is randomization.
26 The p-value of the chi-square statistic is less than .10 about 26.9% of the time, so even using this threshold
the the null hypothesis of random assignment is rejected more than twice as often as we would expect by
16
In some cases this is due to specialization. For example, in El Paso and Jefferson Counties
some judges specialize in covering particular types of crime categories. In other cases, it is
likely due to the fact that certain crimes, such as murder, are relatively rare. For example,
Victoria county is served by two courts (Districts 24 and 377). In 2007, there were just four
homicide cases in the county in our dataset, and all were assigned to District 377. In 2009
there were four such cases and all were assigned to District 24. In 2010 there were four cases,
two assigned to each District. Summing across all years the division of homicide cases was
quite even – 13 to District 24 and 12 to District 377 – and a chi-square test would clearly
not reject the null hypothesis of random assignment. But in some years, such as 2007 and
2009, the distribution of cases was quite skewed and statistical tests for balance could lead
to rejection.
In most county-years we find that even if the chi-square tests reject the null hypothesis
of independence (at, say, the .01 level) for one or more variables, after dropping one judge
– or, in some cases two or three judges – the chi-square tests fail to reject the null on all
of the variables studied. For some county-years – e.g., Harris county in every year except
2005 – this is not the case. We therefore constructed a “cleaned” sample of county-years by
dropping all county-years for which (i) the p-value of the chi-square statistic is below .01 for
any of the seven variables checked, or (ii) two of more of the p-values for the seven variables
are below .10.
In the sample remaining after dropping these cases, the distribution of p-values from the
chi-square tests look quite good. Table 3 shows the fraction of p-values that fall below
various thresholds for the subsample. For the .05 and .10 thresholds, the fraction of cases
with p-values falling below the threshold is much lower than what we would expect by
chance. This is of course not too surprising given our criterion for dropping cases. But it is
even true for the .15 threshold. And, except for the Category variable, the fraction of cases
chance.
17
with p-values falling below the .20 threshold is also about what we would expect by chance.
Table 3: Random Assignment P-Values
Variable
Fraction of Cases with P <
.05
.10
.15
.20
Male
0.028
Race
0.012
Young
0.018
Category 0.009
Severity 0.015
Violent
0.012
0.043
0.037
0.062
0.065
0.074
0.055
0.056
0.040
0.065
0.080
0.092
0.074
0.179
0.179
0.185
0.292
0.225
0.203
Note: P-values are from chi-square tests of independence for the given variable, where the cases are
county-years. In all cases the number of observations
is 324.
In the remainder of the paper, we present results obtained using the “cleaned” sample.
The results do not change substantially if, instead, we use the complete, uncleaned sample
in the analysis. In the interest of space, we do not report the latter set of results. They are
available from the authors upon request.
4
Analysis
We first conduct three baseline analyses: (1) the influence of judges’ race and ethnicity
on their sentencing harshness, (2) the influence of judges’ political backgrounds on their
sentencing harshness, and (3) the extent of judges’ preference heterogeneity. Then, we investigate the influence of cross-judge heterogeneity on sentencing fairness within and across
counties.
18
4.1
The Influence of Judges’ Race and Ethnicity
We analyze the influence of judges’ race and ethnicity on sentencing harshness with three
specifications. In the first specification, we estimate the influence of judges’ race and ethnicity without interacting it with defendants’ race:
Harshnessijt = β0 + β1 Black Judgei + β2 Hispanic Judgei + γ xi jt + δwit + εi jt ,
(2)
where Harshnessijt is the normalized sentencing harshness, as defined on page 14, of judge
i in case j in year t, Black Judgei and Hispanic Judgei are dummy variables indicating that
judge i is Black or Hispanic, respectively, xi jt is a vector of case characteristics, and wit
is a vector of other characteristics of judge i and his/her county in year t. In the second
specification, we also estimate the influence of the match between judges’ and defendants’
race and ethnicity:
Harshnessijt = β0 + β1 Different Raceij + β2 Black Judgei + β3 Hispanic Judgei
+γ xi jt + δwit + εi jt ,
(3)
where Different Raceij is a dummy variable that takes value one if judge i and the defendant
in case j are of different race or ethnicity, and zero otherwise.
Table 4 presents results of estimating equations (2) and (3). All specifications include
county-year fixed effects. The key parameters are precisely estimated and have magnitudes
close to zero. The results using the full sample indicate that, relative to their non-AfricanAmerican peers, African-American judges tend to assign shorter sentences, although the
magnitude of the effect is small (roughly 1 percent of the range of Harshness). When sexual
assault cases are separately considered, the pattern is reversed, and African-American judges
assign longer sentences. The interaction between judges’ and defendants’ race is significant
19
Table 4: The Influence of Judges’ Race/Ethnicity on Sentencing Harshness - Baseline
Variables
(1)
Full
Sample
Different Race
Black Judge
Hispanic Judge
Female Judge
Years in Office
Black Defendant
Hispanic Defendant
Female Defendant
Age at Offense
Age squared
Observations
R-squared
Dependent variable: Harshness
(2)
(3)
(4)
Full
Violent
Sexual
Sample
Offenses
Assaults
(5)
Property
Crimes
(6)
Drug
Offenses
-0.0125***
(0.0038)
-0.0047
(0.0118)
0.0034
(0.0052)
-0.0002
(0.0003)
-0.0072**
(0.0033)
0.0010
(0.0025)
-0.0609***
(0.0023)
0.0014**
(0.0005)
-0.0000
(0.0000)
0.0061*
(0.0035)
-0.0125***
(0.0043)
-0.0033
(0.0115)
0.0033
(0.0051)
-0.0002
(0.0003)
-0.0126**
(0.0053)
-0.0035
(0.0042)
-0.0609***
(0.0023)
0.0014**
(0.0005)
-0.0000
(0.0000)
-0.0068
(0.0074)
0.0044
(0.0103)
-0.0048
(0.0109)
0.0101
(0.0067)
-0.0004
(0.0004)
-0.0014
(0.0083)
-0.0176***
(0.0066)
-0.0808***
(0.0070)
0.0072***
(0.0013)
-0.0001***
(0.0000)
-0.0138
(0.0133)
0.0525***
(0.0152)
-0.0012
(0.0122)
0.0168
(0.0120)
-0.0009
(0.0007)
-0.0149
(0.0167)
-0.0369**
(0.0151)
-0.1224***
(0.0299)
0.0303***
(0.0025)
-0.0003***
(0.0000)
0.0031
(0.0115)
-0.0063
(0.0085)
0.0197
(0.0148)
-0.0040
(0.0052)
0.0003
(0.0005)
-0.0328**
(0.0128)
-0.0295**
(0.0130)
-0.0351***
(0.0045)
0.0060***
(0.0012)
-0.0001***
(0.0000)
0.0178***
(0.0057)
-0.0014
(0.0079)
-0.0167**
(0.0069)
0.0029
(0.0050)
-0.0001
(0.0003)
-0.0043
(0.0098)
0.0405***
(0.0075)
-0.0615***
(0.0037)
0.0026*
(0.0014)
-0.0001***
(0.0000)
228,557
0.160
228,557
0.160
44,566
0.153
7,322
0.307
38,770
0.177
70,691
0.273
Note 1: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗ significant at
1%, ∗∗ significant at 5% and ∗ significant at 10%.
Note 2: All specifications include county-year fixed effects, offense categories (12 dummy variables for 13 categories), and the criminal history of defendants as control variables. For criminal history, we use five dummy
variables for the number of previous convictions in felony: one, two, three, four, and five or more. The base
group is one with no previous convictions. We use three dummy variables for the number of previous violent
felony convictions: one, two, and three or more.
20
at 10% in the whole sample and at 1% in drug crimes. Again, the magnitudes are small.
Several defendant characteristics are statistically significant, but they may well reflect unobserved cases characteristics. For example, female defendants consistently receive more
lenient sentences across crime categories, which may reflect the possibility that offenses by
females are less heinous.
Despite the common belief that racial identity affects decision making, the negligible estimated effects of judges’ race and ethnicity have intuitive explanations. Unlike jurors that
are randomly drawn from the population, judges are professionally trained and selected under considerable scrutiny. Judicial candidates with minority backgrounds may face stronger
scrutiny and may be selected only when it is unlikely that they will fit racial or ethnic stereotypes.27 Moreover, while serving on the bench, local bar associations conduct and publish
ratings of judges. A judge whose behavior clearly fits racial or ethnic stereotypes might
easily attract the attention from these associations, causing a controversy that could be detrimental to her career.
In the third specification, we incorporate full interactions between judges’ and defendants’
race:
Harshnessijt = β0 + β1 Black Judgei ∗ Black Defj + β2 Black Judgei ∗ Hispanic Defj
+β3 Black Judgei ∗ White Defj + β4 Hispanic Judgei ∗ Black Defj
+β5 Hispanic Judgei ∗ Hispanic Defj + β6 Hispanic Judgei ∗ White Defj
+β7 Black Defj + β8 Hispanic Defj
+γ xi jt + δwit + εi jt ,
(4)
where Black Defj , Hispanic Defj and White Defj are dummy variables indicating that the defendant in case j is Black, Hispanic, or White, respectively, xi jt is a vector of case charac27 For
example, in the case of the U.S. Supreme Court, the only black justice, Clarence Thomas, is on the
conservative side of the ideological spectrum.
21
teristics, and wit is a vector of other characteristics of judge i and his/her county in year t.
Table 5 shows the results.
The coefficients for the full interactions between judges’ and defendants’ race and ethnicity are less precisely estimated than the coefficient for the race and ethnicity mismatch in
Table 4 because the number of observations in each group becomes smaller. However, the
results in Table 5 are still consistent with those in Table 4. African-American and Hispanic
judges show some favoritism for defendants of their own race or ethnicity in the full sample
(Column (1)) and in drug offenses (Column (5)), but the magnitude is small.28
Although not the focus of this paper, we investigated other hypotheses that appear in the
literature on criminal sentencing. For example, we investigated whether female judges give
longer sentences in sexual assault cases. We also investigated whether there is any genderbased favoritism – do female judges sentence male defendants more harshly, or do male
judges sentence female defendants more harshly? We find no substantively meaningful or
statistically significant differences between male and female judges in either case.
4.1.1
Sensitivity Analysis with Alternative Measures
We now analyze the sensitivity of our results to alternative measures of sentencing harshness.
We consider four variants of our baseline measure defined in equation (1) on page 14. Our
first alternative measure (Measure A) uses the minimum and the maximum sentence lengths
in each group of cases, instead of the 10th and 90th percentiles, as anchoring values in the
28 Drug-related
offenses (those involving drug possession in particular) are often classified as relatively mild.
One could interpret our findings as suggesting that racial and ethnical biases in sentencing tend to occur in the
less serious cases, maybe because judges deciding these cases are normally under low scrutiny. To address this
possibility, we estimated equation (4) using only non-drug-related offenses classified as “state jail felonies”, a
relatively mild severity level to which most drug procession cases in our data belong. The results indicate no
racial or ethnical bias by the judges. Estimating the same specification for drug-related state jail felonies, we
found results similar to those in column (5) of Table 5. These findings, which are available from the authors
upon request, provide further support for the hypothesis that drug-related cases are the only ones in which
sentencing is (slightly) biased in favor of defendants of he same race or ethnicity as the judge.
22
Table 5: The Influence of Judges’ Race on Sentencing Harshness - with Full Race Interaction
Variables
BlackJudge*BlackDef
BlackJudge*HispanicDef
BlackJudge*WhiteDef
HispanicJudge*BlackDef
HispanicJudge*HispanicDef
HispanicJudge*WhiteDef
Black Defendant
Hispanic Defendant
Female Defendant
Age at Offense
Age squared
Years in Office
Observations
R-squared
Dependent variable: Harshness
(1)
(2)
(3)
Full
Violent
Sexual
Sample
Offenses
Assaults
(4)
Property
Crimes
(5)
Drug
Offenses
-0.0261***
(0.0098)
-0.0113***
(0.0043)
0.0090
(0.0079)
0.0107
(0.0149)
-0.0096
(0.0087)
-0.0046
(0.0098)
-0.0075**
(0.0031)
0.0025
(0.0025)
-0.0609***
(0.0023)
0.0014**
(0.0005)
-0.0000
(0.0000)
-0.0002
(0.0003)
0.0271
(0.0257)
-0.0011
(0.0062)
0.0328***
(0.0101)
-0.0012
(0.0154)
0.0072
(0.0127)
-0.0142
(0.0105)
-0.0078
(0.0050)
-0.0244***
(0.0046)
-0.0807***
(0.0070)
0.0072***
(0.0013)
-0.0001***
(0.0000)
-0.0005
(0.0004)
0.0277
(0.0739)
0.0781***
(0.0158)
0.0470
(0.0342)
-0.0034
(0.0173)
0.0224
(0.0172)
-0.0009
(0.0256)
-0.0261**
(0.0050)
-0.0511***
(0.0121)
-0.1216***
(0.0299)
0.0304***
(0.0025)
-0.0003***
(0.0000)
-0.0010
(0.0007)
0.0036
(0.0088)
-0.0292**
(0.0137)
0.0074
(0.0056)
0.0389*
(0.0208)
0.0090
(0.0150)
0.0144
(0.0192)
-0.0319***
(0.0063)
-0.0247***
(0.0051)
-0.0351***
(0.0045)
0.0060***
(0.0012)
-0.0001***
(0.0000)
0.0003
(0.0005)
-0.0280***
(0.0065)
0.0039
(0.0086)
0.0423*
(0.0226)
0.0042
(0.0100)
-0.0352***
(0.0072)
-0.0136
(0.0097)
0.0117*
(0.0065)
0.0580***
(0.0060)
-0.0616***
(0.0037)
0.0026*
(0.0014)
-0.0001***
(0.0000)
-0.0001
(0.0003)
228,557
0.160
44,566
0.153
7,322
0.307
38,770
0.177
70,691
0.273
Note 1: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗ significant at 1%, ∗∗ significant at 5% and ∗ significant at 10%.
Note 2: All specifications include county-year fixed effects, offense categories (12 dummy variables for
13 categories), and the criminal history of defendants as control variables.
23
normalization of sentencing harshness. That is,
Measure A =
Sentence − minimum
.
maximum − minimum
(5)
Our second alternative measure (Measure B) uses the 10th and 90th percentiles for normalization as in our baseline measure. However, we do not use any observations whose jail time
is below the 10th percentile or above the 90th percentile, while in the baseline measure we
coded them as 0 and 1, respectively. That is,
Measure B =



missing



if Sentence < p10,
Sentence−p10
p90−p10




 missing
if p10 < Sentence < p90,
(6)
if Sentence > p90.
Our third alternative measure (Measure C) is identical to the baseline measure except that we
do not use bottom-coding or top-coding. That is, instead of coding sentence lengths below
the 10th percentile as 0 and above the 90th percentile as 1, we leave them as values below 0
and above 1, respectively. That is,
Measure C =
Sentence − p10
.
p90 − p10
(7)
Our fourth alternative measure (Measure D) is based on a different categorization of cases.
In addition to crime categories and sentencing year used for sentence normalization in our
baseline measure, Measure D considers the defendants’ criminal histories. For two cases
to belong to the same group, they should have identical number of defendants’ previous
convictions in felony and violent felonies. In sum, Measure D normalizes sentencing harshness relative to the group of cases that were sentenced with the same crime categories and
defendant criminal history and in the same year.
Tables 6 and 7 show the sensitivity analyses of the key results in Tables 4 and 5, respec24
Table 6: Sensitivity Analysis using Alternative Measures - Baseline Specification
Variables
Different Race
Black Judge
Hispanic Judge
Female Judge
Years in Office
Black Defendant
Hispanic Defendant
Female Defendant
Age at Offense
Age squared
Observations
R-squared
Dependent Variable (Measure of Sentencing Harshness)
(1)
(2)
(3)
(4)
(5)
Baseline
Measure A Measure B Measure C Measure D
0.0061*
(0.0035)
-0.0125***
(0.0043)
-0.0033
(0.0115)
0.0033
(0.0051)
-0.0002
(0.0003)
-0.0126**
(0.0053)
-0.0035
(0.0042)
-0.0609***
(0.0023)
0.0014**
(0.0005)
-0.0000
(0.0000)
0.0007
(0.0007)
0.0007
(0.0008)
-0.0007
(0.0017)
0.0009
(0.0009)
-0.0001
(0.0001)
-0.0004
(0.0009)
-0.0018***
(0.0006)
-0.0114***
(0.0007)
0.0015***
(0.0002)
-0.0000***
(0.0000)
0.0042
(0.0026)
-0.0117***
(0.0031)
-0.0034
(0.0095)
0.0029
(0.0041)
-0.0001
(0.0003)
-0.0117***
(0.0038)
-0.0013
(0.0034)
-0.0373***
(0.0020)
-0.0011***
(0.0004)
0.0000**
(0.0000)
0.0149*
(0.0077)
-0.0136
(0.0098)
-0.0072
(0.0190)
0.0098
(0.0084)
-0.0003
(0.0005)
-0.0099
(0.0110)
-0.0148*
(0.0084)
-0.1276***
(0.0097)
0.0117***
(0.0017)
-0.0001***
(0.0000)
0.0064**
(0.0029)
-0.0144***
(0.0033)
-0.0073
(0.0101)
0.0052
(0.0049)
-0.0003
(0.0003)
-0.0094**
(0.0047)
-0.0010
(0.0037)
-0.0585***
(0.0024)
0.0021***
(0.0006)
-0.0000
(0.0000)
228,557
0.160
228,549
0.197
200,490
0.132
228,549
0.080
208,675
0.154
Note 1: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗
significant at 1%, ∗∗ significant at 5% and ∗ significant at 10%.
Note 2: All specifications include county-year fixed effects, offense categories (12 dummy variables for 13 categories), and the criminal history of defendants as control variables.
25
Table 7: Sensitivity Analysis using Alternative Measures - with Full Race Interactions
Variables
BlackJudge*BlackDef
BlackJudge*HispanicDef
BlackJudge*WhiteDef
HispanicJudge*BlackDef
HispanicJudge*HispanicDef
HispanicJudge*WhiteDef
Black Defendant
Hispanic Defendant
Female Defendant
Age at Offense
Age squared
Years in Office
Observations
R-squared
Dependent Variable (Measure of Sentencing Harshness)
(1)
(2)
(3)
(4)
(5)
Baseline
Measure A Measure B Measure C Measure D
-0.0261***
(0.0098)
-0.0113***
(0.0043)
0.0090
(0.0079)
0.0107
(0.0149)
-0.0096
(0.0087)
-0.0046
(0.0098)
-0.0075**
(0.0031)
0.0025
(0.0025)
-0.0609***
(0.0023)
0.0014**
(0.0005)
-0.0000
(0.0000)
-0.0002
(0.0003)
-0.0011
(0.0028)
0.0008
(0.0019)
0.0034**
(0.0017)
-0.0004
(0.0023)
-0.0008
(0.0017)
-0.0001
(0.0017)
0.0004
(0.0006)
-0.0012**
(0.0006)
-0.0114***
(0.0007)
0.0015***
(0.0002)
-0.0000***
(0.0000)
-0.0001*
(0.0000)
-0.0218***
(0.0048)
-0.0093***
(0.0016)
0.0031
(0.0084)
0.0129
(0.0113)
-0.0088
(0.0081)
-0.0079
(0.0083)
-0.0090***
(0.0025)
0.0027
(0.0021)
-0.0373***
(0.0020)
-0.0011***
(0.0004)
0.0000***
(0.0000)
-0.0001
(0.0003)
-0.0418
(0.0266)
-0.0077
(0.0217)
0.0174
(0.0154)
0.0006
(0.0233)
-0.0166
(0.0181)
0.0066
(0.0231)
0.0051
(0.0065)
-0.0003
(0.0056)
-0.1275***
(0.0097)
0.0117***
(0.0017)
-0.0001***
(0.0000)
-0.0004
(0.0005)
-0.0222***
(0.0080)
-0.0131***
(0.0024)
0.0007
(0.0076)
0.0043
(0.0141)
-0.0125*
(0.0074)
-0.0035
(0.0091)
-0.0039
(0.0030)
0.0055**
(0.0023)
-0.0584***
(0.0024)
0.0020***
(0.0006)
-0.0000
(0.0000)
-0.0003
(0.0003)
228,557
0.160
228,549
0.197
200,490
0.133
228,549
0.080
208,675
0.154
Note 1: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗ significant at 1%, ∗∗ significant at 5% and ∗ significant at 10%.
Note 2: All specifications include county-year fixed effects, offense categories (12 dummy variables for
13 categories), and the criminal history of defendants as control variables.
26
tively. The results are remarkably robust to changes in the measure of sentencing harshness.
Judges are slightly more lenient towards defendants of the same race or ethnicity. The analysis with the full set of interactions suggests that this result is driven by African-American
and Hispanic judges. Thus, judges’ race and ethnicity seem to matter in some cases. But
the smallness of the estimate implies that the overall magnitude of the influence is rather
small.29
4.2
The Influence of Judges’ Political Background
We now turn to the analysis of how judges’ political background is reflected in their sentencing harshness. We first estimate partisan bias without interacting it with defendant characteristics:
Harshnessijt = β0 + β1 Republicani + γ xi jt + δwit + εi jt ,
(8)
where Republicani is a dummy variable indicating that judge i is Republican, xi jt is a vector
of case characteristics, and wit is a vector of other characteristics of judge i and his/her county
in year t. The results are presented in Table 8. The influence of party affiliation is precisely
estimated, and suggests that, if anything, Republican judges tend to assign slightly shorter
sentences than Democrats and independents in sexual assault and property crime cases. For
29 A
potential concern with all our measures of sentencing harshness is that our data contains only incarceration sentences. Cases resulting in other outcomes such as probation or community service are not observed,
which causes a sample selection problem. One way to address this issue is to treat the selection process as
one of truncation – i.e., model incarceration sentences as positive realizations of a latent harshness variable
that assumes negative values when a case results in a non-incarceration sentence. Under this assumption, the
selection problem can be addressed by estimating a truncated regression model. A challenge with this approach
in our setting is incorporating county-year fixed effects. Using our full sample, there are too many county-year
parameters to be estimated, which hinders convergence of the estimator. We therefore restricted our attention
to cases resolved in four large counties – Harris, Dallas, Tarrant and Bexar. We estimated equations (2), (3), (4)
and (8) (the last of which is to be discussed in section 4.2) by OLS and truncated regression model, controlling
for county and year-specific fixed effects. The results, which are available from the authors upon request, are
almost identical for the OLS and the truncated model. This suggests that the OLS results presented throughout
the paper are not heavily affected by sample selection.
27
Table 8: The Influence of Judges’ Party Affiliation on Sentencing Harshness - Baseline
Variables
Republican
Black Defendant
Hispanic Defendant
Female Defendant
Age at Offense
Age squared
Years in Office
Observations
R-squared
Dependent variable: Harshness
(1)
(2)
(3)
Full
Violent
Sexual
Sample
Offenses
Assaults
(4)
Property
Crimes
(5)
Drug
Offenses
-0.0088
(0.0092)
-0.0078**
(0.0032)
0.0005
(0.0026)
-0.0612***
(0.0024)
0.0014**
(0.0005)
-0.0000
(0.0000)
-0.0001
(0.0003)
-0.0133
(0.0172)
-0.0061
(0.0051)
-0.0213***
(0.0044)
-0.0821***
(0.0066)
0.0074***
(0.0013)
-0.0001***
(0.0000)
-0.0005
(0.0004)
-0.0223*
(0.0123)
-0.0247*
(0.0128)
-0.0462***
(0.0121)
-0.1272***
(0.0302)
0.0304***
(0.0026)
-0.0003***
(0.0000)
-0.0011
(0.0008)
-0.0256**
(0.0108)
-0.0302***
(0.0057)
-0.0282***
(0.0065)
-0.0360***
(0.0043)
0.0061***
(0.0012)
-0.0001***
(0.0000)
0.0003
(0.0005)
0.0058
(0.0063)
0.0104
(0.0069)
0.0523***
(0.0062)
-0.0615***
(0.0037)
0.0026*
(0.0014)
-0.0001***
(0.0000)
0.0001
(0.0003)
219,489
0.161
42,933
0.153
7,047
0.305
37,370
0.177
67,542
0.275
Note 1: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗
significant at 1%, ∗∗ significant at 5% and ∗ significant at 10%.
Note 2: All specifications include county-year fixed effects, offense categories (12 dummy variables for 13 categories), and the criminal history of defendants as control variables.
other crime categories, the effect of party affiliation is statistically insignificant. Even when
the effect is statistically significant, its magnitude is small. This result is consistent with an
early study by Ashenfelter et al. (1995), which finds that the party affiliation of a judge’s
nominating president does not significantly affect trial outcomes. Unlike many appellate
court decisions, sentencing decisions by trial court judges are essentially bureaucratic tasks
rather than policy-making. Thus, the absence of partisan bias is plausible.
In Table 9, we present a set of sensitivity analyses. In Column (2), we include other
characteristics of judges, in addition to party affiliation. Specifically, we include judges’
party affiliation interacted with the dummy variable of having short tenure (less than 4 years),
as well as their race and gender. The rationale is that inexperienced judges may rely more
28
29
219,489
0.161
Yes
-0.0078**
(0.0032)
0.0005
(0.0026)
-0.0612***
(0.0024)
0.0014**
(0.0005)
-0.0000
(0.0000)
-0.0001
(0.0003)
-0.0088
(0.0092)
(1)
Baseline
219,489
0.161
Yes
-0.0078**
(0.0032)
0.0005
(0.0026)
-0.0612***
(0.0024)
0.0014**
(0.0005)
-0.0000
(0.0000)
-0.0002
(0.0005)
-0.0053
(0.0086)
-0.0081
(0.0105)
-0.0102
(0.0070)
-0.0133***
(0.0047)
-0.0067
(0.0130)
0.0038
(0.0051)
(2)
Augmented
43,155
0.111
Yes
-0.0031
(0.0052)
0.0062
(0.0081)
-0.0564***
(0.0039)
0.0007
(0.0011)
-0.0000
(0.0000)
-0.0010*
(0.0006)
-0.0133**
(0.0064)
(3)
Balanced districts
219,489
0.161
Yes
0.0102
(0.0080)
0.0006
(0.0046)
-0.0043
(0.0056)
-0.0144**
(0.0065)
-0.0002
(0.0036)
-0.0584***
(0.0041)
0.0014**
(0.0005)
-0.0000
(0.0000)
-0.0001
(0.0003)
-0.0112
(0.0099)
(4)
Interaction
219,481
0.197
Yes
0.0002
(0.0006)
-0.0015***
(0.0005)
-0.0114***
(0.0007)
0.0015***
(0.0002)
-0.0000***
(0.0000)
-0.0001*
(0.0000)
-0.0013
(0.0018)
(5)
Measure A
192,492
0.134
Yes
-0.0080***
(0.0025)
0.0018
(0.0022)
-0.0374***
(0.0020)
-0.0011**
(0.0004)
0.0000***
(0.0000)
-0.0001
(0.0003)
-0.0047
(0.0084)
(6)
Measure B
219,481
0.084
Yes
0.0012
(0.0068)
-0.0050
(0.0060)
-0.1283***
(0.0100)
0.0117***
(0.0017)
-0.0001***
(0.0000)
-0.0003
(0.0005)
-0.0124
(0.0197)
(7)
Measure C
200,422
0.155
Yes
-0.0046
(0.0031)
0.0030
(0.0024)
-0.0590***
(0.0024)
0.0021***
(0.0006)
-0.0000
(0.0000)
-0.0002
(0.0003)
-0.0099
(0.0098)
(8)
Measure D
Note 1: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗ significant at 1%, ∗∗ significant at 5% and ∗ significant at 10%.
Note 2: All specifications include county-year fixed effects, offense categories (12 dummy variables for 13 categories), and the criminal history of defendants
as control variables.
Observations
R-squared
County-year FE
Short Tenure
Years in Office
Age squared
Age at Offense
Female Defendant
Hispanic Defendant
Black Defendant
Republican*Female Defendant
Republican*Hispanic Defendant
Republican*Black Defendant
Female Judge
Hispanic Judge
Black Judge
Republican*Short Tenure
Republican
Variables
Table 9: The Influence of Judges’ Party Affiliation on Sentencing Harshness - Sensitivity Analysis
heavily on their intuition rather than formal knowledge of law, which may in turn make them
more influenced by their political orientation. The estimate shows that there is no such effect.
In Column (3), we use only the set of counties where the average Democratic Vote Share is
between 45 and 55 percent, i.e., counties that are ideologically balanced. The result shows
almost no change from the baseline specification using all counties.30 In Column (4), we
include interactions between judges’ party affiliation with defendants’ race and gender: This
is to investigate whether judges with more conservative ideology treat female defendants
or defendants with minority backgrounds differently. The result shows no such effect. In
Columns (5)-(8), we use alternative measures of sentencing harshness defined in Section
4.1.1. The key result is again very robust to using alternative measures.
It is possible that, even though trial judges would like to act in a more explicitly partisan
manner, the influence of party affiliation on their behavior is limited by the possibility of
having controversial decisions overturned by the appellate courts, which would rationalize
the null results reported above. If this hypothesis is true, it is possible that decisions taken
by trial judges depend on how liberal or conservative the appellate courts are. We tested
this hypothesis using variation in the partisan composition of the Texas courts of appeals.
The state is geographically divided into fourteen courts of appeals.31 Using electoral data,
Texas Courts Online, the Appellate Advocate, and the American Bench, we reconstructed
the partisanship of each court of appeals for each year of our sample. The courts of appeals
are predominately Republican, reflecting the political orientation of the state. However, two
of the courts had a majority of Democrats in the period covered by our data, and one court
30 Given
that the estimate of party influence in the whole set of counties is negligible, it is natural that we
obtain negligible estimates in ideologically balanced counties. The main reason why existing studies often
focus on ideologically balanced electorates (e.g., Lee et al. (2004); Ferreira and Gyourko (2009)) is because
using the entire set of counties leads to confounding the influence of public officials’ party affiliation with that
of electorates’ ideology. This in turn leads to an over-estimate of the party influence. That is, focusing on
ideologically balanced electorates only reduces the estimate of party influence.
31 Except in a few cases, counties are not split across these Courts. Harris County (Houston) is served by the
1st and 14th courts of appeals. The number of justices varies across courts, from three to 13.
30
had a Democratic majority during a part of this period.32 Seven of the fourteen courts exhibited some changes in partisanship during the data period.33 We added the interaction of
the district judge’s party with the proportion of Republican judges at the court of appeals to
equation (8). We found no systematic evidence of the influence of appellate court partisanship on sentencing.
4.3
The Extent of Judge Heterogeneity
The analyses above show that key observable characteristics of judges do not have much
explanatory power for sentencing harshness, conditional on geographic factors. This finding
leads to an important question: do judges vary at all in sentencing harshness in Texas? Several studies found substantial cross-judge variation in decisions on criminal cases in other
settings and using other measures. For example, Abrams et al. (2012) find significant crossjudge heterogeneity in the racial gap in incarceration rates in Cook County, Illinois. Lim
(2013) also finds that sentencing harshness varies substantially across the political orientation
of electorates when judges are selected and retained through partisan elections in Kansas.34
To investigate this issue, we first document the extent of cross-judge heterogeneity in
sentencing harshness. Then, we conduct additional analyses to explore its causes. First, we
examine the extent to which cross-judge variation in sentencing is explained by the fact that
32 The average proportion of Republican judges in the courts of appeals over the 2004-2013 period is 76.38%.
Both the 8th and the 13th courts of appeals start 2004 as entirely Democrat. The former court remains entirely
Democrat over the period covered by our data, while, in the latter court, the proportion of Republican judges
increases to one-third by 2013. The 6th court of appeals has a proportion of one-fourth Republican judges in
2004, which increases to two-thirds by 2013.
33 The overall standard deviation of the shares of Republican judges across courts of appeals and over time
in our data is 0.32. If we subtract from these shares the means at the court of appeals level and leave only
the variation over time, the standard deviation is still 0.08. This within-court variation allows us to control for
county fixed effects (without the interaction with year fixed effects) in the regressions described below.
34 She argues that reelection incentives play an important role in sentencing variation across districts. She
also conducts various simulations to show that the relationship between the political orientation of electorates
and sentencing harshness critically depends on judges’ payoff from the office. If judges’ payoff from the office
is not significantly higher than their potential payoff from outside options (e.g., law practice), then reelection
incentives may be weak, which in turn reduces differences in sentencing harshness across areas.
31
they serve in different areas.35 Second, we analyze the extent to which electorates’ racial
composition and political orientation are related to judges’ sentencing harshness. Third, we
examine the relationship between various characteristics of judges and sentencing harshness,
unconditional on geographic factors. To quantify the extent of cross-judge heterogeneity in
sentencing harshness, we estimate a regression model of the following form:
Harshnessijt = α + βxi jt + γwi + δzt + εi jt ,
(9)
where xi jt is a vector of case characteristics, wi is a judge fixed effect, zt is a year fixed ef-
0
1
Density
2
3
4
fect, and εi jt captures idiosyncratic, unobservable characteristics of the case. Figure 2 shows
-.2
0
.2
Judge Fixed Effects
.4
.6
0.00
Mean
0.11
SD
Min
-0.25
p25
-0.07
Median
0.01
p75
0.07
Max
0.70
Count
400.00
F=55.959
p-value=0.00
Figure 2: Judge Fixed Effects
a histogram of judge fixed effects from the above model (9), their summary statistics, and
35 Our
analysis in this section is, to some extent, related to an empirical literature that investigates the impact
of teachers on the performance of students. For a survey of that literature, see McCaffrey et al. (2004). Similar
to a sentencing decision—which depends on the judge, the county of prosecution and the characteristics of the
case—the performance of a student depends on the teacher, the classroom and the said student’s characteristics.
Papers in the teachers’ impact literature often employ empirical Bayes “shrinkage” methods to distinguish
teacher-specific effects from classroom-specific ones. Recent examples include Kane and Staiger (2008) and
Chetty et al. (2005). In principle, we could adapt these methods to separately estimate judge and countyspecific effects in our setting. However, to the extent of our knowledge, doing so would require us to assume
that these two effects are independently distributed. Such an assumption is likely to be unreasonable in the
context of our analysis, since Texas is a large and heterogeneous state, and judges are locally elected. Indeed,
in the current section, we present evidence that observable characteristics of judges’ political jurisdictions are
related to sentencing harshness. Therefore, we decided against using shrinkage methods in our study.
32
the F-test result of a hypothesis that all the judge fixed effects are zero.36 The standard deviation of judge fixed effects is .11 points, that is, 11% of the approximate range of judges’
discretion—which is comparable to the effect of increasing the number of previous violent
crime convictions of the defendant from none to two.37 The interquartile range, 0.14 points,
is close to the effect of changing criminal history from none to three violent crime convictions. Using the conventional F-test, we reject the hypothesis that judge fixed effects do not
affect sentencing.
4.3.1
Variation Across Judges vs. Variation Across Counties
How much of the variation in sentencing behavior across judges is driven by the fact that different judges serve in different areas, and how much is due to judge-specific factors? We can
assess this by comparing different judges in the same county. For judges who serve multiple
counties, we can also assess the degree to which judges are consistent in their sentencing
behavior across counties. While judges might seek consistency, they might also vary their
sentencing behavior across counties, perhaps to cater to local tastes, or to avoid “sticking
out” relative to other judges serving in a given county. To address these issues, we estimate
a regression model of the following form:
Harshnessijt = α + βxi jt + γwic + δzt + εi jt ,
(10)
where xi jt is a vector of case characteristics (the criminal history of defendants and crime
category), wic is a vector of judge-county dummies, zt is a vector of year indicators, and εi jt
captures idiosyncratic, unobservable characteristics of the case.
36 To
avoid estimates of judge heterogeneity being driven by judges who handle a small number of cases, we
restrict this analysis to judges who handled at least 50 cases.
37 In our data, having one, two, and three previous convictions of violent crimes increases sentencing harshness by 0.06, 0.10, and 0.19 points, respectively, compared with a defendant who has no history of violent
crime convictions.
33
The vector γ captures judge-county fixed effects. Our estimates for these fixed effects
present three revealing patterns. First, the within-county variation across judges is much
larger than the within-judge variation across counties. Specifically, let γic denote the estimated fixed-effect for judge i in county c. Averaging across counties, the standard deviation
of the γic across judges within counties is .252. Averaging across judges, the standard deviation of the γic across counties within judges is just .152.
Second, as a corollary, the variation across judges accounts for much more of the overall
variation in the γic ’s than the variation across counties. For each judge i, let γi be the average
of the γic across the counties i serves, and for each county c, let γc be the average of the γic
across the judges who serve in c. Regressing γic on γi yields an R2 of .97, while regressing
γic on γc yields an R2 of only .16.38
Third, there is little evidence that judges shift their sentencing behavior toward other
judges in counties they serve. For each judge i and each county c, let γc,−i be the average of
the γic across all judges who serve in c other than judge i. Also, let γi,−c be the average of the
γic across all counties served by judges i other than c. Regressing γic on both γc,−i and γi,−c
yields the results in Table 10. The coefficient on γc,−i is nearly zero and statistically insignificant, while the coefficient on γi,−c is large and highly significant. That is, the idiosyncratic
features of a given judge’s sentencing behavior are essentially unrelated to the behavior of
other judges in the counties served by the judge. On the other hand, the idiosyncratic features of a given judge’s sentencing behavior are quite similar across the counties served by
the judge.
4.3.2
The Influence of Localities and Political Jurisdictions
We now investigate the influence of localities (counties) and political jurisdictions (judicial
districts) to understand sources of cross-judge heterogeneity in sentencing harshness. In the
38 Regressing
γic on both γi and γc also yields an R2 of .97.
34
Table 10: Decomposition of Judge-County Fixed Effects
Dependent variable: γic
γc,−i
-.004
(.030)
γi,−c
.961
(.026)
constant
-.000
(.006)
2
R
.923
Observations
159
analyses presented in Table 11, we regress our normalized measure of sentencing harshness,
Harshness, on demographic characteristics, political orientation, and their interaction with
defendant and judge characteristics.39 For demographic characteristics, we use the share
of black population, the share of Hispanics, (log) per-capita income, and (log) crime rate.
For political orientation, we use Democratic Vote Share. We measure these variables at two
levels – the county where the case was prosecuted and the district of the judge deciding the
case.
Columns (1)-(3) report the results obtained using our full sample and measuring demographic and political orientation variables at the county level. In Column (1), we interact the
defendant’s race with the racial composition of the county where the case was prosecuted.
In Column (2), we interact the defendant’s race with the political orientation of the county.
In Column (3), we add the judge’s party affiliation interacted with the political orientation
of the county. The results suggest that the share of African-Americans and Hispanics in the
county population is negatively correlated with the harshness of the assigned sentences. The
effect of the African-American population is non-trivial. An increase of ten p.p. in the share
African-Americans is associated to a decrease of approximately two percent in Harshness
(−0.20 ∗ 0.10 = −0.02). The same increase in the share of Hispanics is associated with a
39 We
also control for crime categories and include year fixed effects in all the seven specifications.
35
36
Geographic Unit
Observations
R-squared
(log) Crime Rate
(log) Per-capita Income
Democratic Vote Share (DVS)
Age Squared
Age At Offense
Female Defendant
Republican Judge * DVS
Republican Judge
Hispanic Defendant * DVS
Hispanic Defendant *Share Hispanic
Share Hispanic
Hispanic Defendant
Black Defendant * DVS
Black Defendant * Share Black
Share Black
Black Defendant
County
248,151
0.117
-0.0607***
(0.0022)
0.0016***
(0.0005)
-0.0000
(0.0000)
-0.0032***
(0.0007)
-0.1612***
(0.0348)
-0.0123**
(0.0056)
0.0212
(0.0155)
-0.0966*
(0.0557)
-0.0435
(0.0430)
-0.0211*
(0.0113)
-0.2253**
(0.1041)
0.0837
(0.0722)
(1)
County
248,151
0.117
-0.0606***
(0.0021)
0.0016***
(0.0005)
-0.0000
(0.0000)
-0.0029***
(0.0007)
-0.1514***
(0.0362)
-0.0131**
(0.0056)
-0.0003
(0.0005)
-0.0007
(0.0005)
0.0179
(0.0184)
-0.1106**
(0.0533)
0.0159
(0.0168)
-0.1925*
(0.0979)
(2)
County
219,350
0.116
-0.0001
(0.0004)
-0.0711**
(0.0353)
0.0020**
(0.0009)
-0.0597***
(0.0023)
0.0017***
(0.0006)
-0.0000
(0.0000)
-0.0039***
(0.0007)
-0.1450***
(0.0353)
-0.0136**
(0.0056)
-0.0006
(0.0004)
0.0061
(0.0148)
-0.0997*
(0.0519)
0.0109
(0.0163)
-0.2163**
(0.1076)
(3)
County
61,466
0.096
-0.0627***
(0.0043)
0.0007
(0.0010)
0.0000
(0.0000)
-0.0012*
(0.0007)
-0.0072
(0.0331)
-0.0033
(0.0049)
0.0149
(0.0133)
0.0078
(0.0437)
-0.0188
(0.0315)
0.0069
(0.0134)
0.0226
(0.1106)
-0.0778
(0.1570)
(4)
County
61,466
0.096
-0.0627***
(0.0043)
0.0008
(0.0010)
0.0000
(0.0000)
-0.0015*
(0.0008)
-0.0031
(0.0336)
-0.0037
(0.0051)
0.0003
(0.0005)
0.0002
(0.0007)
-0.0007
(0.0173)
0.0034
(0.0433)
-0.0071
(0.0201)
0.0156
(0.1135)
(5)
(6)
County
58,968
0.098
0.0006
(0.0005)
-0.0445*
(0.0267)
0.0020**
(0.0008)
-0.0635***
(0.0043)
0.0009
(0.0010)
0.0000
(0.0000)
-0.0019**
(0.0008)
-0.0089
(0.0337)
-0.0035
(0.0045)
0.0001
(0.0006)
-0.0137
(0.0162)
-0.0167
(0.0421)
-0.0050
(0.0192)
-0.0679
(0.1099)
Table 11: The Influence of Localities and Political Jurisdictions
District
61,589
0.096
-0.0635***
(0.0043)
0.0007
(0.0010)
0.0000
(0.0000)
-0.0012
(0.0007)
0.0012
(0.0393)
-0.0096
(0.0068)
0.0107
(0.0137)
0.0117
(0.0438)
-0.0108
(0.0315)
0.0065
(0.0140)
0.0696
(0.1209)
-0.0940
(0.1707)
(7)
District
61,589
0.096
-0.0635***
(0.0043)
0.0008
(0.0010)
0.0000
(0.0000)
-0.0015*
(0.0008)
0.0056
(0.0393)
-0.0100
(0.0069)
0.0003
(0.0005)
0.0001
(0.0007)
-0.0037
(0.0181)
0.0094
(0.0422)
-0.0068
(0.0214)
0.0573
(0.1162)
(8)
District
59,091
0.098
0.0007
(0.0005)
-0.0455
(0.0285)
0.0019**
(0.0009)
-0.0642***
(0.0043)
0.0009
(0.0010)
0.0000
(0.0000)
-0.0020**
(0.0008)
-0.0028
(0.0414)
-0.0094
(0.0067)
-0.0001
(0.0007)
-0.0171
(0.0162)
-0.0087
(0.0423)
-0.0014
(0.0206)
-0.0223
(0.1147)
(9)
decrease of only one percent in the measure of harshness. The effects of racial and ethnic
composition of the county do not depend on the defendants’ race and ethnicity.
All of the three columns consistently show a moderate but statistically significant influence of the political orientation and income level of the communities.40 Counties that are
liberal (with a large value of DVS) or have high income tend to have more lenient judges. A
one standard deviation (14 percentage point) increase in Democratic Vote Share decreases
Harshness by approximately four percent (0.003 ∗ 14 ≈ 0.042) of the range of sentencing
harshness. Interestingly, column (3) shows a statistically significant coefficient estimate of
Republican ∗ DVS. The sign of the coefficient is positive, indicating that Republican judges
tend to become harsher on the defendant as the county gets more liberal, but the magnitude
of the effect is small. As for income, a one standard deviation (.20) increase in (log) percapita income decreases Harshness by approximately three percent (−0.15 ∗ 0.20 = −0.03)
of its range.41
We are interested in assessing the relative importance of the county of prosecution versus
the judicial district in explaining variations in sentencing harshness. Unfortunately, in our
full sample, the correlation between variables measured at the county and at the district
levels is very high.42 We therefore consider a subsample of cases from judicial areas with
a multi-county, multi-district overlapping pattern.43 Focusing on these areas alleviates to
some extent the correlation between county-level and district-level variables.44 Although
40 Crime
rate is also significantly correlated with Harshness. This should obviously be interpreted as the
result of reverse causality (i.e., the influence of sentencing on crime rates rather than vice versa).
41 Theoretically, it is not obvious in what direction income level should be correlated with sentencing harshness. On one hand, low income communities may be more conscious of social problems associated with crimes
(gang activities, drug problems, etc.), which would in turn generate strong social pressure to reduce crime. On
the other hand, affluent communities may be more sensitive to property crimes than poor communities because the economic loss would be larger in the former. The overall relationship between the income level of
communities and sentencing harshness will be the combination of these two forces.
42 Using variables measured at the district level in specifications analogous to the ones in columns (1)-(3)
of Table 11 generates nearly identical results. The correlation between variables measured at the county and
district levels using the full sample ranges between 0.98 and 0.99 for each one of the variables considered.
43 Specifically, we use areas with overlapping patterns C, E and F in Table 1.
44 The correlation coefficients are as follows: 0.97 for the Democratic vote share, 0.93 for the black population share, 0.97 for the Hispanic share, 0.89 for per capita income and 0.73 for the crime rate.
37
it is still not possible to consider specifications simultaneously including county-level and
district-level characteristics, we are able to separately analyze the influence of these two sets
of variables on sentencing harshness and compare the magnitude of the estimated effects.45
Columns (4)-(6) of Table 11 present regression results using only cases from multi-county,
multi-district areas and county-level variables. Columns (7)-(9) present the results of similar
regressions using district-level variables. We find no evidence on the relationship between
racial composition and sentencing harshness neither at the county level nor at the district
level. Concerning political orientation, the absolute value of the coefficients is smaller than
in the full sample. However, they are statistically significant, and the magnitude is similar for
the county and the district levels. The coefficient estimates of Republican ∗ DVS in columns
(6) and (9) are statistically significant and very close to the estimates obtained with the full
sample. Neither the local racial and ethnic composition nor crime or per-capita income
are significant in any of Columns (4)-(9), unlike in the full sample. However, coefficient
estimates are of similar magnitude for the county and the district levels. Overall, we do
not find any systematic evidence that relationships between characteristics of communities
and sentencing harshness are driven by district-level versus county-level variations. Rather,
county-level variables seem to be related to sentencing in a similar way to district-level
variables.
4.3.3
The Influence of Judges’ Backgrounds without County-year Fixed Effects
In this subsection, we present additional analyses of the relationship between judges’ sentencing harshness and their backgrounds. The results from the preceding analyses can be
summarized as follows: (1) judges’ demographic characteristics have almost no explanatory
power conditional on geographic factors (county-year fixed effects); (2) nevertheless, there is
substantial cross-judge heterogeneity in sentencing harshness; and (3) observable character45 The results of regressions simultaneously including county-level and district-level variables, which are
available from the authors upon request, show clear signs of multicollinearity.
38
istics of localities and political jurisdictions only have moderate relationships to sentencing
harshness. These observations lead us to the following question: to what extent do judges’
demographic backgrounds explain their sentencing harshness if we do not condition on geographic factors? Do other elements of the judges’ backgrounds, such as career history, have
any explanatory power? We address these questions below.
Table 12: Regression of Judge Fixed Effects on Demographic and Career Backgrounds
Dependent Variable: Judge Fixed Effect
Variables
Total Legal Experience
(1)
(2)
(3)
0.0004
(0.0008)
(4)
(5)
(6)
-0.0016
(0.0012)
-0.0533
(0.0455)
-0.0428**
(0.0210)
-0.0258
(0.0168)
0.0001
(0.0139)
307
0.042
-0.0517
(0.0459)
-0.0416*
(0.0213)
-0.0247
(0.0171)
0.0008
(0.0141)
-0.0389
(0.0510)
-0.0302
(0.0232)
-0.0213
(0.0187)
0.0020
(0.0156)
-0.0478
(0.0519)
-0.0307
(0.0237)
-0.0291
(0.0184)
0.0010
(0.0159)
-0.0393
(0.0517)
-0.0216
(0.0243)
-0.0219
(0.0192)
0.0036
(0.0162)
-0.0052
(0.0049)
0.0001
(0.0001)
0.0084***
(0.0029)
-0.0002**
(0.0001)
-0.0018
(0.0039)
0.0002
(0.0002)
-0.0281
(0.0514)
-0.0244
(0.0241)
-0.0163
(0.0191)
0.0050
(0.0161)
304
0.043
256
0.060
256
0.036
243
0.065
243
0.095
Total Legal Experience2
Private Law Practice
0.0017**
(0.0007)
0.0029***
(0.0011)
Private Law Practice2
Prosecution
-0.0009
(0.0012)
0.0010
(0.0014)
Prosecution2
Black Judge
Hispanic Judge
Female Judge
Republican Judge
Observations
R-squared
Note: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗ significant
at 1%, ∗∗ significant at 5% and ∗ significant at 10%. In all regressions, unit of observation is individual
judge.
In Table 12, we regress judge fixed effects, obtained in Section 4.3, on judges’ demographic characteristics and their career history. For their career history, we use three variables: total legal experience, experience in private law practice, and experience in prosecution—
39
all of which are measured in number of years.
The results indicate that Hispanic judges are slightly more lenient than non-Hispanic ones,
although the effect is only statistically significant in two out of six specifications. The point
estimates suggest that female and African-American judges are associated with lenient sentencing, but the effects are always small in magnitude and statistically insignificant. Interestingly, party affiliation has almost no relationship with sentencing harshness, even unconditional on geographic factors.
The results also indicate that career history has little relationship with sentencing harshness. Only the experience in private law practice has a statistically significant relationship
with sentencing harshness in a subset of regressions, and the magnitude of the coefficient is
small. In Columns (2) and (4) and (5), one standard deviation (10 years) increase in private
law practice is associated with an increase in sentencing harshness by 1.7 (0.0017*10=0.015)
to 8.4 percent of the range.
In Table 13, we present case-level regressions of sentencing on judges’ backgrounds. In
Column (3), we measure the lengths of experience in private law practice and prosecution as
their ratio to the total legal experience. The key difference between this set of regressions and
its counterpart in Section 4.1 is that we do not control for county-year fixed effects. The key
results are consistent with Table 12. African-American and Hispanic judges are moderately
associated with lenient sentencing, though the relationship is statistically insignificant in
many of the specifications. Career history and party affiliation have little explanatory power.
4.4
A Counterfactual Experiment: Judicial Redistricting
In this section, we evaluate the extent to which differences in sentencing patterns across
Texas counties could be alleviated by judicial redistricting. The results reported in Section
4.3 show substantial heterogeneity in the sentencing behavior across judges. Moreover, they
indicate that such heterogeneity is, to a large extent, due to judge-specific factors rather than
40
41
114,841
0.171
-0.0149*
(0.0079)
-0.0348*
(0.0201)
0.0071
(0.0126)
-0.0305***
(0.0101)
0.0002
(0.0008)
-0.0006
(0.0009)
0.0005
(0.0006)
-0.0010
(0.0007)
114,841
0.087
-0.0868**
(0.0402)
-0.0239
(0.0385)
-0.0107
(0.0182)
0.0274
(0.0253)
0.0019
(0.0016)
0.0013
(0.0012)
0.0018
(0.0017)
-0.0024
(0.0019)
114,841
0.087
0.0209
(0.0324)
-0.0827**
(0.0397)
-0.0241
(0.0378)
-0.0066
(0.0173)
0.0279
(0.0256)
0.0397
(0.0260)
0.0016
(0.0016)
-0.0013
(0.0017)
114,841
0.088
-0.0811*
(0.0417)
-0.0263
(0.0386)
-0.0066
(0.0173)
0.0289
(0.0254)
0.0010
(0.0045)
0.0001
(0.0002)
0.0017
(0.0017)
-0.0067
(0.0043)
0.0001
(0.0001)
0.0052
(0.0032)
-0.0001
(0.0001)
(4)
22,319
0.067
-0.0258
(0.0472)
-0.0605
(0.0368)
-0.0039
(0.0158)
0.0285
(0.0197)
0.0003
(0.0041)
0.0002
(0.0002)
0.0031*
(0.0016)
-0.0059
(0.0039)
0.0000
(0.0001)
0.0053*
(0.0028)
-0.0001
(0.0001)
Violent
Crime
(5)
3,598
0.133
0.0381
(0.0344)
-0.0567*
(0.0321)
-0.0194
(0.0202)
0.0111
(0.0211)
-0.0004
(0.0042)
0.0001
(0.0002)
0.0019
(0.0020)
-0.0037
(0.0049)
0.0001
(0.0001)
0.0056*
(0.0032)
-0.0002**
(0.0001)
Sexual
Assault
(6)
35,525
0.176
-0.1184***
(0.0404)
-0.0025
(0.0378)
-0.0187
(0.0217)
0.0295
(0.0265)
0.0017
(0.0045)
0.0000
(0.0002)
0.0014
(0.0018)
-0.0015
(0.0050)
0.0000
(0.0001)
0.0030
(0.0034)
-0.0001
(0.0001)
Drug
Offense
(7)
19,728
0.056
-0.0809**
(0.0326)
0.0042
(0.0344)
0.0075
(0.0186)
0.0002
(0.0317)
-0.0030
(0.0048)
0.0004
(0.0003)
0.0013
(0.0018)
-0.0045
(0.0044)
0.0001
(0.0001)
0.0026
(0.0036)
-0.0000
(0.0001)
Property
Crime
(8)
Note 1: Results from OLS regressions. Standard errors, clustered by county, in parentheses: ∗∗∗ significant at 1%, ∗∗ significant at 5%
and ∗ significant at 10%. None of the regressions include county-year fixed effects. Regressions also include defendants’ age at offense
and its square term as in earlier tables. In all columns, unit of observation is individual criminal case.
Note 2: In Column (3), we measure the lengths of experience in private law practice and prosecution as their ratio to the total legal experience.
Observations
R-squared
Republican Judge
Female Judge
Hispanic Judge
Black Judge
Prosecution (Ratio)
Prosecution2
Prosecution
Private Law Practice (Ratio)
Private Law Practice2
Private Law Practice
Total Legal Experience2
Total Legal Experience
Judge’s age
(1)
Full Sample
(2)
(3)
Table 13: Case-level Regressions of Harshness on Judges’ Backgrounds
to differences across the geographic units served by the judges. Importantly, the results
suggest that judges tend to be consistent in their sentencing across the counties within their
jurisdictions. These findings have an important implication for the role of judicial districting
in the functioning of the justice system: allocating judges with distinct sentencing behavior
to different counties may generate a large variation in sentencing patterns across counties.
To be specific, consider two extreme hypothetical scenarios: (i) a large geographical area
is treated as one judicial district, which is served by a pool of several judges46 , and (ii) the
area is partitioned into several small districts, each of them served by a single judge. Scenario
(i) might be more desirable than (ii) in terms of fairness. In principle, two otherwise identical
convicts within the same court system should not be subject to different expected sentences
just because their cases are handled in different judicial districts. Moreover, it is possible
that, under a substantial variation in sentencing harshness across districts, criminals could
“sort” and commit more crimes in districts with relatively lenient judges. Another potential
benefit of large, multi-judge districts is that, by comparing several judges who are randomly
assigned to cases in the same district, it might be relatively easy for appellate courts to
identify particularly harsh or lenient judges. As far as appellate courts are more likely to
overturn decisions by “outlier” judges, who have established a pattern that puts them at
the boundary of the law, trial judges may have the incentive to moderate their sentencing
behavior. Thus, large judicial districts might lead to more consistency in sentencing even
across judges within the same district.
To evaluate the extent to which enlarging districts of Texas district courts could reduce the
cross-county heterogeneity in sentencing harshness, we simulate the following redistricting
intervention: for each judicial area in which the courts have overlapping patterns E and F in
46 Large,
multi-court judicial districts are common in many states. This is the case of judicial areas with
overlapping pattern C in Texas (see Table 1). Another example are the Superior Courts in North Carolina,
which partitions the 100 counties of the state into eight different divisions. Judges are required to rotate among
the many counties within their divisions on a regular basis so that, over time, each county is served by all judges
in the division.
42
Table 147 , we expand the jurisdiction of every court to comprise the whole area. We focus on
areas with overlapping patterns E and F because, for these areas, it is possible to separately
identify court (judge)-specific and county-specific fixed effects.48 For example, consider
the area of pattern F composed of courts 76, 276 and 115. Court 76 serves the counties
of Camp, Morris and Titus. Court 276 serves Camp, Morris, Titus and Marion. Court 115
serves Marion and Upshur. By taking court 76 and the county of Camp as a reference, we
can estimate fixed effects for courts 276 and 115 as well as for the counties of Morris, Titus,
Marion and Upshur.49
More generally, we consider the following specification:
Harshnessijt = α + βxi jt + θhic + γwi + ηkc + δzt + εi jt ,
(11)
where xi jt is vector of case characteristics, hic is a judicial area50 fixed effect, wi is a judge
fixed effect, kc is a county fixed effect, zt is a year fixed effect, and εi jt captures idiosyncratic,
unobservable characteristics of the case. It is important to note that γ captures court fixed
effects relative to other courts within the same judicial area. Similarly, η captures county
fixed effects relative to other counties within the same judicial area. The differences across
judicial areas are captured by θ, and our analysis cannot distinguish whether such differences
are mostly due to judge-specific or county-specific factors.
Having obtained estimates γ̂ for the court fixed effects in the specification above, let us
focus on a single judicial area h. For each county c in h, let n be the number of courts serving
h and define ∆c ≡ ( fc,1 , . . . , fc,n ), where fc,i is the empirical frequency of cases resolved in
47 Overlapping
patterns E and F have multiple counties and multiple courts that overlap imperfectly with
each other.
48 Because of judge turnover, ideally we would like to estimate judge-specific fixed effects rather than districtspecific ones. The option of estimating the latter is due to sample size limitations.
49 Notice that we can also separately identify district-specific and county-specific fixed effects in areas with
overlapping pattern C. But, since the courts in these areas already have identical geographical jurisdiction, our
counterfactual policy intervention in them would be innocuous by definition.
50 As in Table 1, areas are the smallest units that form a partition of the entire state.
43
court i among all cases prosecuted in county c. We then compute
n
Ψc = ∑ fc,i γˆi ,
(12)
i=1
where γˆi is the estimated fixed effect of court i relative to other courts within judicial area
h. The quantity Ψc is an estimate of the mean relative court fixed effect in county c, with
weights based on the distribution of courts within the county. If all courts in area h had the
same boundaries and cases were randomly assigned across courts, Ψc would be exactly the
same across all counties within h. Different boundaries of courts, together with heterogeneity
in court fixed effects, generate variation in Ψc . Therefore, this measure offers a way of evaluating the extent to which cross-county disparities in sentencing harshness within a judicial
area h could be reduced by extending the boundary of each court in area h to comprise the
whole area. To assess the extent to which redistricting would affect sentencing dispersion,
we can thus compare Ψc across counties within the same judicial area. With this goal, we
estimate equation (11) and compute Ψc for all counties in each judicial area with overlapping
pattern E or F.
Table 14 reports the mean absolute deviation of Ψc within each area with overlapping pattern E or F. In computing the mean absolute deviation, we weight Ψc by the proportions of
cases resolved in county c. For each judicial area h, this statistic can be interpreted as measuring the variation in sentencing harshness across counties in h that would be eliminated by
expanding the geographical jurisdiction of the courts. In two of the areas, the mean absolute
deviation is above 0.05 (bold numbers in the table), which is comparable in magnitude to the
effect of the defendant having one violent crime conviction. In four other areas, the mean
absolute deviation is still non-trivial – ranging from 0.0114 to 0.0445. For the remaining
13 areas, the measure is smaller, indicating that the heterogeneity in sentencing patterns due
to differences in court fixed effects is trivial. Thus, for about one third of the areas exam-
44
Table 14: Judicial Redistricting: Counterfactual Results
Area
Pattern
Counties
Mean Absolutea
Deviation of Ψc
q E Var W̃h − Var (Wc ) a
E
Willacy and Cameron
.0231
.0354
E
Bell and Lampasas
.0015
.0026
E
Johnson and Somervel
.0002
.0005
E
Chambers and Liberty
.0026
.0026
E
Hutchinson, Hansford and Ochiltree
.0001
.0001
E
Kleberg, Kenedy and Nueces
.0001
.0002
E
Callahan, Coleman and Taylor
.0068
.0093
E
Duval, Jim Hogg and Starr
.0011
.0011
E
Victoria, Calhoun, De Witt,
Goliad, Jackson and Refugio
.0037
.0037
E
Gray, Hemphill, Lipscomb,
Roberts and Wheeler
.0102
.0107
E
Bandera, Gillespie, Kendall, Kerr Kimble,
McCulloch, Mason and Menard
.0118
.0143
F
Camp, Morris, Titus,
Marion and Upshur
.0098
.0102
F
Colorado, Guadalupe, Lavaca,
Gonzales and Hays
.0114
.0121
F
Waller, Fayette, Austin and Grimes
.0022
.0025
F
Jasper, Newton, Sabine, San Augustine,
Tyler, Shelby and Panola
.0445
.0485
F
Potter, Randall and Armstrong
.0009
.0010
F
Coke, Irion, Sterling, Tom Green,
Schleicher, Concho and Runnels
.0033
.0048
F
Crockett, Pecos, Reagan, Sutton, Upton,
Val Verde, Kinney, Edwards and Terrel
.0727
.0735
F
Bowie, Lamar and Red River
.0728
a For
.0761
every judicial area h, both the mean absolute deviation of Ψc and the average of Var W̃h − Var (Wc ) are weighted by
the proportion of cases resolved in each county of h.
45
ined, extending the boundaries of the courts to the whole area would be effective in reducing
disparities in sentencing harshness across counties.
One potential concern in expanding the boundaries of the courts is that, by increasing the
number of judges serving each county, it could increase the within-county variation in sentencing harshness. As argued above, large districts could lead particularly harsh or lenient
judges to moderate their sentencing behavior to avoid being classified as outliers. Ignoring
this potential benefit, we can evaluate the degree to which extending the boundaries of courts
to the whole area would increase within-county variation in sentencing harshness. Specifi
cally, we define ∆˜ h ≡ f˜h,1 , . . . , f˜h,n , where f˜h,i is the relative frequency of cases resolved
in court i among all cases prosecuted in judicial area h. That is, f˜h,i is the probability that
a case in any county within area h would be assigned to court i in the scenario in which all
courts in h have jurisdiction over the whole area. Let W̃h denote the court fixed effect when
courts are distributed according to ∆˜ h in all counties within h. Similarly, for any county c,
let Wc denote the court fixed effect when courts have distribution ∆c in county c, defined on
page 44. We can then compute Var W̃h − Var (Wc ) to assess the impact of redistricting on
the within-county variance in sentencing harshness.51
The square-root of the average Var W̃h − Var (Wc ) across the counties within each judicial area with overlapping pattern E or F is reported in Table 14. The averages are weighted
by the proportions of cases resolved in each county. We take the square root in order to
convert the difference in the variances to the same scale as the mean absolute deviation of
Ψc and facilitate the comparison of these two statistics. The results show that, for all areas in which extending the boundaries of the courts would substantially reduce cross-county
heterogeneity in sentencing, the increase in within-county variation is also significant. Indeed, for all areas, the mean absolute deviation of Ψc has the same order of magnitude as the
square-root of the average change in sentencing variance due to redistricting. Therefore, in
51 Var (W )
c
is computed directly by the formula ∑ni=1 δc,i (γˆi − Ψc )2 . We calculate Var W̃h analogously.
46
evaluating the desirability of judicial redistricting, it is important to balance the benefits of
lower cross-county variation in sentencing harshness with the costs of higher within-county
variation in the same variable. The analysis in this section serves as a first step towards a
better understanding of this trade-off.
5
Conclusion
This paper studies the influence of judges’ race, ethnicity, and party affiliation on criminal
sentencing decisions. Our key results show precisely estimated null effects, conditional on
geographic factors. Even without conditioning on geographic factors, we find no systematic
evidence on the influence of judges’ race, ethnicity, and party affiliation on sentencing.
The difference between our results and previous studies on the influence of race and party
affiliation in other settings suggests that the influence may critically depend on the nature
of decision-making. Quick decisions (e.g., by sports referees), decisions by non-experts
(e.g., jurors in criminal trials), or decisions by policy-makers (e.g., U.S. Congressmen) may
be significantly influenced by race or political orientation. In contrast, decisions by those
who perform relatively bureaucratic functions that require significant expertise and are also
compared to a large number of peers may not be influenced much by factors other than their
professional knowledge and skills.
Despite the null effect of judges’ racial, ethnic, and political backgrounds, we find substantial variation in judges’ sentencing harshness. Our analyses also show a remarkable
degree of consistency in individual judges’ sentencing behavior across counties, and the possibility that cross-county disparities can be significantly mitigated in some areas by enlarging
boundaries of the districts. Further research that examines the influence of other factors (e.g,
competitiveness of the election of judges or campaign contributions by trial lawyers) will
help to enhance our understanding of how to improve fairness in applications of law.
47
References
Abrams, David, Marianne Bertrand, and Sendhil Mullainathan, “Do Judges Vary in
Their Treatment of Race?,” Journal of Legal Studies, June 2012, 41 (2), 347–383.
Antonovics, Kate and Brian Knight, “A New Look at Racial Profiling: Evidence from the
Boson Police Department,” The Review of Economics and Statistics, January 2009, 91 (1),
163–177.
Anwar, Shamena, Patrick Bayer, and Randi Hjalmarsson, “The Impact of Jury Race in
Criminal Trials,” Quarterly Journal of Economics, 2012, 127 (2), 1017–1055.
Ashenfelter, Orley, Theodore Eisenberg, and Stewart J. Schwab, “Politics and the Judiciary: The Influence of Judicial Background on Case Outcomes,” Journal of Legal Studies,
6 1995, 24 (2), 257–281.
Bar, Talia and Asaf Zussman, “Partisan Grading,” American Economic Journal: Applied
Economics, 2012, 4 (1), 30–48.
Becker, Gary S., The Economics of Discrimination, 2nd ed., University of Chicago Press,
1971.
Bertrand, Marianne and Sendhil Mullainathan, “Are Emily and Greg More Employable
than Lakisha and Jamal? A field Experiment on Labor Market Discrimination,” American
Economic Review, 2004, 94 (4), 991–1013.
Besley, Timothy and Anne Case, “Does Electoral Accountability Affect Economic Policy
Outcomes? Evidence from Gubernatorial Term Limits,” Quarterly Journal of Economics,
1995, 110, 769–798.
Boylan, Richard, “The Effect of Punishment Severity on Plea Bargaining,” Journal of Law
and Economics, 2012, 55 (3), 565–591.
48
Carson, E. Ann and Daniela Golinelli, “Prisoners in 2012 – Trends in Admissions and Releases, 1991–2012,” Bulletin NCJ 243920, U.S. Department of Justice, Bureau of Justice
Statistics, Washington, DC: U.S. Department of Justice December 2013.
Chetty, Raj, John Friedman, and Jonah Rockoff, “Measuring the Impact of Teachers I:
Evaluating Bias in Teacher Value-Added Estimates,” American Economic Review, 2005,
104 (9), 2593–2632.
Chew, Pat K. and Robert E. Kelley, “Myth of the Color-Blind Judge: An Empirical Analysis of Racial Harassment Cases,” Washington University Law Review, 2008, 86 (1), 1117–
1166.
Combs, John Gruhl Susan Welch Michael, “Black Elite Decision Making: The Case of
Trial Judges,” American Journal of Political Science, 1988, 32 (1), 126–136.
Cox, Adam B. and Thomas J. Miles, “Judging the Voting Rights Act,” Columbia Law
Review, 2008, 108 (1), 1–54.
Daughety, Andrew F. and Jennifer F. Reinganum, “Settlement,” in Chris W. Sanchirico,
ed., Encyclopedia of Law and Economics, second ed., Vol. 8 - Procedural Law and Economics, Cheltenham, UK: Edward Elgar Publishing Co, 2012.
Ferreira, Fernando and Joseph Gyourko, “Do Political Parties Matter? Evidence from
U.S. Cities,” Quarterly Journal of Economics, 2009, 124 (1), 399–422.
George, Tracey E., “Court Fixing,” Arizona Law Review, 2001, 43 (1), 9–62.
Gordon, Sanford C. and Gregory A. Huber, “The Effect of Electoral Competitiveness on
Incumbent Behavior,” Quarterly Journal of Political Science, 2007, 2 (2), 107–138.
49
Huber, Gregory A. and Sanford C. Gordon, “Accountability and Coercion: Is Justice
Blind when it Runs for Office?,” American Journal of Political Science, 2004, 48 (2),
247–263.
Kane, Thomas J. and Douglas O. Staiger, “Estimating Teacher Impacts on Student
Achievement: An Experimental Evaluation,” Technical Report, National Bureau of Economic Research 2008.
Knowles, John, Nicola Persico, and Petra Todd, “Racial Bias in Motor Vehicle Searches:
Theory and Evidence,” Journal of Political Economy, 2001, 109 (1), 203–229.
LaCasse, Chantale and A. Abigail Payne, “Federal Sentencing Guidelines and Mandatory
Minimum Sentences: Do Defendants Bargain in the Shadow of the Judge?,” Journal of
Law and Economics, 1999, 42 (S1), 245–270.
Lee, David S., Enrico Moretti, and Matthew J. Butler, “Do Voters Affect or Elect Policies? Evidence from the U.S. House,” Quarterly Journal of Economics, August 2004,
119, 807–859.
Levitt, Steven D., “The Effect of Prison Population Size on Crime Rates: Evidence from
Prison Overcrowding Litigation,” Quarterly Journal of Economics, May 1996, 111 (2),
319–351.
, “Understanding Why Crime Fell in the 1990s: Four Factors that Explain the Decline and
Six that Do Not,” Journal of Economic Perspectives, Winter 2004, 18 (1), 163–190.
Lim, Claire S.H., “Preferences and Incentives of Appointed and Elected Public Officials:
Evidence from State Trial Court Judges,” American Economic Review, June 2013, 103 (4),
1360–1397.
50
and James Snyder, “Elections and the Quality of Public Officials: Evidence from U.S.
State Courts,” 2014. working paper.
,
, and David Strömberg, “The Judge, the Politician, and the Press: Newspaper Cov-
erage and Criminal Sentencing Across Selection Systems,” American Economic Journal:
Applied Economics, forthcoming.
McCaffrey, Daniel F, JR Lockwood, Daniel Koretz, Thomas A Louis, and Laura Hamilton, “Journal of E ducational an d Behavioral,” Journal of Educational and Behavioral
Statistics, 2004, 29 (1), 67–101.
Poole, Keith and Howard Rosenthal, “The Polarization of American Politics,” Journal of
Politics, 1984, 46, 102–131.
Price, Joseph and Justin Wolfers, “Racial Discrimination Among NBA Referees,” Quarterly Journal of Economics, 2010, 125 (4), 1859–1887.
Schanzenbach, Max, “Racial and Sex Disparities in Prison Sentences: The Effect of
District-Level Judicial Demographics,” Journal of Legal Studies, 2005, 34 (1), 57–92.
Segal, Jeffrey A. and Albert D. Cover, “Ideological Values and the Votes of U.S. Supreme
Court Justices,” The American Political Science Review, 1989, 83 (2), 557–565.
Silveira, Bernardo S., “Bargaining with Asymmetric Information: An Empirical Study of
Plea Negotiations,” 2012. Mimeo, New York University.
Snyder, James and Timothy Groseclose, “Estimating Party Influence in Congressional
Roll-Call Voting,” American Journal of Political Science, 2000, 44, 187–205.
Uhlman, Thomas M., “Black Elite Decision Making: The Case of Trial Judges,” American
Journal of Political Science, 1978, 22 (4), 884–895.
51
Waldfogel, Joel, “The Selection Hypothesis and the Relationship between Trial and Plaintiff
Victory,” Journal of Political Economy, 1995, 103 (2), 229–260.
Yang, Crystal S., “Free at Last? Judicial Discretion and Racial Disparities in Federal Sentencing,” 2013. Mimeo, Harvard University.
52