The Racial Politics of Mass Incarceration

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Electronic copy available at: https://ssrn.com/abstract=3025670
The Racial Politics of Mass Incarceration
Clegg, John∗† Usmani, Adaner‡
February 2017
Abstract
Dominant accounts of America’s punitive turn assume that black elected
officials and their constituents resisted higher levels of imprisonment and polic-
ing. We gather new data and find little support for this view. Panel regressions
and an analysis of federally-mandated redistricting suggest that black elected
officials had a punitive impact on imprisonment and policing. We corroborate
this with public opinion and legislative data. Pooling 300,000 respondents to
polls between 1955 and 2014, we find that blacks became substantially more
punitive over this period, and were consistently more fearful of crime than
whites. The punitive impact of black elected officials at the state and federal
level was concentrated at the height of public punitiveness. In short, the racial
politics of punishment are more complex than the conventional view allows.
We find evidence that black elected officials and the black public were more
likely than whites to support non-punitive policies, but conclude that they
were constrained by the context in which they sought remedies from crime.
Keywords: Crime, Criminal justice, Public Opinion, Race, Mass Incarceration.
Word Count: 9,321 in text (1,830 in footnotes).
∗The authors are listed here in alphabetical order only. Each contributed equally to the research
and writing involved.
†Ph.d. candidate, NYU Sociology, 295 Lafayette St., New York, NY, 10012, USA.
jjclegg@nyu.edu. Tel: (212) 998-8340, Fax: (212) 995-4140.
‡Ph.d. candidate, NYU Sociology, 295 Lafayette St., New York, NY, 10012, USA.
au324@nyu.edu. Tel: (212) 998-8340, Fax: (212) 995-4140.

Electronic copy available at: https://ssrn.com/abstract=3025670
The Racial Politics of Mass Incarceration
1 Introduction
The modern American way of doing criminal justice is both punitive and dispropor-
tionate. Between 1970 and the present, the proportion of adults in prison or jail
exploded, and now exceeds that found in any comparable society. During this period
racial disparities in incarceration remained very high, with African Americans five or
six times more likely to be jailed than whites (Muller 2012). The combined inten-
sity and disparity of punishment has had a devastating impact on African American
communities, especially those marked by concentrated poverty (Weaver, Hacker, and
Wildeman 2014; Lee, Porter, and Comfort 2014).
While there is no consensus on the origins of this punitive turn, its disproportion-
ate impact has led most scholars to emphasize white protagonists and racial motives.
For the scholarly mainstream, mass incarceration was the work of a revanchist, white,
and mostly Southern elite determined to roll back the tide of black advancement af-
ter the Civil Rights movement (Beckett 2000; Weaver 2007; Tonry 2012). In the
well-known words of Alexander (2012), mass incarceration amounts to ‘The New Jim
Crow’.
This emphasis on white protagonists has encouraged assumptions about the views
and actions of African Americans and their representatives. Specifically, blacks are
generally reduced to the status of unwilling or unwitting victims. By extension, many
scholars believe that black enfranchisement, where and when it existed, should have
attenuated or perhaps even reversed punitive trends over this period (Beckett 2000,
26; Behrens, Uggen, and Manza 2003, 596; Yates and Fording 2005, 1119).
Recent research, however, has questioned this conventional view. Several scholars
1

have demonstrated that black political leaders in the 1970s and 1980s often supported
the same “get tough” approach advocated by their white counterparts. Michael Javen
Fortner (2013, 2015a) has shown that many civic leaders in Harlem were in favor of
the 1973 Rockefeller drug laws, considered by many the model for the War on Drugs.
Similarly James Forman Jr (2012, forthcoming) has documented that a majority-black
legislature in D.C. passed tough-on-crime policies in the 1980s, leading to exception-
ally high levels of incarceration in that city. Both authors present their findings as
a challenge to the conventional view, arguing that it “oversimplifies the origins of
mass incarceration” (Forman Jr 2012, 103) and fails to “take black agency seriously”
(Fortner 2015a, 14).1In view of this evidence, Vanessa Barker (2009, 179) has con-
cluded that “[b]lack incorporation and political participation have made them both
accomplices and victims of penal reform.”
While these authors marshal compelling evidence to make their case, there are rea-
sons to be sceptical of this revisionist account. First, this account is based exclusively
on case studies. We do not know how well their findings generalize to other times and
places. Second, the conventional view can draw on supporting evidence that black
public opinion is less punitive than white (Bobo and Johnson 2004), and that black
political and civil rights organizations have played a leading role in recent decarcera-
tion efforts (Nadelman 2010). Finally, these studies do not settle the question of why
black leaders supported punitive policies, if and when they did. For instance, while
Fortner emphasizes that black constituents are particularly vulnerable to crime, and
are thus amenable to punitive arguments, Forman tends to lay responsibility on black
elites.
We take this controversy as an invitation to consider the relevant evidence in
1. In a similar vein Donna Murch (2015, 173) has argued that “[m]any black politicians and other
prominent leaders supported drastic carceral policies in hopes of staunching the crack crisis facing
black communities across the country.”
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greater detail. Our purpose is not to explain the origins of mass incarceration, but to
scrutinize the image of black politics that the conventional account projects. What
did black politicians accomplish during the era of the punitive turn? What did the
black public demand? And how were these related?
1.1 Existing Literature
Other scholarship on crime and incarceration can be brought to bear on this debate,
but our view is that direct evidence is wanting. For instance, a well-established soci-
ological literature has argued that the racialized fears of a white majority drive tem-
poral and cross-sectional variation in American regimes of social control (Jacobs and
Jackson 2010). These studies tend to find that larger black populations are correlated
with higher state-level incarceration rates (Beckett and Western 2001; Greenberg and
West 2001; Jacobs and Carmichael 2001; Smith 2008; Campbell, Vogel, and Williams
2015) and larger city-level police forces (Sever 2003; Sharp 2006; Stults and Baumer
2007).2This evidence has obvious affinities to the conventional account of the puni-
tive turn, but the evidence these authors present does not answer the questions posed
above. First, the punitive turn unfolded over time in a period when black population
shares at the state level changed very little (see Figure 5). They are thus unlikely to
explain the sharp rise in prisons and police per capita. Second, demographic measures
invite conceptual confusion, since the black population share is a plausible proxy for
both white anxiety and black empowerment.
Some scholars have estimated the impact of black politicians on outcomes broadly
related to the punitive turn, but most of this work focuses on mayors and judges,
and finds ambivalent or clashing results (Hopkins and McCabe 2012; Uhlman 1978;
2. However, earlier studies find no or negative effects of percent black on incarceration
(Michalowski and Pearson 1990; Myers 1990; Arvanites and Asher 1998), and Greenberg, Kessler,
and Loftin (1985) find no effect on police force size in the 1970s.
3

Spohn 1990; Steffensmeier and Britt 2001). To our knowledge, no study has examined
black federal legislators, despite the Congressional Black Caucus’s support for the
major crime bills of the mass incarceration era (Fortner 2015b). There has also been
little work on the impact of black state legislators.3These lacunae are surprising,
considering the well-known impact of state-level punitive legislation—on everything
from mandatory minimums and structured sentencing to prison construction and
parole eligibility
Similarly, there is great room for improvement upon existing work on the views of
black constituents. We actually know very little about the contours of black public
opinion over the period of the punitive turn. Existing work examines select questions
and focuses on cross-sectional variation in particular periods (Bobo et al. 2004; Meares
1997; Beckett 2000). No one has yet used polling data to build a representative and
long-run measure of the kind that Enns (2014, 2016) has proposed for the aggregate
public.
1.2 Our Approach
To these ends we marshal new evidence. First, we estimate the impact of black rep-
resentation on levels of imprisonment and policing using an original panel dataset
spanning 1972 to 2008. We find no evidence that black political representation atten-
uated punitive outcomes, and some evidence for the contrary revisionist hypothesis.
Second, we exploit an instance of federally-mandated majority-minority redistricting
3. Yates et al. (2005) estimate the effect of black officials on state prison populations, but they
focus on racial disparities rather than total incarceration rates. They find that black politicians
reduce the black incarceration rate but leave the white incarceration rate unaffected. We failed to
replicate these results in our models. The discrepancy could be a function of model specification
(they model most variables in first differences and do not include lags of the dependent variable),
sample truncation (their data runs only from 1977 to 1995) or their measure of black representation
(they include all local and city-level elected officials whereas we analyze only state and federal
representatives).
4

in the early 1990s, in mainly Southern states. Here, we find even stronger evidence
that black enfranchisement increased rather than attenuated punitive trends.
These results are surprising, and not robust to examining trends in corrections
spending, so we dig a little deeper. We gather original data on black and white
public opinion from dozens of nationally-representative opinion polls administered to
over 300,000 respondents. These estimates confirm that blacks are less punitive than
whites, but they also show that absolute levels of punitiveness in the black community
were high, and that they were often more fearful of crime. We show that the positive
effect of black politicians on carceral outcomes is concentrated in periods of high
punitiveness, crime anxiety, and mistrust; in the opposite context, we find some
evidence of a negative effect. Trends in partisanship and welfare disbursements around
redistricting suggest that post-redistricting punitiveness is unlikely to be driven by
revanchist whites. Last, to thicken our interpretation of the legislative dynamics
that panel analysis leaves obscure, we examine original data on voting patterns in
Congress, focusing on the passage of Clinton’s 1994 Crime Bill.
All considered, our evidence contravenes the conventional view. “White backlash”
does not adequately capture the racial politics of incarceration or policing. Neither
black elected officials nor the public they represented were implacably opposed to
punitive policies. Rather, during the heyday of incarceration and policing, they ex-
ercised their limited power and voice to support and even amplify punitive trends.
Our interpretation thus highlights black agency, but also the considerable con-
straints under which this agency was exercised (Miller 2010). As voting patterns
at the Federal level make clear, black leaders supported these punitive policies in
a political environment which foreclosed non-punitive strategies for handling crime
and criminals. As the public opinion data makes clear, these alternatives enjoyed
overwhelming support among the black public. Yet in a context of elevated concern
5

about crime and high punitiveness—when, in effect, black communities were demand-
ing that their representatives do something, anything, to reduce crime rates—these
other demands fell by the wayside, and black political influence was channeled towards
more prisons and more police.
2 Panel Regressions
Most research defines the punitive turn as the enormous increase in the rate of in-
carceration over the last several decades, but incarceration is only one dimension of
the decades-long inflation of the American criminal justice apparatus.4As Figure 2
shows, the number of police officers for every 100,000 people has increased dramat-
ically, as well. Given the high salience of intensive policing and police misconduct
in recent discussions of the American way of doing criminal justice, we consider this
dimension of the punitive turn throughout. These two measures—the incarceration
rate and the officer rate—are our main outcomes of interest. They have been studied
in past work, and they best capture the lay understanding of America’s punitive turn.
Our central explanatory variable is a straightforward measure of the political clout
of black politicians in a given state, defined as the proportion of state and federal
elected officials who are African-American. We add a set of mostly standard controls
to all models. We include a measure of the rate of violent crime, which plausibly affects
the incarceration rate directly and both punitive outcomes indirectly (by inducing a
response from politicians, prosecutors and the public). We also include a measure
of partisanship: this is a variable denoting which party has true control of the state
4. We define the incarceration rate as the number of prisoners under a state’s jurisdiction for every
100,000 people in the state’s resident population. Our measure thus excludes those held in local jails
or federal prisons. Others sometimes refer to this as the ‘imprisonment’ rather than incarceration
rate.
6

legislature.5We account for the possibility that the punitive turn reflects the general
modernization of the state by controlling for GDP per capita.6To take account of
the revenue space available to state governments, we control for the amount of tax
collected per capita. To control for the possibility that income inequality has driven
some of the punitive turn, we include the state-level Gini coefficient. Finally, since
Enns (2016) has argued that the punitive turn in policy was driven in part by a
corollary turn in public opinion, we include a measure of punitiveness of the total
population in a given state in a given year.7
We model the relationship between our independent and dependent variables at
the state level. Data availability limits the sample, which is consistent across the
specifications we trial, to a slightly unbalanced panel of 49 states, most observed in
all years between 1972 and 2010.8Our focus here is to establish whether recent data
reveal any broad associations between black representation and the incarceration or
officer rates. Specifically, we estimate regressions of the form:
DVst =
m
X
j=1
αjDVst−j+
n
X
j=1
γnBPst−n+
p
X
j=1
x0
st−pβp+δs+µt+st (1)
5. The variable is coded 1 if Democrats exercise control, 0 if neither, and −1 if Republicans. Past
research has used the percentage of seats in a state legislature controlled by a given party and/or
the affiliation of the governor, but we consider this composite measure a more informative gauge of
partisanship. See Klarner (2003).
6. We also include the logarithmic growth rate of this variable to account for the ebb and flow of
a state’s economic fortunes. It is convention to include measures of the unemployment and poverty
rate, but we omit these in order to to avoid truncating our sample. Intercensal estimates of the state-
level unemployment rate are unavailable before 1976, and of the poverty rate before 1989. Because
our state-level panel regressions consider only over-time variation in these variables (as discussed
below) this is unlikely to be a very costly decision. We expect within-state movement in poverty
and unemployment to be highly correlated with the growth rate of GDP per capita. All results of
interest are robust to truncating the sample by including these variables. We also include them in
our difference-in-difference analyses in the next section.
7. Sections 4.1 and D of the Online Appendix give details. Note that in using Enns’ measure of
punitiveness, we collapse the three different dimensions that we later opt to distinguish. This has
two advantages: it avoids truncating the sample (questions about ‘crime anxiety’ are not present in
our dataset before 1975), and it most closely matches what Enns himself did.
8. Nebraska has a non-partisan legislature, so it is missing from the entire sample.
7

where DVst is the value of either of these dependent variables in state sat time
t, and each of the αjDVst−jterms stands for a lag of this value. The independent
variable of interest is BPst−n, which represents the share of state and federal legislators
that are African-American in state sat time t−n, and x0
st−pis a row vector containing
all the controls. In the discussion that follows, we focus on the joint impact of the
γn’s on the dependent variable in question. We allowed dynamic structure to vary
across models and variables, such that m,nand prepresent the number of lags that
maximized model fit.9
Otherwise, δsdenotes a fixed-effect for state sat time t, the µt’s represent a
set of year fixed effects, and it denotes the error in state sand time t, adjusted
for clustering at the state level.10 We include state-fixed effects to account for the
likely existence of time-invariant confounders which we cannot measure. Of course,
as we discuss in the next section, the inclusion of fixed-effects does not resolve the
difficulties of causal inference. Two variables can be associated over time by virtue of
their common association with a third, time-varying but omitted variable. Moreover,
they can be associated when the causal effect runs in the reverse direction. We lag
all independent variables by one year, but this is only a weak defense against this
second possibility.
Finally, we examined all series for unit roots using tests appropriate for balanced
panel data. As Section 7 of the Online Appendix illustrates, results are ambiguous.
9. De Boef and Keele (2008) notes that researchers often unthinkingly restrict their models by
either excluding lagged dependent variables or including only a single lag of independent variables.
We follow their recommendations and let the data decide. Our preferred measure of model fit is the
Bayesian Information Criterion (BIC). Thus, when we report choosing a model which maximizes
model fit, we mean that we chose the specification that minimized the BIC.
10. The inclusion of fixed-effects in models with lagged dependent variables raises the spectre of
Nickell’s bias since, by construction, the lagged dependent variable and the effective error term are
correlated. However, as Nickell (1981) shows, the resulting bias fades as the length of the panel
increases, and subsequent work has shown that it is not a grave concern when Tis larger than 30
(Judson and Owen 1999).
8

All series are cleared by at least one test; all series are also implicated by at least
one test. The standard remedy for nonstationarity is to first difference any culprit
series. This is costly, since it discards all information contained in that variable’s
original level. In many cases, theoretical arguments that apply to a variable in levels
may not apply to that same variable in differences. For this reason, and for brevity’s
sake, in the body of this paper we limit our discussion to the specification in which
all variables are left in their levels. Where this decision affects our conclusions, we
discuss it in the main body of the paper.
As specified, Equation 1 allows us to estimate both the immediate and the cu-
mulative ‘impact’ of changes in any of the independent variables. In effect, including
a lag of the dependent variable means that a change in any independent variable is
transmitted for an infinite number of subsequent periods (De Boef et al. 2008). In the
discussion below we focus on the long-run impact of a given change in our indepen-
dent variables—specifically, we focus on the long-run consequences of a reasonably
large increase in black political representation.11
2.1 Results
Table 2 presents estimates from the specifications that maximized model fit. In
both cases, the estimated long-run impact of black politicians is positive, and in
the case of the officer rate, statistically significant at conventional levels. This is
the most noteworthy result. According to this model, an influx of black politicians
into office is associated with the addition of about 6 police officers for every 100,000
11. This estimated long-run impact is the ratio of two or more estimates, which means that it
is itself an estimated quantity. Calculating this uncertainty analytically is complicated (De Boef
et al. 2008), so we proceeded by simulation. We simulated 5,000 draws from the estimated variance-
covariance matrix of the model in question (adjusted for clustering), and computed a distribution for
the long-run multiplier. The standard errors and p-values that we report summarize this distribution.
Appendix B explains this procedure in more detail.
9

people (plus or minus 5.5).12 Our estimate of the impact of black representation on
incarceration is also positive, suggesting that a similarly-sized influx of black elected
officials is associated with the subsequent addition of about 14 prisoners for every
100,000 people. The estimate of this latter effect is very imprecise, however; the
95% confidence interval ranges from -20 to +48. In Section 4.1 we offer a fuller
interpretation of this ambiguous result.
Otherwise, we find that the only significant determinants of movements in the
incarceration and officer rate are the antecedent rate of violent crime (positive), tax
revenues (positive), and income inequality (negative). Neither partisanship nor the
share of the population that is black has any clear consequences. Nor does the measure
of punitiveness, which we discuss again in Section 4.1.
3 The Great Shock Forward
While these results are striking, they invite further scrutiny. The coincidence of
black elected officials and the subsequent rise in the officer rate may be explained
by the reverse causal sequence, or by an unobserved third variable. In many cases,
researchers are forced to settle for correlations drawn from observational evidence.
But in this case, the history of federal intervention into the state-level electoral process
has produced spurts of black enfranchisement that can be considered exogenous to the
covariates in our model. Our case selection follows Ueda (2005), who exploits these
interventions to estimate the impact of minority representation on school funding.
12. To give some impression of effect size, we multiplied all estimates reported in Table 2 by their
respective average within-state standard deviations. The average within-state standard deviation of
our measure is 2.15.
10

3.1 1990s Redistricting
The Voting Rights Act of 1965 empowered the Federal Government to intervene in
state elections to ensure minority representation. In 1982 Congress amended the act
to explicitly prohibit voting schemes that result in minority vote dilution. Subsequent
Supreme Court decisions simplified the legal criteria for overturning discriminatory
electoral schemes. As a result, when it came time to redraw electoral districts in the
aftermath of the 1990 census, states were under pressure to maximize the number
of districts in which minorities would form a majority of voters. By the elections
of 1992, a total of 83 new majority-black electoral districts had been created, a 25
percent increase from 1990 (Grofman 2003, 18-19).13 The resulting influx of black
politicians into state and federal legislatures has been characterized as “the single
largest increase in black representatives in U.S. history”(Kim 2002, 65).
For inference, two facts about these changes bear emphasizing. First, while black
mobilization and advancement certainly induced federal intervention into state elec-
tions, the influx of black politicians cannot be attributed to earlier state-level legal
and political decisions. The sharp increase in black elected officials immediately after
1990 was the result of redistricting following the 1990 census, the timing of which
was exogenous to black protest or progress (Grofman 2003, 16). Second, redistricting
affected states covered by the Section 5 provisions of the Voting Rights Act much
more dramatically than others. Figure 6 plots the average level of black electoral
representation in the states in which these new black-majority electoral districts were
concentrated. In the unaffected states, the percentage of black legislators increases
slightly, but at a rate that is basically continuous with the trends prior to 1990. By
contrast, there is a sharp discontinuity in the affected states between 1990 and 1995,
13. These figures combine state senate, state house, and congressional districts.
11

reflecting the post-90s influx.
3.2 Estimation
To estimate the impact of this influx, we exploit the fact that redistricting affected
only a subset of all states and for a confined period of time.14 Specifically, we compare
trends before and after redistricting in states that were subject to it, to trends before
and after in states that were not—an approach commonly known as difference-in-
differences. This controls for unobserved differences between the two groups, and for
trends over time that are common to both.15
More formally, we estimate models where
DVst = (RDs×P Dt)θ+x0
st−1β+δs+µt+st (2)
Again, DVst represents either the incarceration or officer rate in year tin state s.
RD is a dummy variable denoting membership in the set of redistricted states, and
P D similarly indicates years during which we expect redistricting to have an effect
on outcomes.16 θthus estimates the impact of redistricting on the dependent variable
14. “Treated” states in this analysis are: Alabama, Florida, Georgia, Louisiana, Mississippi, North
Carolina, South Carolina, Texas, Virginia and New York. These are the states which match the
following criteria: (1) they were bound by Section 5 of the Voting Rights Act to submit redistricting
plans for all or some of their counties to Dept. of Justice pre-approval, (2) they had a black
population of at least 10% in 1990, (3) the number of black majority districts increased between
1990 and 1992. Data on black majority districts come from Grofman (2003, 18-19).
15. Admittedly, redistricting was more pronounced in some states than in others. Our baseline
approach assumes that the ‘treatment effect’ of redistricting was equivalent in all states that we
count as affected, which is not ideal. In one specification reported in Table 3, we use the number of
new majority-minority districts created as a proxy for the intensity of treatment. Because these data
are only available for (almost all) redistricted states, the strategy rests on the generous assumptions
that there were zero new districts created in non-redistricted states, and that the number of new
districts created is a gauge of the magnitude of enfranchisement.
16. We assume that redistricting had its first impact on the percentage of black officials in the
legislature in the elections that were held at the end of 1990. Supporting this, Figure 6 shows a
discernible increase in black political representation in redistricted states beginning in 1991. Most
redistricting was probably completed by the 1992 elections, but the resulting influx of black politi-
12

of interest.
While the timing of redistricting was exogenous, America in the early 1990s was
far from an experimental setting. Other factors affecting punitive outcomes may
have covaried with redistricting. For instance, at the same time as majority-minority
redistricting produced an influx of black elected officials into redistricted states, Re-
publicans increased their seat share in redistricted states. This did not result in
veto-proof control of state legislatures in any of these states in the period in question,
but it diminished Democrat control by the end of this period. Similarly, the crack
epidemic hit redistricted states more severely than not-redistricted states, and violent
crime also increased more. Section 4 discusses the plausibility of other explanations
of these results in detail, but as a first-order defense our preferred models include
all controls we employed in the panel specification, as well as measures of the state-
specific intensity of the crack epidemic, the unemployment rate, and the poverty rate.
The sample is truncated relative to the panel specification: from the left due to the
sparsity of these additional data, and from the right due to the expectation that the
effects of redistricting are likely to fade after the early 1990’s.
3.3 Results
Table 3 reports estimates of θfrom different specifications, which show that redis-
tricting had a significant, positive effect on imprisonment and policing. Both the
incarceration rate and the level of policing per capita increased more in redistricted
than in not-redistricted states.17 Specifically, redistricting seems to account for an in-
cians seems to have lasted till 1995. Because we expect these officials to have had an effect on
the political process at a year’s remove, we define our post-redistricted outcomes as those observed
between 1992 (one year after the first increase of black politicians into office) and 1996 (one year
after this influx ends).
17. Note that the estimated impact of redistricting on the incarceration rate is only significant at
α= 0.10. In the simple comparison of means, this estimate is larger and significant at α= 0.01.
13

crease of roughly 47 prisoners (plus or minus 53) and 17 police officers (plus or minus
11) for every 100,000 people. These are sizeable effects, equivalent to a approximately
one-fifth of the increase in the incarceration rate and the officer rate over the entire
period.18
We report several specifications as a test of the robustness of these results.19 Model
(3) interacts treatment with a measure of treatment intensity.20 Model (4) reports
results from a specification in which suspect variables are first-differenced, given con-
cerns about unit roots. As Table 3 shows, estimates of the impact of redistricting on
policing are not substantively different from those obtained in our preferred specifi-
cation. The estimated impact of redistricting on the incarceration rate is slightly less
robust to these alternatives. All estimates remain positive, but θis not statistically
significant when a measure of intensity of redistricting is introduced, or when suspect
variables are first differenced.
4 Racial Threat or Black Agency?
Given conventional wisdom, these results are surprising. They suggest that, where
black elected officials had a discernible impact on punitive outcomes, they exacer-
bated rather than attenuated trends towards increased policing and imprisonment.
Moreover, the evidence considered thus far is not just correlational. The exogenous
This gives an impression of the relative trends.
18. Between 1981 and 1996, the average imprisonment rate in redistricted states increased by
about 267 prisoners per 100,000 people, and the average level of officers by about 87 for every
100,000 people.
19. The last two columns of Table 3 also show which of these results are robust to aggregation
and block-bootstrapping, which are two strategies recommended as a defense against the fact that
D-in-D data are often autocorrelated (Bertrand, Duflo, and Mullainathan 2004). Note that the
recommended corrections reduce the probability of Type I error, but at the cost of lower power.
20. We measure intensity by the number of new districts created after redistricting as a percentage
of electoral districts that existed pre-redistricting. The estimate shown in Table 3 reports the effect
of redistricting evaluated at the median intensity of redistricting.
14

influx of black elected officials into mainly Southern states in the early 1990’s seems
to have sparked a punitive turn. However, any analysis of how covariates and out-
comes move in tandem has the inescapable shortcoming of black-boxing the operative
mechanisms. In this case, this problem manifests itself in an obvious way. For at least
two reasons, one might doubt that black elected officials themselves did the legislative
work of turning policy in a punitive direction.
First, the influx of black politicians caused by redistricting was not overwhelming.
Between 1990 and 1995, black legislators as a percentage of all legislators increase
by an average of 6 percentage points in the redistricted states (or, an average of 11
new minority legislators in every state), compared to about 1% in the not-redistricted
states. Since they never amounted to a critical majority in state or federal legislatures,
could their influence really explain large increases in punitive outcomes? On the other
hand, in line with the racial threat perspective, it could be that the uptick in punitive
trends was an indirect response to the influx. In other words, perhaps dominant forces
in the state legislatures were antagonized and thus spurred to action by black political
empowerment.
The next section considers the evidence for and against the “racial threat” inter-
pretation of these results, but first we try to capture legislative dynamics by analyzing
a dependent variable that is closer to the legislative floor. Spelman (2009) argues that
spending outcomes have been neglected by the existing scholarship of the punitive
turn. After all, several determinants of the state-level incarceration rate are in the
hands of other actors (judges, prosecutors, and police), and only a small minority
of police hires are made by state agencies. In effect, in modeling the officer rate at
the state level, we assume that the intensity of policing reflects political and fiscal
priorities set at the state level.
15

Thus, we also analyzed the level of state spending on corrections.21 As gauges of
state-level punitiveness, of course, this measure has its own shortcomings, which is
why this was not our preferred strategy. Spending on corrections is only one way in
which we expect politicians to affect incarceration. Tables 2 and 3 also present the
results of substituting the corrections rate into the models described earlier. These
results provide reason for pause. In the panel regressions, the estimated impact of
black political representation on corrections spending is negative, and statistically
significant at α= 0.10. A within-state standard deviation change in the level of
black representation is associated with just under a 4% decline in state spending on
corrections (give or take 4 percentage points). The difference-in-differences analysis
yields muddier results. As shown in Table 3, the level of state spending on correc-
tions increased by more in redistricted states than in not-redistricted counterparts.
The estimated impact of redistricting is negative once controls are included, but the
estimates are imprecise. The only specification in which the estimated impact of
redistricting is statistically significant from zero is Model (3), which incorporates a
measure of treatment intensity. Here, redistricting of median intensity is estimated
to cause a bit more than a 12% decline in corrections spending (give or take 10%).
Given earlier results, these results are puzzling. How can black political repre-
sentation be positively associated with punitive outcomes, but negatively associated
with spending on corrections? To answer this question we turn to other kinds of
evidence to build a fuller interpretation of the racial politics of the punitive turn. In
Section 4.1, we examine levels of and trends in black and white public opinion on a
host of relevant questions. We do this in order to delimit plausible interpretations of
our earlier findings. If significant majorities of blacks expressed hostility to police and
21. Spelman (2009) analyzed capital outlays on corrections facilities. We model total spending,
instead, since data on capital spending are very sparse over the period we examine.
16

prisons this would cast doubt on the finding that their elected representatives exacer-
bated punitive outcomes, and provide support for the conventional wisdom reflected
in the fiscal results. In Section 4.2 we test whether white revanchism better explains
the coincidence of punitive outcomes and the BEO influx. Last, in Section 4.3, we
examine the voting patterns of black Representatives at the federal level in order to
gage the direct impact of black representation in one key arena for the production of
criminal justice policy.
4.1 A Punitive Public
In order to analyze black and white public opinion, we gathered information from a
number of nationally-representative surveys. In all, we examined 39 questions asked
between 1955 and 2014 to roughly 300,000 respondents (251,000 of whom were white,
and 34,000 black).22 Our approach largely follows Enns (2014, 2016), but with one
important amendment. Enns assumes that all questions illuminate a single latent
dimension of public opinion, which he labels punitiveness. To this point, this is the
measure we have employed in our panel analysis. Enns reasons that longitudinal and
cross-sectional variation in responses to these questions are comparable. Increased
distrust of the police, he reasons, should express the same shift in sentiment indicated
by an increase in support for the death penalty. Correspondingly, respondents more
likely to distrust the police should also be more likely to support the death penalty.
We relax this assumption in our own analysis in order to shed light on what Zimring
and Johnson (2006) identified as three distinct dimensions of public opinion bearing
on the punitive turn: punitiveness (questions about the death penalty, suspects’
rights, and the harshness of courts), crime anxiety (questions about how much should
22. For information on how frequently each question was asked, and during which years, see Table
6 in the Online Appendix.
17

be spent on fighting crime), and mistrust (questions about confidence in existing
criminal justice institutions). Disaggregating the data in this way helps clarify the
nature of the racial gap as well as trends over time, which vary depending on the
dimension under analysis.
Figure 7 presents estimates of the proportion of black and white respondents
giving punitive (or anxious or mistrustful) responses to each of the 39 questions in
our dataset, out of all of those who gave either punitive or non-punitive responses. The
y-axis is grouped by dimension, and ordered by the proportion of blacks answering
punitively. Points to the right of the dashed line indicate that more respondents
answered punitively than did not. Figure 8 displays the racial gap that corresponds.
The y-axis is again grouped by dimension, and then ordered by the magnitude of the
average difference between whites and blacks. Points to the right therefore indicate
that whites were more punitive, anxious or mistrustful than blacks, and points to the
left indicate the reverse.
In each dimension, the story is different. Whites tended to give much more puni-
tive answers than blacks. This is in line with the conventional view (Bobo et al. 2004),
but the magnitude and consistency of this gap is worth noting. In seventeen out of
the nineteen questions we examined, whites were more punitive. The raw proportions
do convey important information, alongside this gap, but it is not easy to discern pat-
terns. This is because these raw proportions mix two kinds of variation: some is due
to differences in when questions were asked, and some is due to the idiosyncrasies of
the questions themselves. Sorting one from the other is not straightforward within the
limits of our approach, but note one telling pattern. As shown in Figure 10, questions
which prime respondents to a choice between alternative policies are significantly less
likely to elicit punitive answers than questions which ask, in effect, for an up-or-down
vote on a particular policy (Cullen, Fisher, and Applegate 2000). On average, almost
18

65% of blacks favor non-punitive to punitive options when given a choice. Contrast
this to the roughly 75% of blacks giving clear-cut answers who expressed support for
Clinton’s crime bill, or the 90% who responded that courts should treat suspects more
harshly. Questions without obvious alternatives seem to gauge desperation as much
as punitiveness. They capture the fact that respondents prefer something be done to
nothing at all. The high proportion who answer not-punitively when presented with
alternatives bears emphasizing. We return to this point in our conclusion.
In the second dimension, racial differences were less stark. Both whites and blacks
were consistently very anxious about crime. Blacks were about 10% more likely to
say that they were worried or felt inadequately protected. The other five questions all
ask whether money should be spent on dealing with crime. In the three which only
refer to crime spending in the abstract, there is no significant racial gap. As Figure
7 shows, over 90% of those giving clear-cut answers say that it should. But in the
two that refer to specific institutions (the police and law enforcement), a gap does
appear, suggesting perhaps that these questions gauge mistrust alongside anxiety
about crime.
Blacks were also significantly more likely to express mistrust of criminal justice
institutions. These differences were particularly acute when respondents were asked
about the police. In each case, blacks expressed higher levels of mistrust. When asked
about the courts and/or the criminal justice system in the abstract, the pattern
was more mixed and differences generally slighter: in one case whites were more
mistrustful, and in two cases blacks were. Again, the racial gap should be interpreted
alongside the raw proportions: even though blacks were much more mistrustful of the
police, in some cases large majorities answered that they respected police.23
23. In other cases, a majority answered the opposite. Within the limits of our approach, we cannot
clarify whether this specific variation is due to sampling or wording differences, or due to the different
span covered by questions that are otherwise similar.
19

This approach illuminates the racial gap, but it ignores variation in punitiveness,
anxiety and mistrust by time and place. To estimate this variation, we proceed in
steps. First, for each question, we modeled the probability of a punitive, mistrustful
or anxious response as a function of gender, race, age group, education level, year, and
state (or region, where state-level info was unavailable).24 We used the resulting model
to predict the probability of a punitive (or anxious or mistrustful) response for each
permutation of demographic and geographic characteristics. Last, to estimate state or
state-race opinion in each of the years in which a question was asked, we weighted each
of these demographic-geographic types by their share of the relevant population.25
These steps give state-race-year estimates of responses to each question. To make
analysis tractable, we follow Enns and estimate trends in each of the three dimensions,
by pooling information across questions in a given dimension using Stimson’s Dyad
Ratios algorithm (Bartle, Dellepiane-Avellaneda, and Stimson 2011; Stimson 1999).
Figure 9 plots the results of running Stimson’s algorithm separately in each of
the three dimensions, and for each state-race permutation. The faded lines plot these
state-race trends, and the bold lines plot the state-level averages. These indices reveal
information that the earlier analysis obscured. There is a discernible increase in the
proportion of white and black people giving punitive and mistrustful answers between
the early 1970s and the mid-to-late 1990s—a period which corresponds quite well with
the punitive turn in policy. In fact, black punitiveness increases more than white.
24. We fit models of varying complexity, the most complex of which made allowances for interac-
tions between race, place, and time. To adjudicate between the three models we trialed, we estimated
three different models on a training set (a random sample of 80% of the respondents), and picked
the model which best fit respondent patterns in the test set (the other 20%). Not all questions are
fit with the same model, either for reasons of fit or because more complex models failed to converge.
Section D of the Appendix gives details.
25. Together, this set of steps has come to be known as MRP (multilevel regression and poststrat-
ification). For more details about the approach and its advantages vis-a-vis simple disaggregation,
see Park, Gelman, and Bafumi (2004) and Lax and Phillips (2009b).
20

Anxiety about crime, on the other hand, remains at elevated levels throughout.26
4.1.1 Black Politicians and Public Opinion
These graphs reveal trends that broadly correlate with the punitive turn. While
we found no evidence, unlike Enns (2016), that punitiveness drove policy directly
(see Table 2), shifts in public opinion could still have shaped policy indirectly. To
test this, we add interactions between our covariates and state-specific measures of
public opinion to the models estimated earlier. Our first model interacts Enns’s
composite measure of punitiveness with each of the two political covariates in our
model (democratic control, and black representation). To examine whether these
results were robust to disaggregating the different dimensions of public opinion, we
replaced Enns’s measure of punitiveness with measures of state-level opinion in each
of the three dimensions, and interacted each of the same two covariates. Table 4
presents estimates of the long-run effect of black elected officials in each of these
models, evaluated under two different scenarios. Scenario (A) refers to the expected
long-run effect of an influx of black elected officials in a situation of low concern—with
punitiveness, anxiety, and mistrust set to their 20th percentile values. Scenario (B)
calculates the same effect, but in a very different context—with punitiveness, mistrust
and anxiety set to their 80th percentile values.
Note that Model (1) only includes punitiveness, as defined by Enns, so these sce-
narios are distinguished by movements in that variable alone. Regardless, in lumping
movements in these three dimensions into two scenarios, in Model (2), one might won-
der why we expect high levels of mistrust to have the same mediating effect on political
outcomes as high punitiveness and anxiety. Indeed, if people turn mistrustful of crim-
26. There is no meaningful interpretation of the underlying scale in Stimson’s algorithm, but some
meaning can be imputed given an interpretation of the levels of all the questions on which it is based.
21

inal justice institutions, should they not be less likely to demand police and prisons?
We considered this possibility, but all evidence points in the opposite direction. The
interaction coefficients estimated below suggest that higher levels of mistrust make
black politicians more punitive. We suspect this is because mistrust registers dissat-
isfaction with existing criminal justice institutions, much of which stems from anxiety
about crime. In a political environment which forecloses other alternatives, it is not
surprising that this is channeled into support for police and prisons.
Recall that in our baseline specification, the effect of black political representa-
tion on the incarceration rate was positive, but insignificant. With the interaction
included, however, a more informative story takes shape. In both models, the effect of
black politicians on the incarceration rate is significantly more positive at high than
at low levels of concern.27 In Model (1), this difference is significantly different from
zero, even though the individual estimates are not themselves different. Results from
Model (2) are even more suggestive. Here, where the population turns more punitive,
anxious, and mistrustful of courts and criminal justice institutions, an influx of black
politicians is associated with the subsequent addition of 26 prisoners for every 100,000
people (give or take 26). Where they are not, the same influx is associated with a
decline of about 7 prisoners (give or take about 18).
This same specification invites an interpretation of the otherwise puzzling finding
that black political representation had a negative effect on corrections spending. With
interactions included, this negative effect is pronounced (substantially larger, and
significant at α= 0.05 and α= 0.10) in a context of low concern—the same context
in which the estimated effect on the incarceration rate is substantially lower and/or
negative. It is attenuated in Scenario (B).28
27. This is shown in the row denoted by ∆, which is the estimate of the difference between the
long-run multipliers in the two scenarios.
28. As Table 4 shows, this difference is statistically significant at α= 0.10 in Model (1), and close
22

In summary, the evidence suggests black politicians had a positive effect on the
incarceration rate, but that this effect was concentrated in a context of high black
concern. In the opposite context, they may well have had the opposite effect. Future
work might consider whether anything meaningful can be learned from the domain
in which they had these dueling effects. A positive effect on the incarceration rate
(absent the same on spending) suggests a legislative impact at times of high con-
cern (in the late 1980s and early 1990s), whereas a negative effect on corrections
spending (absent clear-cut evidence of the same, on the incarceration rate) suggests
a predominantly budgetary influence in (later and more recent) low-concern periods.
With regards to policing, the implications are different. Here, we find that an
influx of black legislators has a positive long-run effect on the officer rate in both
scenarios. High black concern amplifies this association, but not dramatically. The
balance of evidence suggests, as before, that black politicians had a positive effect on
policing, and that this effect was largely impervious to the context set by aggregate
public opinion.
4.2 Revanchist Whites?
Redistricting occurred in mostly Southern states at the same time as a flight of
Southern whites to the Republican party. Could the rise in punitive outcomes around
redistricting have been the work of Southern Republicans empowered by an influx of
white voters? We consider this unlikely. Over the redistricted period, Republicans did
not have veto-proof control of any of the state legislatures affected by redistricting.
Their first gains, in these terms, came in the late 1990s, well after the end of the
period we considered. Some scholars date the departure of Southern whites to the
late 1960s (Kuziemko and Washington 2015), but, as Figure 11 shows, this was most
to statistically significant in Model (2).
23

pronounced in presidential elections. In congressional elections, realignment was more
gradual. As Gavin Wright (2016, 18) argues, “...the median southern white voter cast
a ballot for a moderate-to-liberal Democrat until 1994.”
But if revanchism was not partisan, it could still have been racial. The influx
of black politicians might have triggered a punitive alliance of the white majority,
Democrats and Republicans alike. However, this interpretation understates the extent
to which the Democratic party had been transformed by the Civil Rights movement.
As Wright (2016) argues, by the 1980s and 1990s, the Democratic party had evolved
into a multiracial coalition in the South. This strategy yielded success in the 1980s and
immediately after the post-redistricting elections, where they increased their share of
veto-proof control in redistricted states to 90% (in 1991 and 1992). Success of this
kind would seem a strange pretext for a revanchist party revolt.
If outcomes around redistricting were the work of a majority white reaction to
black advance, their hand should have been visible in other policy outcomes. We
examined the level of AFDC benefits paid out by individual states. Given the highly
racialized character of welfare provision, particularly in the South, we would expect a
revanchist white majority to have cut these benefits. But we find no evidence of this.
The estimated impact of redistricting is actually positive, and statistically significant
in a simple comparison of means. Put another way, while all states were cutting
welfare at this time (see Table 3), those affected by redistricting cut it less than those
which were not. While Table 3 shows that this result is not robust to adding controls
or to the other specifications we trial, the estimate never turns negative. In short,
the balance of evidence suggests that redistricting empowered black representatives.
Of course, our inference is not that they made policy unilaterally. But redistricting
gave them the clout to bargain more effectively with whites inside and outside of their
party. As the next section argues, they made policy, even if not under conditions of
24

their own choosing.
4.3 Federal Voting Patterns
While the evidence accumulated thus far suggests a punitive impact on policing and
incarceration, nothing in our analysis explains how an increase of black politicians at
the state level translated to more prisoners or to more police. It is not straightfor-
ward, unfortunately, to analyze legislative histories at the state level. No long-run,
centralized repository of voting records exists, nor is there a record of the identifiably
punitive legislation to analyze. Constructing a database like this one for select states
should be a priority for future research, but it is likely to be considerably resource-
intensive. In lieu of this, we propose a substitute case study: we examine the role of
African-American congressmen and congresswomen in the federal House of Represen-
tatives.29 Their votes were a matter of public record, and the availability of roll call
data for amendments as well as bills allows for fine-grained analysis of the legislative
process.
4.4 The Punitive Turn in Congress
In 1968, when it passed Johnson’s Omnibus Crime Control Act, the House of Repre-
sentatives had 6 black members. By 2014, it had 45—the largest increases occurring
in the 1970s and 1990s, a result of the voting rights reforms discussed earlier. These
incoming members have almost all been affiliated with the Democratic party, and
since 1971 they have been organized in the Congressional Black Caucus (CBC)—a
remarkably cohesive voting bloc (Pinney and Serra 1999). We tracked the votes of
these black representatives on federal crime policy from 1968 to 2015, and compared
29. We look only at the House because black members in the Senate have always been too few to
constitute a significant voting bloc.
25

them to the voting record of non-black Democrats.
Figure 12 plots the percentage of representatives who voted in a punitive direc-
tion on federal crime bills. In the case of those bills and amendments that increased
mandatory minimum sentences or gave more power and resources to prosecutors and
police, this is the percentage who voted “yea.” In the case of those bills and amend-
ments that promised to reduce sentence length or severity, restrict police or prose-
cutorial power, or provide alternatives to incarceration this is the percentage who
voted “nay.” Non-voting members are included in the denominator.30 In line with
the evidence from the opinion polls, these data yield contrasting findings. On the
one hand, they indicate that African-American members of the House have been con-
sistently less punitive than their fellow Democrats in their voting patterns. In 22 of
28 votes a smaller percentage of African-American politicians took punitive positions
than did other Democrats, and in 13 of these cases the difference was significant.
Note that in this figure the error bars reflect the relative size of each group. They
can be thought of as the impact of a marginal vote change, rather than an underly-
ing population estimate. There is no clear trend in the gap between the percentage
of Democrats and CBC members voting punitively, but the increasing numbers of
African-American congressmen narrow the error bars and demonstrate that the gap
is consistently significant in this sense.
On the other hand, Figure 12 shows that an absolute majority of African-American
representatives voted in favor of each of the major federal crime bills of the punitive
turn: the Omnibus Crime Control of 1968; the Comprehensive Crime Control Act
of 1984; and the Violent Crime Control and Law Enforcement Act of 1994. It also
shows that the majority of CBC members consistently supported bills that increased
30. We tried to include all bills relevant to crime and punishment, whether they increased or de-
creased punitiveness. Unfortunately many bills were subject to a voice vote, in which case individual
votes were not recorded.
26

mandatory minimums for those at the centre of public outrage, such as drug dealers
in the 1980s, and sex offenders in the 1990s and 2000s. For instance, a majority of
Caucus members (65%) voted in favor of the Anti-Drug Abuse Act of 1986, which
imposed the notorious 100-1 disparity in sentencing for crack vs. powder cocaine.
Yet from the 1990s CBC members pushed to repeal that disparity, finally succeeding
with the Fair Sentencing Act of 2010 (not shown in Figure 12 because it was a voice
vote).
4.5 Clinton’s Crime Bill
Overall, CBC members appear as reluctant supporters: at times opposing tougher
amendments supported by most Democrats, but generally following the party line
on crucial roll call votes. A telling example is the Violent Crime Control and Law
Enforcement Act of 1994. Clinton’s signature crime bill added 60 new federal death
penalties, increased mandatory minimums for federal drug offenders, and granted $8
billion of federal aid for prison construction. Much of that aid was made contingent
on states passing truth-in-sentencing policies requiring that all violent offenders serve
at least 85% of their sentence. By 1998, 28 states and the District of Columbia had
qualified. Since truth-in-sentencing unilaterally increased sentence length scholars
have seen the 1994 bill as a major contributor to the continued expansion of American
prison populations (Travis, Western, and Redburn 2014, 79-83).
The 1994 bill came at a time when the CBC was at the height of its influence
(Frymer 1999, 150,176), and the CBC played an important role in shaping early
drafts of the bill. The previous fall CBC members in the House had blocked passage
of a draconian crime bill passed by the Senate, which Clinton had supported. In
January Jesse Jackson’s National Rainbow Coalition held a summit on crime, in
27

which CBC leader Kweisi Mfume (D-MD) complained the Senate’s bill would only
“find better ways to incarcerate people.” CBC members on the House judiciary
committee subsequently ensured the first draft of the House bill contained crime-
prevention programs that would direct funds to poor neighborhoods, and successfully
fought to add a “racial justice” provision, allowing death row inmates to challenge a
sentence as racially discriminatory.31 Overall, the CBC’s interventions led to a less
punitive crime bill in the House.
The vote counts in Figure 13 show this influence. As the bill passed through the
legislative process, CBC members often opposed amendments designed to make it
more punitive. In particular, they were critical to defeating a Republican attempt
(A019) to remove the racial justice provisions. A majority of members also opposed
(albeit less successfully) amendments to extend and strengthen the federal death
penalty (A003–A010), to add drug offenses to the bill’s “three strikes and you’re out”
provisions (A011), and to abolish Pell Grants for federal prisoners (A023).32 And
while a third of the membership supported adding “truth-in-sentencing” to the bill
(A014), CBC votes were critical to passing an amendment (A017) that replaced the
truth-in-sentencing language (“85% time served”) with the looser requirement that
the state had to have “sufficiently severe punishment for violent repeat offenders” in
order to receive federal funds.
Despite the influence CBC members exerted in both drafting and preserving the
crime prevention and racial justice provisions of the House bill, a third of the mem-
31. Republicans in the House had previously blocked a Racial Justice Act containing the same
provisions—on the grounds that it would lead to racial quotas in sentencing. 15% of the judiciary
committee were CBC members in 1993-1994 (Canon 1995).
32. The Kopetski, Derrick and Wynn amendments each represented failed Democratic attempts
to offer a compromise on a part of the bill that had already been amended in a punitive direction.
For instance, Wynn (D-MD), a CBC member, proposed to restrict rather than abolish Pell Grants
to prisoners, leaving it to individual states to decide. Although they would actually have made the
bill more punitive than its initial draft, we have coded them as non-punitive in Figure 13 because
they were intended to make the bill less punitive than it had become.
28

bership still opposed the bill when it first came to a general vote on April 21. These
members were holding out against the death penalty provisions that had been added.
These hopes were soon dashed, however. Democratic leaders would eventually win
even more CBC members over to the final and far more draconian version of the bill.
In this process the CBC was a victim of both maneuvering by House leaders and its
own internal divisions over crime.
First, in the initial congressional conference, convened to combine House and
Senate versions of the bill, Senate leader Joe Biden convinced Democratic senators to
drop the racial justice constraints on the death penalty.33 Conferees also reinserted
the truth-in-sentencing language that the CBC had helped to remove. The conference
report was widely seen as a defeat for the CBC. When it was brought to the House
on 11 August, the nay votes of CBC members were pivotal to defeating the bill in
a procedural vote. The loss came as a shock to Democratic leaders. Almost all
Republicans voted against it, and they were joined by 48 anti gun-control Democrats
and 11 CBC members. In justifying their defection from the party line they cited the
dropping of the racial justice provisions (Seelye 1994; Frymer 1999, 175).
Next, in the following week the White House and Democratic leaders managed to
convince some key CBC holdouts—Charles Rangel (NY), Cleo Fields (LA) and John
Lewis (GA)—to back the bill. To do this they exploited divisions within the black
community, by collecting endorsements for the bill from dozens of prominent African-
American religious leaders and ten black big-city mayors. Moreover, House leaders
discovered they they could pass the bill without CBC support, by attracting moderate
Republicans to their side (Kim 2002, 66). The resulting compromise involved a drastic
reduction of funding for crime-prevention measures that CBC members had fought
33. After House conferees had voted to include these provisions Biden announced: “The question
is whether to accept the House provision, racial justice, which will kill the bill.” Since Republican
conferees abstained in this vote the provision was removed by a majority vote of Democratic senators.
29

to defend.34
Crucially, even as the CBC saw some of their most valued provisions stripped
from the bill, the majority of members continued to support it—illustrating the bind
confronting black elected officials. When the House voted on the final bill, on August
21, the CBC voted 24 to 12 in favor. How do we explain this? Some have argued that
Democratic party loyalty, or pressure from higher ups, trumped concerns about the
bill’s punitiveness (Fortner 2015b). Others have claimed that they were motivated
by fear of an even more punitive Republican bill if Clinton’s was to fail (Hinton,
Kohler-Hausmann, and Weaver 2016). But while both theories help to explain the
swing votes of some CBC members, they provide less insight into the support shown
by many CBC members for some of the amendments which made the bill even more
punitive.
For example, eight CBC members (20% of the membership) supported the death
penalty for “drug kingpins” (A006), one third voted in favor of the Chapman amend-
ment that added truth-in-sentencing to the bill (A014), and more than half supported
the Brooks amendment that restricted the ability of prisoners to sue prison admin-
istrators and banned weight-lifting in prison (A018). When questioned about theses
decisions CBC members, like most other members of congress, tended to cite the
urgent need do something about a widely perceived crime epidemic. For example
an interview with Alan Wheat (D-KS) explained that “the crime bill’s promise of
more police, more prisons and more money for crime prevention was too important
to jeopardize by holding out for the racial-justice provision”(Sawyer 1994).
In keeping with this sentiment, polls indicated strong public support for Clinton’s
34. As critics of these measures focused on a small number of earmarks for “midnight basketball”
programs in inner city neighborhoods, crime prevention was increasingly identified by both sides of
the debate as a black issue (Wheelock and Hartmann 2007). In the end, funding for crime prevention
was cut by 20% ($2 billion), while funding for prisons was cut by 7% ($800 million).
30

crime bill, especially among African Americans.35 As Figure 9 shows, black puni-
tiveness, anxiety and mistrust were all at or close to their peak levels at this time.
Moreover, many prominent black leaders had come out strongly in favor of the bill,
urging CBC members to put aside their reservations. In the end, the combination of
political constraints and deep crime anxiety shoehorned CBC members into backing
a bill that many of them had vociferously criticized.
5 Conclusion
In this article we have gathered a large amount of evidence that is difficult to reconcile
with the conventional view of the racial politics of the punitive turn. In state-level
panel regressions spanning almost forty years, we found that black representation
was associated with higher levels of policing per capita in subsequent years. Re-
sults around carceral outcomes were also unexpected: while black elected officials
had a negative and weakly significant effect on corrections spending, their effect on
incarceration was positive. This ambiguous finding is probably explained by context,
since the positive impact on incarceration was concentrated during the peak of public
punitiveness, and the negative impact on carceral spending during its trough. Our
analysis of the impact of federally-mandated redistricting in mostly Southern states
in the early 1990s found that the positive association between black political rep-
resentation and subsequent levels of policing and imprisonment was not obviously
spurious. Redistricted states saw larger increases in policing and imprisonment than
their non-redistricted counterparts.
In general, public opinion and legislative evidence affirmed that these trends are
unlikely to be the product of “white backlash.” Polling data shows that blacks became
35. The third row in Figure 7 shows that 76% of blacks with clear views supported the bill,
compared to only 59% of whites.
31

more punitive during the period of the punitive turn, and that—alongside evidence
of a “racial gap” in punitiveness—absolute levels of black punitiveness and crime
anxiety were remarkably high. We found parallels in the congressional record: black
representatives in Congress expressed concern with punitive legislation, but when
faced with up and down votes a majority invariably opted for more police and prisons.
One could interpret these findings as a testament to the exceptionally demo-
cratic character of the American criminal justice system. We have shown that black
Americans were racked by fears of crime, and that their representatives made policy
accordingly. This interpretation fits with those who have emphasized the “populist”
character of the punitive turn (Enns 2016). Yet we also found that black congressmen
and congresswomen provided majority support for the Clinton crime bill only when
the less punitive measures many of them had supported were defeated. Furthermore,
we found that the public answered much less punitively when offered a choice between
punitive and non-punitive alternatives. Both pieces of evidence suggest another read-
ing of our results: that support for tough-on-crime policies among black politicians
and their constituents may best be explained by structural and political constraints
that narrowed the field of policy options (Alexander 2016; Hinton et al. 2016; For-
man Jr, forthcoming). African-Americans and their elected representatives may have
chosen punitiveness, but they did not do so under conditions of their own choosing.
While we believe that the evidence we have accumulated represents a significant
advance, there is ample room for future improvements. First, we examined the politics
of incarceration and policing together. The obvious benefit of this approach is that it
allowed us to interrogate the conventional account in two salient domains of criminal
justice policy–both of which have entertained variants of the “white backlash”-based
explanation of punitiveness. The cost, of course, is that the politics of policing might
be substantially different from the politics of incarceration. We found some evidence
32

of this in our panel specifications: the effect of black elected officials on policing
was consistently more statistically noticeable than the analogous effect on incarcer-
ation, and this effect seemed more impervious to context. It is plausible that black
politicians saw police rather than prisons as their first line of defense against crime.
Future work should consider disentangling these two outcomes more deliberately than
we have done here.
Second, while our analysis of public opinion makes use of better data and better
techniques than have previously been employed in this domain, our approach is inef-
ficient. Recall that we estimate 39 different models, many of which were limited by
data availability. These estimates were then pooled via Stimson’s Dyad Ratios algo-
rithm. One should merge these two steps, and fit a single model which would estimate
each question’s idiosyncrasies alongside the impact of key covariates on respondent
answers. We are pursuing this approach in current work. Empirically, these estimates
raise a host of relevant but as-yet unanswered questions. Do black and white publics
respond to crime rates, to levels of policing, levels of incarceration, and/or to the
media’s presentation of crime? Do they do so differently, or in similar ways?
Third, though we have referred to the considerable constraints under which black
politicians and the black public supported punitive legislation, this paper has done
little to clarify their character or their precise importance. Certainly, the fact that the
political process narrowed the field of possible policy responses is unsurprising, but
alternatives were not abandoned because they were technically infeasible or unimag-
inable. Recall that in 1968 the Kerner Report urged the Federal government, as a
matter of urgency, to combat riots and crime with a jobs program, an integrated
education system, expanded welfare and decent housing. If a Marshall Plan could be
crafted for Europe, why not for the ghetto?
The reasons are mostly beyond the scope of this paper, but they deserve to be
33

better understood. Black elected officials were obviously bound by the fact that
they were, at best, only ever a significant minority in state and federal legislatures.
They had to make their way in an environment in which “law and order” policies were
already dominant. Perhaps it is difficult to imagine that alliances with the incumbent
political elite could have produced anything but a punitive agenda.
The structure of American political power hamstrung them further. As Miller
(2010) argues, alternatives to a punitive agenda have flourished at the level of local
government, where black victims are most likely to be involved, but have floundered
as they have made their way up the political food chain. She attributes this to
balkanizing effects of American federalism, which both impede collective action at
the municipal level and limit the “scope and tenor of the central government’s power
to address social problems” (ibid., 807). These constraints combine to make tougher
sentencing the policy of least resistance: state-level politicians can credibly claim
representation while also avoiding well-supported but significantly more difficult al-
ternatives.
This said, in recent years the political mainstream has shifted in favor of penal
reform, and black politicians have often led this charge (Barker 2010). Our own data
shows some signs of this shift. We found that the negative effect of black political
representation on corrections spending was concentrated in times of low punitiveness.
It is far from clear that these reform attempts will add up to a wholesale change in the
criminal justice system (Gottschalk 2014), but falling rates of crime and a growing
awareness of the social costs of mass incarceration may, we hope, augur a new politics
of punishment.
34

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40

Table 1: In-Sample Descriptive Statistics
µ σW ithin σBetween % Var. Within ∆
Incarceration Rate 269.80 132.90 105.70 64.80 Yes
Officer Rate 230.90 35.10 47.30 39.80 No
Corrections Spending 4.41 0.55 0.34 72.50 No
Black Political Representation (%) 5.37 2.06 4.77 28.10 No
Democratic Control 0.24 0.46 0.52 48.20 No
Violent Crimes per 100,000 440.60 93.80 207.00 20.50 No
GDP per capita (Log) 10.30 0.17 0.10 76.10 Yes
Growth Rate 10.30 0.17 0.10 75.70 Yes
Income Inequality 0.54 0.05 0.02 87.10 Yes
Tax Collection 192.30 41.10 49.10 52.70 No
Black Population (%) 9.86 0.75 9.40 1.09 No
Punitiveness (Enns) 57.50 5.69 1.65 92.30 No
Crack Index 0.89 0.85 0.63 70.60
Unemployment Rate 6.77 1.58 1.45 55.40
Poverty Rate 13.00 0.85 3.56 6.80
Punitiveness (Ours) 69.50 8.61 1.81 95.80
Anxiety 67.90 2.27 1.89 58.90
Mistrust 42.20 4.57 2.28 80.00
1All statistics refer to a consistent, single sample. For dependent variables, this is the sample specific to the
preferred models for the given dependent variable. For independent variables, this is the preferred sample for the
models of the incarceration rate. For the variables present only in the D-in-D analysis, this is the difference-in-
difference sample.
2In the tables presenting our regression results, all estimates are multiplied by the average within-state standarard
deviation of the relevant variable, to give an impression of effect size. These are given in the column ‘σW ithin ’.
3‘% Var. Within’ is the ratio of the sum of squares within states, to the total sum of squares. As discussed in the
main text, the use of state fixed-effects across our specifications means that we make use of only this dimension of
variance in our analyses.
TF-1

Table 2: Results from Panel Regressions
Incarceration Rate Officer Rate Corrections Spending
Lagged Dep. Vars
Incarceration Ratet−11.089**
(0.063)
Incarceration Ratet−2-0.131*
(0.062)
Officer Ratet−10.557**
(0.072)
Officer Ratet−20.228**
(0.020)
Officer Ratet−30.116+
(0.066)
Officer Ratet−4-0.060*
(0.029)
Corrections Spendingt−10.806**
(0.021)
Short-Run Impact
Black Political Representation (%)t−10.568 0.957*-0.656+
(0.657) (0.421) (0.355)
Democratic Controlt−10.168 -0.119 -0.542+
(0.412) (0.262) (0.312)
Violent Crimes per 100,000t−12.160** 0.840** 0.608
(0.657) (0.280) (0.405)
GDP per capita (Log)t−1-2.126 -0.817 7.994**
(2.387) (2.132) (2.415)
Growth Ratet−10.934 3.180 -5.446+
(2.442) (2.525) (2.919)
Income Inequalityt−1-0.913 -2.045*-0.241
(0.943) (0.810) (0.642)
Tax Collectiont−11.308** 0.832** 0.961**
(0.200) (0.243) (0.246)
Black Population (%)t−1-0.617 -0.615 -0.038
(0.563) (0.447) (0.279)
Punitiveness (Enns)t−11.730 -0.708 -1.786
(5.159) (5.169) (2.884)
Long-Run Multiplier
Black Political Representation (%) 13.240 6.041*-3.368+
(16.187) (2.572) (1.932)
Democratic Control 3.694 -0.733 -2.817+
(10.151) (1.757) (1.512)
Violent Crimes per 100,000 51.454** 5.288** 3.141
(15.085) (1.750) (2.126)
GDP per capita (Log) -52.912 -5.292 41.516**
(58.487) (14.054) (13.695)
Growth Rate 21.887 20.161 -28.448+
(61.492) (15.807) (16.296)
Income Inequality -21.482 -12.991*-1.325
(25.026) (6.100) (3.339)
Tax Collection 31.224** 5.249** 4.958**
(6.306) (1.774) (1.307)
Model Info
Observations 1802 1764 1813
States 49 49 49
Range 1972-2008 1973-2008 1972-2008
Avg. Ni36.8 36 37
State FE Yes Yes Yes
Year FE Yes Yes Yes
Lags of DV 2 4 1
Adj. R20.937 0.876 0.911
1 **p < 0.01, *p < 0.05,+p < 0.10. Two-tailed tests. Standard errors in parentheses.
2To give an impression of the conditional effect size, we multiply all estimates by the average within-state standard
deviation of the relevant variable. These are given in Table 1.
TF-2

Table 3: Difference-in-Difference Estimates Around 1990 Redistricting
Model θRD Aggregation? Block-Bootstrap?
Incarceration Rate (1) Simple 65.090** Yes** Yes*
(21.8)
(2) Full 47.469+No Yes+
(27.3)
(3) New Districts 20.545 No No
(16.1)
(4) ∆ 8.198 No No
(7.42)
Officer Rate (1) Simple 24.569** Yes** Yes**
(5.54)
(2) Full 16.928** No Yes**
(4.68)
(3) New Districts 21.260** No Yes**
(5.77)
(4) ∆ 19.447** Yes+Yes**
(5.09)
Corrections Spending (1) Simple 1.272 No No
(7.26)
(2) Full -3.556 No No
(10.1)
(3) New Districts -12.346*No No
(4.97)
(4) ∆ -2.340 No No
(8.43)
AFDC Benefits (1) Simple 15.524** Yes** Yes*
(5.29)
(2) Full 7.619 No No
(5.52)
(3) New Districts 1.591 No No
(6.64)
(4) ∆ 9.622 No No
(5.86)
1 **p < 0.01, *p < 0.05,+p < 0.10. Two-tailed tests.
2The numbers in parentheses delimit a 95% confidence interval for the parameter estimate.
3Model (1) gives estimates of βT reatment from a straightforward comparison of means. Model (2) adds state and
year fixed-effects, and a full set of controls. Model (3) interacts the treatment variable with a measure of the
intensity of redistricting. Model (4) employs the first difference of all variables which might be unit root. See 7 for
details.
4The last two columns report whether the relevant results were robust to aggregating the data to just two time
periods and to block-bootstrapping, respectively. See Bertrand et al. (2004).
5As before, the estimates are multiplied by a scalar to ease intepretation. Where the dependent variable is
logged, the estimate is multiplied by 100, and thus roughly interpretable as the expected percentage change in the
dependent variable conditional on treatment. Where the treatment variable is interacted with a measure of the
intensity of treatment, the estimates are multiplied by the median increase in black-majority districts in states
which experienced redistricting.
TF-3

Table 4: Long-Run Effect of Increase in Black Political Representation, Conditional on Black
Public Opinion
Scenario (1) (2)
Incarceration Rate (A) Low 2.548 -7.096
(13.3) (17.5)
(B) High 19.657 26.300*
(14.9) (13.8)
∆ 17.283*33.430**
(8.53) (12.4)
Officer Rate (A) Low 8.330** 6.046*
(2.09) (2.95)
(B) High 8.992** 10.279**
(2.25) (2.49)
∆ 0.642 4.192
(1.93) (3.15)
Corrections Spending (A) Low -5.588*-5.278+
(2.42) (3.18)
(B) High -2.734 -1.699
(1.99) (2.06)
∆ 2.887+3.611
(1.68) (2.67)
1 **p < 0.01, *p < 0.05,+p < 0.10. Two-tailed tests. Standard errors in parentheses.
2All estimates refer to the expected long-run effect of an influx of black legislators equivalent to the average
within-state standard deviation.
3Under Scenario (A) we compute the estimated long-run effect when punitiveness, black mistrust, and black anxiety
are set to their 20th percentile values. This denotes a ‘low concern’ scenario. By contrast, Scenario (B) denotes
high punitiveness, high mistrust, and high anxiety. Here, both of these values are set to their 80th percentile values.
∆ displays the estimated difference between the long-run multipliers in the two scenarios.
TF-4

Figure 1: Incarcerated per 100,000
Dashed lines denote years for which we have data on the incarcerated population, but which are excluded from the
regression analysis due to other missingness. The red line fits a locally-weighted smooth through the data.
TF-5

Figure 2: Police Officers per 100,000
See notes after Figure 1
TF-6

Figure 3: Corrections Spending per capita (Log)
See notes after Figure 1
TF-7

Figure 4: Black Political Representation
See notes after Figure 1
TF-8

Figure 5: Black Population Share
See notes after Figure 1
TF-9

Figure 6: Impact of 1990s Redistricting
Redistricting first affected electoral outcomes in the elections that took place at the end of 1990. This is reflected
in the increase in black political representation first observed in 1991. The entire period of the influx is shaded in
grey.
TF-10

Figure 7: Proportion Punitive, Anxious or Mistrustful
TF-11

Figure 8: Average White-Black Difference in Proportion Punitive, Anxious or Mistrustful
The point estimate and 95% confidence intervals are colored according to the level of αat which the null of no
difference can be rejected.
TF-12

Figure 9: Trends in Punitiveness, Anxiety and Mistrust
The thin lines plot trends over time, for each of the 50 states. The thick lines plot the average across states, for a
given race in a given year.
TF-13

Figure 10: Questions With Alternatives Elicit Significantly Less Punitive Responses
Questions which prime respondents to alternatives are: Prefer Death Penalty (Gallup), Use Force (ANES), More
Prisons and Police (Gallup), Stop Crimes Regardless (ANES), More Important to Punish (Gallup), Prefer Death
Penalty (ABC), Put Criminals Away (LAT).
*Questions which do not: Favor Death Penalty (Gallup), Favor Death Penalty (GSS), Favor Death Penalty (ABC),
Courts Not Harsh Enough (Gallup), Favor Death Penalty (Time), Favor Death Penalty (Roper), Favor Harsher
Sentencing (Roper), Courts Not Harsh Enough (GSS).
TF-14

Figure 11: Difference in Southern vs. Not-Southern Whites Voting for Democratic Party
TF-15

Figure 12: Percentage of Congressmen Voting Punitively, 1968 to 2015
1Bolded labels denote bills. Plain-text labels denote votes on conference amendments.
2Italics indicate bills and amendments which failed to pass.
3Asterisks indicate that the bill in question proposed to raise mandatory minimums.
4Crosses indicate that the vote of African-American congressmen was pivotal.
5Carets indicate that voting against a bill or amendment is considered the punitive response.
TF-16

Figure 13: Voting in the Violent Crime Control and Law Enforcement Act of 1994
See notes following Figure 12
TF-17

Online Appendix
A Sources and Definitions
Variable Source Coverage Definition
Incarceration
Rate
BJS National
Prisoner
Statistics,36 and
BJS Historical
Statistics on
Prisoners in
State and
Federal
Institutions37
1925-2011 The number of prisoners under
the jurisdiction of a given state
for every 100,000 residents. See
below for more details.
Police Officers
Per Capita
LEOKA Master
File from FBI
Criminal Justice
Information
Services
Division (by
request), and
BJS Directory
of Law
Enforcement
Agencies38
1960-2012 The number of police officers em-
ployed in a given state for every
100,000 residents. See below for
more details.
Spending on
Corrections Per
Capita
State
Government
Finances, U.S.
Census
Bureau39
1960-2007 Total state-level spending correc-
tions. Adjusted to 2007 dol-
lars using the deflator available in
Klarner’s State Economic Data.
36. Available as ICPSR 34540, at:http://www.icpsr.umich.edu/icpsrweb/NACJD/studies/34540/version/1
37. Available as ICPSR 8912, at:http://www.icpsr.umich.edu/icpsrweb/NACJD/studies/8912/version/1
38. Available at: http://www.icpsr.umich.edu/icpsrweb/NACJD/series/00169
39. Available at: http://www2.census.gov/pub/outgoing/govs/special60/State Govt Fin.zip
AP-1

State and US
Population
U.S. Census
Bureau (various
files)40
1900-2014 Estimate of resident population
at mid-year. Used to calculate
rates where they were not given in
the original data (i.e., for the cal-
culation of the incarceration rate
and the number of police officers
per capita).
% of Black
Elected Officials
The Joint
Center for
Economic and
Political Studies
(by request),
and Richard
Fording (by
request)
1970-2014 The proportion of state and fed-
eral legislators that are African-
American.
Violent (or
Property) Crime
Rate
FBI’s Uniform
Crime Reports41
1960-2012 Number of violent (or prop-
erty) crimes committed for every
100,000 residents
State
Population, by
Race
National Cancer
Institute42
1969-2013 Estimate of resident population
at mid-year, including estimates
of the number of black, white, and
other residents. Used to calculate
the percentage of a state’s popu-
lation that is African-American.
Partisan Control State Partisan
Balance, Carl
Klarner 43
1937-2011 Coded 1 if Democrats have veto-
proof control of the State, 0 if nei-
ther party does, and −1 if the Re-
publicans do.
Income Per
Capita (Level,
and Growth
Rate)
State Economic
Data, Carl
Klarner 44
1929-2012 Real personal income in 2007 US
dollars.
40. Available through: http://www.census.gov/popest/data/historical/index.html
41. Available at: http://www.ucrdatatool.gov/Search/Crime/State/StateCrime.cfm
42. Available at: http://seer.cancer.gov/popdata/download.html#state
43. Available at: http://hdl.handle.net/1902.1/20403
44. Available at: https://dataverse.harvard.edu/dataset.xhtml?persistentId=hdl:1902.1/20404
AP-2

Tax Collections
Per Capita
State
Government
Tax Collections,
U.S. Census
Bureau 45
1951-2013 Taxes collected by state gov-
ernment (adjusted to 2007 dol-
lars using deflators available in
Klarner’s State Economic Data)
Gini Coefficient US State-Level
Income
Inequality Data,
Mark W. Frank
46
1917-2012 State-level Gini coefficient. See
Frank (2009) for more details.
Unemployment
Rate
Local Area
Unemployment
Statistics,
Bureau of Labor
Studies (by
request)
1976-2014 Proportion of the labor force un-
employed.
Poverty Rate Small Area
Income and
Poverty
Estimates,
Census47
1960-201048 Proportion of the population liv-
ing below the poverty line.
Crack
Prevalence
Index
Measuring
Crack Cocaine
and Its Impact,
Roland Fryer49
1980-2000 Proxy for the impact and preva-
lence of crack cocaine (combin-
ing arrests, emergency room vis-
its, deaths, newspapers, and drug
busts). See Fryer, Heaton, Levitt,
and Murphy (2013) for more de-
tails.
AFDC Benefit
Levels
Wexler and
Engel (1999)
1940-1995 Average payment per recipient
through Aid to Families with De-
pendent Children (AFDC). See
Wexler et al. (1999) for more de-
tails.
45. Available at: http://www.census.gov/govs/statetax/historical data.html
46. Available at: http://www.shsu.edu/eco mwf/inequality.html
47. Available at: https://www.census.gov/did/www/saipe/data/statecounty/data/index.html
48. Note that estimates before 1989 are only available in Census years, and are not available online.
We obtained these by request.
49. Available at: http://scholar.harvard.edu/fryer/publications/measuring-crack-cocaine-and-its-
impact
AP-3

Congressional
Voting Data
Votes from
GovTrack,50
Race of Reps.
from House of
Representa-
tives51
1968-2015 Vote percentages on major crimi-
nal justice bills and amendments
calculated for black and white
Democrats in the House.
A.1 Calculating the Incarceration Rate
As mentioned, the data used to calculate the incarceration rate were obtained from
two separate sources: the Bureau of Justice Statistics’ National Prisoner Statistics
series (NPS), which contains detailed information on the status of prisoners in the
custody or jurisdiction of State and Federal institutions between 1978 and 2011; and
the Bureau of Justice Statistics’ Historical Statistics on Prisoners in State and Federal
Institutions (HS), which contains a single series counting the number of prisoners
under the custody of these same institutions.
Given our question, we are searching for a measure of the incarcerated population
that best captures the punitiveness of a given state. In our view, this requires counting
the prisoners under a state’s jurisdiction rather than those in its custody, since the
latter figure excludes prisoners housed in local jails or sent to other jurisdictions,
and may include prisoners imported from other jurisdictions. This is straightforward
enough for the NPS dataset, which provide this category directly (the sum of jurtotm
and jurtotf ). However, the HS dataset only contains information about prisoners
under the custody of a given jurisdiction.
Fortunately, these series overlap for nine years (1978-1986), which allows us to
make some inferences about how the populations under custody and jurisdiction dif-
fered, in any given state. We proceeded by inflating (or, in some states, deflating)
the number of prisoners under custody by the average ratio of the jurisdiction to the
custody count over the first five years of overlap (1978-1982).52 Again, in most cases
this resulted in estimates of the incarceration rate for earlier states that are higher
than estimates based on the population under custody alone, though the differences
are relatively slight. The median factor of inflation is about 1.04, and the average is
50. Available at: http://www.govtrack.us/
51. Available at: http://history.house.gov/
52. We chose the first five years because the codebook suggests (and the data show) that the
difference between the population under custody and jurisdiction grows wider as the 1980’s progress,
as more states began to rely on local and privately-operated facilities. We did not want to inflate
by a factor that reflected new trends which did not apply to the previous era.
AP-4

about 1.12.53
This approach does raise one additional issue for researchers interested in a con-
tinuous series extending to 1925, which is that the definition of the population under
custody was changed, in 1940, to exclude all prisoners with maximum sentences of
less than six months.54 Before that year, all prisoners were included, regardless of
sentence.55 Inflating the entire series by a consistent amount, based on the 1978-1982
overlap, is likely to understate the punitiveness of the first era (1925-1940). This
difference is probably slight, but it is difficult to know for sure. For our analysis this
inconsistency is irrelevant, so we do not dwell on it.
A.2 Calculating Police Officers Per Capita
Our measure of police officers per capita required a count of all the police officers
in a given state in a given year. To obtain this, we relied on two data sources:
(1) the Law Enforcement Officers Killed and Assaulted dataset maintained by the
Criminal Justice Information Services Division of the FBI, and (2) the Directory of
Law Enforcement Agencies Series available through NAJCD. By request we obtained
the former for all years between 1960 and 2013. The latter are a census of all existing
police agencies; as such, they are available only in 1986, 1992, 1996, 2000, 2004, and
2008.56
While the purpose of the LEOKA data is to provide a record of law enforcement
officers killed or assaulted in the course of duty, the dataset also provides information
on the number of officers and employees employed by reporting agencies in any given
year. To obtain the number of police officers per capita, we added the number of
police employees employed by all police agencies falling under a given state, and
divided by the total population (multiplying by 100,000 for informative units).
Unfortunately, these data have shortcomings. Not all police agencies report in all
years. And of those agencies that do, not all appear in all years. This is the case even
though LEOKA (which is under the purview of the Uniform Crime Reports program)
is not a survey but a quasi-census of all existing agencies. Correspondence with both
the FBI Criminal Justice Information Services Division and the National Archive
of Criminal Justice Data at the ICPSR (which also hosts LEOKA) suggested no
53. Alaska is an outlier. Between 1978 and 1982, the number of prisoners under the jurisdiction
were about twice the number that it held in its physical custody.
54. See: http://www.bjs.gov/content/pub/pdf/sfp2585.pdf for a discussion of this and other issues
involved in using the HS dataset.
55. The HS dataset does not report overlapping counts of both these definitions, which makes it
difficult to infer what this change implied. The difference between the 1939 and 1940 count was
ca. 6,000 in all states combined, which suggests that it may not have been that large. But the
population had grown by ca. 16,000 the year before this change, which may actually mean that the
change was more significant than the simple difference suggests.
56. We could not find a version of the 2004 data with complete geographic identifiers, so it was
unusable for our purposes.
AP-5

easy fixes, but suggested looking at the census of law enforcement agencies available
through the Directory of Law Enforcement Agencies Series in select years.
We used these data to adjust the LEOKA data, proceeding as follows. In each of
the census years for which we had geographic identifiers (1986, 1992, 1996, 2000, and
2008), we compared state-level estimates obtained through LEOKA to the figures
from the censuses. On average, we found that the LEOKA figures were off by about
14%. Understandably, 90% of the time, this was because the LEOKA figures under-
estimated the true count. At its largest the discrepancy between the two sources was
60%, but in general the errors were significantly lower (the IQR of the discrepancy
ranged from 7% to 18%).
To adjust our estimates, we calculated a factor of inflation for each state in
each census year (infst =off.CENSU Sst/of f.LEOKAst ). We inflated our census-
year estimates using this factor, which means that we are using census estimates
in census years. We drew on this factor of inflation to estimate counts in inter-
censal years (of f.ES T IM AT Est =infst ∗of f.LEOKAst ) (i.e., 1987-1991, 1993-
1995, etc.). To estimate the factor of inflation in intercensal years, we interpolated (
infs,t=j=(tj−ti)(infs,t=k−infs,t=i)
tk−ti+infs,t=iwhere iand kare census years, and jis an in-
tercensal year ). In doing this we assume that the level of coverage in a state changed
(mostly, improved) linearly between censuses. This is unrealistic, but we considered
it the most plausible way to retain the information contained in the LEOKA dataset
while adjusting those data to match the census. (For the years which predate the
first census (i.e., 1960-1985), we used the factor of inflation observed in 1986.)
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B Long-Run Multipliers
In any specification which includes a lag of the dependent variable on the right-hand
side of the equation, independent variables will have both immediate (or short-run)
effects on the dependent variable, as well as persistent (or long-run) effects. To see
this, note that a single unit change in any of the independent variables at time t
induces an initial adjustment in the dependent variable at time t+ 1 of magnitude
equal to its estimated coefficient (call it β). This is the short-run effect. In the
absence of a lagged term, this short-run effect captures the entirety of an independent
variable’s effect on the level of the dependent variable. Where a lagged term is
included among the estimators, however, the initial adjustment at time t+ 1 will
affect the level of the dependent variable at time t+ 2. The magnitude of this effect is
β×α, where αis the estimated coefficient associated with the lagged term. In turn,
the new level of the dependent variable will have a knock-on effect at time t+ 3, with
magnitude β×α2. This pattern persists, so the total effect of a single unit change
at time ton the dependent variable at time t+nis given by the geometric series
β+βα +βα2+· · · +βαn−1. The long-run effect is derived by setting nto ∞, in
which case this series can be written as P∞
n=0 βαn, which is equivalent to β
1−α.
As (De Boef et al. 2008, pp.191-192) explain, calculating the standard error of this
long-run estimate is not straightforward, since the long-run multiplier is the ratio of
two (or more) coefficients.57 It is possible to directly estimate this uncertainty using
the Bewley transformation. It is also possible to estimate it by simulation, which
is how we proceed in this paper. We simulated 5,000 draws from the appropriate
variance-covariance matrix and calculated a distribution for the long-run multipliers
of interest. We calculate a 95% confidence interval for the estimate by computing
the 2.5th and 97.5th percentiles of this distribution. This is our preferred gauge
of uncertainty. The standard errors we report are the standard deviations of these
same distributions. We also used an empirical cumulative distribution function to
summarize the distribution. This is how approximated the probability of rejecting
the null hypothesis that the true value of the long-run multiplier was 0.
57. When more than one lag of the dependent variable is included, as in most of our preferred
models, the long-run effect is equivalent to β
1−α1−α2−···−αn, where αnis the coefficient associated
with the nth lag of the dependent variable. If more than one lag of the independent variable is
included, the numerator changes to β1+β2+· · · +βm, where βmrefers to the coefficient associated
with the mth lag of the independent variable.
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C Unit Roots
As described in the main text, panel unit root tests were not decisive. All series were
cleared by at least one test; all series were also indicted by at least one test. We
consider this reasonable grounds for leaving all variables in their levels, but Table
9 gives the results of running a specification in which all suspect variables are first-
differenced.
All series failed the Hadri test, which has the most exacting null (see Table 8. For
this reason, we regarded series as suspect when they failed this and at least one of the
other three tests. By this criterion, the problematic series were: the incarceration rate,
police spending, GDP/capita, the growth rate, the Gini coefficient, tax collections,
and Enns’s measure of punitiveness. These suspect variables are identified in Table
1 in the main paper.
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D Public Opinion
D.1 Methods
In order to obtain state-race-year responses to each of the questions in our dataset,
we proceeded via a set of steps known together as multilevel regression and poststrat-
ification (MRP). First, for each question, we modeled the probability of a punitive,
mistrustful or anxious response as a function of a respondent characteristics. Second,
we used these estimates to predict the average response of a given race in a given
state in a given year, using information drawn from the census about this popula-
tion’s characteristics. While most of what we do is fairly typical of past work in this
domain (Park et al. 2004; Lax et al. 2009b, 2009a; Gelman and Hill 2006; Enns and
Koch 2013; Enns 2016; Kastellec, Lax, and Phillips 2014), we made a few amend-
ments to the procedure to better fit our aims and our data. (See Table 6 for details
about the questions and sources).
D.2 Model Specification
Our individual-level models of public opinion focus on a small set of standard covari-
ates.58 We use the following respondent characteristics: race (nonblack vs. black),59
sex, education (less than HS, HS graduate, some college, college grad), age (less than
29, 30 to 44, 45 to 64, and greater than 65), state, region (following others, we code
DC as its own region), and the year in which the poll was administered. Our baseline
model is thus
Pr(yi= 1) = logit−1(β0+αr ace
j[i]+αsex
k[i]+αed
l[i]+αage
m[i]+αstate
s[i]+αyear
t[i]) (3)
β0is the intercept. Each other term represents a ‘random effect’: that is, a term
drawn from a normal distribution with mean zero and a variance to be estimated.
58. Because final estimates rely on the combination of multilevel regression on the original poll
data and weighting by information from the Census, only those covariates can be used which are
available both in the constituent polls and in the Census.
59. We choose this binary coding for race in order to make it easy to fit the more elaborate models
described below. We trialed an ordinal, three-level coding (white, black, other), but this made these
more elaborate models much less likely to converge. This is due to the small number of respondents
who were neither white nor black in our samples. Future work might consider improvements, but
we believe the benefits of this specification outweigh its costs.
AP-9

αrace
j∼N(0, σ2
race), for j= 1,2
αsex
k∼N(0, σ2
sex), for k= 1,2
αed
l∼N(0, σ2
ed), for l= 1,2,3,4
αage
m∼N(0, σ2
age), for m= 1,2,3,4
αyear
t∼N(0, σ2
year ), for t= 1, . . . , t
αregion
n∼N(0, σ2
region , for n= 1,2,3,4,5
αstate
s∼N(αregion
m[s], σ2
state), for s= 1,...,50
As shown, states are nested within regions, so the various state effects are them-
selves drawn from a normal distribution centered around an estimated regional mean,
with variance to be estimated. Note also that the number of year-based random ef-
fects varies, depending on the question under consideration. Some questions are asked
in several years, and some in as few as two.
Given the data at our disposal, however, it is reasonable to wonder whether this
baseline model extracts all useful information. Consider, for instance, our particular
interest in capturing racial differences in the contours of public opinion. By construc-
tion, Equation 3 pools information across these groups, which may underestimate the
impact of race on opinion formation. We therefore also estimated two additional mod-
els, which introduced a series of fixed effects and further, interaction-based random
effects.
Pr(yi= 1) = logit−1(β0+βr aceRAC Ei+βsex SEXi+
βedEDi+αage
m[i]+αstate
s[i]+αyear
t[i]+αrace.state
j[i],s[i]
(4)
Pr(yi= 1) = logit−1(β0+βr aceRAC Ei+βsex SEXi+βedEDi+
αage
m[i]+αstate
s[i]+αyear
t[i]+αrace.state
j[i],s[i]+αrace.year
j[i],t[i]+αrace.state.year
j[i],s[i],t[i]+(5)
The model described in Equation 4 estimates fixed effects for race, sex, and ed-
ucation, and introduces state-year random effects. This relaxes the restriction that
the effect of race on opinion is the same in every state.60
αrace.state
j,s ∼N(0, σ2
race.state), for j= 1,2, s = 1,...,50
60. Of course, given that no sample ever contains respondents of both races in every state, some
pooling across categories is mandatory.
AP-10

The yet-more complex model described in Equation 5 introduces additional race-year
and race-state-year random effects, further relaxing assumed restrictions on the effect
of race.
αrace.year
j,t ∼N(0, σ2
race.year ), for j= 1,2, t = 1, . . . , t
αrace.state.year
j,s,t ∼N(0, σ2
race.state.year ), for j= 1,2, s = 1,...,50, t = 1, . . . , t
In some cases, the middling and complex models had to be adjusted, due to
data availability. We were working with the public-use version of the General Social
Survey (GSS), in which access to state-level identifiers is not possible. Moreover, other
questions lacked usable state-level identifiers. Rather than discarding these data, we
used census division identifiers in lieu of state-level identifiers. These divisions were
nested within a four-tiered classification of regions.61 This is not ideal, and it means
that our final series likely understate geographic variation in responses, but it is far
preferable to discarding these data. It would be easy to improve upon this in future
research.
D.3 Estimation and Selection
Of course, it is not always preferable to fit more complex models, even where possible.
Over-elaborate models have a tendency to make inferential mountains out of stochas-
tic molehills–to fit the ‘noise’, in other words. Thus, to choose between these three
models, we relied on a predictive exercise. We partitioned all responses to a given
question into a training set containing 80% of the responses, and a test set containing
the other 20%. We fit each of the three models to this training set, and chose the
model which best fit the test data. In some cases, more elaborate models failed to
converge. Obviously, we could only pick from amongst those that did. Table 6 in the
main paper lists which models were used for which questions: simple (Equation 3),
middling (Equation 4), or complex (Equation 5).
Note one further wrinkle. Following Enns (2016), we employ Stimson’s Dyad Ra-
tios algorithm to estimate public opinion in each of the three dimensions to which
these many different questions pertain. Stimson’s algorithm requires a binary mea-
sure of punitiveness (or anxiety, or mistrust). Befitting this approach, we fit logistic
regressions to each of the questions in our dataset.
This, however, required a strategy for handling so-called ‘neutral’ responses. What
is to be done about those people who answer neither punitively or not-punitively? We
chose against discarding these responses. If there is some pattern in the population
answering neutrally, discarding responses would be a source of bias. Extrapolating
61. DC could not be its own region, here, since could not identify DC-based respondents in these
data.
AP-11

from this sub-population to the general population (via poststratification) would not
be justifiable.
Instead, we chose to estimate parallel models predicting a neutral response to
the question under consideration. In other words, we estimated the probability that
a respondent chose to answer the question non-neutrally. In most cases, given the
small number of people answering neutrally, the best estimate was simply the sample
mean. Where neutral responses were more common, however, we were able to fit the
basic model described in Equation 3. Again, we chose our model of neutral response
through a predictive exercise on the training and test datasets. See Table 6 for details.
As a result, our final predictions are based on these two parallel models. The
best model of neutral response gives the probability that a respondent in our sam-
ple answers a question non-neutrally. And the main models described above give
the probability that a respondent, having answered non-neutrally, gives a punitive,
anxious or mistrustful response.62 In other words,
Pr(P|S) = Pr(P|N N, S)×Pr(N N |S) (6)
where Pr(P|N N, S) is the probability of giving a punitive, anxious, or mistrustful
response if the respondent is sampled and answered not neutrally, and Pr(NN |S) is
the probability of giving a not neutral response if the respondent was in the sample.
D.4 Questions
Here we list all the questions for which we collected data The responses to these ques-
tions were obtained either from the American National Election Studies, the General
Social Survey, or through the Roper Center for Public Opinion Research. As discussed
in the paper, the proportion punitive (or anxious or mistrustful) was calculated as
the number of respondents answering punitively divided by the number who gave
clear-cut answers. For this reason, next to each question we list the responses we
counted as punitive (or anxious or mistrustful), neutral, and not punitive.
Punitiveness
1. Courts Not Harsh Enough (GSS): In general, do you think the courts
in this area deal too harshly or not harshly enough with criminals?
(P: Not Harsh Enough; NP: Too Harsh; N: About Right, Don’t Know)
2. Favor Death Penalty (GSS): Do you favor or oppose the death penalty
for persons convicted of murder?
(P: Favor ; NP: Opposed; N: Don’t Know)
62. As this implies, these main models are thus fit only on the subset of respondents answering
non-neutrally.
AP-12

3. Favor Death Penalty (Gallup): Are you in favor of the death penalty
for a person convicted of murder?
(P: Favor ; NP: Oppose; N: No Opinion, Don’t Know)
4. Prefer Death Penalty (Gallup): If you could choose between the
following two approaches, which do you think is the better penalty for
murder–the death penalty or life imprisonment, with absolutely no possi-
bility of parole?
(P: Prefer Death Penalty; NP: Prefer Life Without Parole; N: Neither,
Either/It Depends, DK/Refused)
5. Favor Death Penalty (ABC): Do you favor or oppose the death penalty
for persons convicted of murder?
(P: Favor Death Penalty; NP: Oppose Death Penalty; N: Don’t Know, No
Opinion, It Depends (Vol.))
6. Courts Not Harsh Enough (Gallup): In general, do you think the
courts in your area deal too harshly, or not harshly enough with criminals?
(P: Not Harsh Enough; NP: Too Harsh; N: About Right, Don’t Know, No
Opinion)
7. Favor Death Penalty (Time): Do you favor or oppose the death penalty
for individuals convicted of serious crimes, such as murder?
(P: Favor ; NP: Oppose; N: Not Sure)
8. Use Force (ANES): There is much discussion about the best way to
deal with the problem of urban unrest and rioting. Some say it is more
important to use all available force to maintain law and order – no matter
what results. Others say it is more important to correct the problems
of poverty and unemployment that give rise to the disturbances. Where
would you place yourself on this scale, or haven’t you thought much about
this? (1. Solve problems of poverty and unemployment ... 7. Use all
available force.)
(P: 5 to 7 ; NP: 1 to 3; N: 4)
9. More Prisons and Police (Gallup): Which of the following approaches
to lowering the crime rate in the United States comes closer to your own
view–do you think more money and effort should go to attacking the social
and economic problems that lead to crime through better education and
job training or more money and effort should go to deterring crime by
improving law enforcement with more prisons, police, and judges?
(P: Improving Law Enforcement; NP: Social and Economic Problems; N:
Don’t Know/Refused, Both (Vol.), Neither (Vol.))
10. Stop Crimes Regardless (ANES): Some people are primarily con-
cerned with doing everything possible to protect the legal rights of those
accused of committing crimes. Others feel that it is more important to
AP-13

stop criminal activity even at the risk of reducing the rights of the accused.
Where would you place yourself on this scale, or haven’t you thought much
about this? (1. Protect rights of accused ... 7. Stop crimes regardless of
rights of accused)
(P: 5 to 7 ; NP: 1 to 3; N: 4)
11. Death Penalty Deters (Gallup): Do you feel that the death penalty
acts as a deterrent to the commitment of murder, that it lowers the murder
rate, or not?
(P: It Does Deter; NP: It Doesn’t Deter; N: Don’t Know, No Opinion)
12. Favor Death Penalty (Roper): (Frequently on any controversial issue
there is no clear cut side that people take, and also frequently solutions
on controversial issues are worked out by compromise. But I’m going to
name some different things, and for each one would you tell me whether
on balance you would be more in favor of it, or more opposed to it?)...
Imposing the death penalty on those convicted of serious crimes such as
murder, kidnapping, etc.
(P: Favor ; NP: Opposed to; N: Mixed Feelings, Don’t Know)
13. Favor Harsher Sentencing (Roper): (Frequently on any controversial
issue there is no clear cut side that people take, and also frequently solu-
tions on controversial issues are worked out by compromise. But I’m going
to name some different things, and for each one would you tell me whether
on balance you would be more in favor of it, or more opposed to it?)...
Harsher prison sentences for those convicted of crimes.
(P: Favor ; NP: Opposed to; N: Mixed Feelings, Don’t Know)
14. More Important to Punish (Gallup): In dealing with those who are in
prison, do you think it is more important to punish them for their crimes,
or more important to get them started ’on the right road’?
(P: Punish Them; NP: Get Started Right; N: No Opinion)
15. Prefer Death Penalty (ABC): Which punishment do you prefer for
people convicted of murder: the death penalty or life in prison with no
chance of parole?
(P: Prefer Death Penalty; NP: Prefer Life in Prison; N: Don’t Know, No
Opinion)
16. Favor Crime Bill (Gallup): Do you favor or oppose the crime bill which
Congress recently passed?
(P: Favor ; NP: Oppose; N: Don’t Know/Refused)
Crime Anxiety
1. Too Little on Halting Rising Crime (GSS): (We are faced with many
problems in this country, none of which can be solved easily or inexpen-
sively. I’m going to name some of these problems, and for each one I’d like
AP-14

you to tell me whether you think we’re spending too much money on it,
too little money, or about the right amount.) e. Halting the rising crime
rate.
(A: Too Little Money; NA: Too Much Money; N: About Right, Don’t Know )
2. Too Little on Law Enforcement (GSS): (We are faced with many
problems in this country, none of which can be solved easily or inexpen-
sively. I’m going to name some of these problems, and for each one I’d like
you to tell me whether you think we’re spending too much money on it,
too little money, or about the right amount.) e. Law enforcement.
(A: Too Little Money; NA: Too Much Money; N: About Right, Don’t Know )
3. Spend More Halting Crime (Roper): (Turning now to the business
of the country–we are faced with many problems in this country, none of
which can be solved easily or inexpensively. I’m going to name some of
these problems, and for each one I’d like you to tell me whether you think
we’re spending too much money on it, too little money, or about the right
amount) Halting the rising crime rate–are we spending too much, too little,
or about the right amount on halting the rising crime rate?
(A: Too Little; NA: Too Much; N: About Right)
4. Spend More on Crime (ANES): If you had a say in making up the
federal budget this year, for which (1986 and after: of the following) pro-
grams would you like to see spending increased and for which would you
like to see spending decreased: Should federal spending on dealing with
crime be increased, decreased, or kept about the same?
(A: Increased; NA: Decreased or Cut Entirely; N: Same, Don’t Know)
5. Feel Inadequately Protected (Time): Do you feel adequately pro-
tected by the police from being the victim of a crime?
(A: Yes; NA: No; N: Not Sure)
6. Worry About Crime (Time): Is being a victim of crime something you
personally worry about, or not?
(A: Yes; NA: No; N: Not Sure)
7. Spend More on Police (GSS): (Listed below are various areas of gov-
ernment spending. Please indicate whether you would like to see more or
less government spending in each area. Remember that if you say ”much
more,” it might require a tax increase to pay for it.) c. The police and law
enforcement.
(A: Spend More, Spend Much More; NA: Spend Less, Spend Much Less;
N: Spend Same, Can’t Choose)
8. Worry About Crime (CBS): How much of the time do you worry about
being the victim of a crime — a lot of the time, some of the time, hardly
ever, or never?
AP-15

(A: A lot of the time, Some of the time; NA: Never, Hardly ever ; N:
NA/Don’t Know)
9. Too Little on Reducing Crime (GSS): (We are faced with many prob-
lems in this country, none of which can be solved easily or inexpensively.
I’m going to name some of these problems, and for each one I’d like you to
tell me whether you think we’re spending too much money on it, too little
money, or about the right amount.) e. Reducing crime.
(A: Too Little Money; NA: Too Much Money; N: About Right, Don’t Know )
Mistrust
1. No Confidence in Police (Gallup): (Now I am going to read you a list
of institutions in American society. Please tell me how much confidence
you, yourself, have in each one–a great deal, quite a lot, some, or very
little?) How about the police?
(M: Some, Very Little, None (Vol.); NM: A Great Deal, Quite A Lot; N:
Don’t Know/Refused)
2. No Confidence in Criminal Justice (Gallup): (Now I am going to
read you a list of institutions in American society. Please tell me how much
confidence you, yourself, have in each one–a great deal, quite a lot, some,
or very little?) How about the criminal justice system?
(M: Some, Very Little, None (Vol.); NM: A Great Deal, Quite A Lot; N:
Don’t Know/Refused)
3. Cold Toward Police (ANES): (There are many groups in America that
try to get the government or the American people to see things more their
way. We would like to get your feelings towards some of these groups. I
have here a card on which there is something that looks like a thermome-
ter. We call it a ”feeling thermometer” because it measures your feelings
towards groups. Here’s how it works. If you don’t know too much about a
group or don’t feel particularly warm or cold toward them, then you should
place them in the middle, at the 50 degree mark. If you have a warm feel-
ing toward a group or feel favorably toward it, you would give it a score
somewhere between 50 degrees and 100 degrees, depending on how warm
your feeling is toward the group. On the other hand, if you don’t feel very
favorably toward some of these groups–if there are some you don’t care for
too much–then you would place them somewhere between 0 degrees and
50 degrees.) Policemen/the police.
(M: 0 to 49 ; NM: 51 to 100; N: 50 )
4. No Confidence in Legal System (Roper): (Now, taking some specific
aspects of our life, we’d like to know how confident you feel about them.
First, do you feel very confident, only fairly confident, or not at all confident
that: we can on the whole depend on the justice of our legal system?
AP-16

(M: Not at all confident; NM: Very confident; N: Only fairly confident,
Don’t Know)
5. No Confidence in Police Protection (Gallup): How much confidence
do you have in the ability of the police to protect you from violent crime–a
great deal, quite a lot, not very much, or none at all?
(M: None At All, Not Very Much; NM: A Great Deal, Quite A Lot; N:
Don’t Know/Refused)
6. No Respect for Police (Gallup): How much respect do you have for
the police in your area – a great deal, some, or hardly any?
(M: Hardly Any; NM: A great deal; N: Some )
7. Police Have Been Brutal (Gallup): In some places in the nation,
there have been charges of police brutality. Do you think there is any
police brutality in your area, or not?
(M: Yes; NM: No; N: Don’t Know/Refused)
8. Police Not Honest (Gallup): (Please tell me how you would rate the
honesty and ethical standards of people in these different fields–very high,
high, average, low or very low?) How about...police officers?
(M: Low, Very Low; NM: High, Very High; N: Average, Don’t Know/Refused)
9. No Confidence in Courts (GSS): (How much confidence do you have
in...) e. Courts and the legal system
(M: Very Little Confidence, No Confidence At All ; NM: Complete Confi-
dence, A Great Deal of Confidence; N: Some Confidence, Don’t Know)
10. No Confidence in Conviction (Gallup): How much confidence do you
have in the ability of courts to convict and properly sentence criminals?
(M: None, Not Much; NM: Great Deal, Quite A Lot; N: Don’t Know )
11. Police Not Honest (NBC): How would you rate the honesty and ethical
standards of police officers?
(M: Low, Very Low ; NM: High, Very High; N: Average, Don’t Know/Not
Sure)
AP-17

Table 6: Questions in Public Opinion Dataset
Polls Resp. Black Resp. Coverage Neutrals Pr(P) Pr(NN)
Courts Not Harsh Enough (GSS) 30 53,548 7,325 1972-2014 19.4 C S
Favor Death Penalty (GSS) 30 55,216 7,666 1972-2014 6.62 S S
Favor Death Penalty (Gallup) 28 43,059 4,069 1956-2013 8.95 C S
Prefer Death Penalty (Gallup) 13 12,476 1,510 1985-2014 10.4 C S
Favor Death Penalty (ABC) 8 9,884 930 1981-2006 5.75 S µ
Courts Not Harsh Enough (Gallup) 7 13,911 1,478 1965-1993 32.8 S µ
Favor Death Penalty (Time) 6 4,781 569 1989-2003 5.75 S S
Use Force (ANES) 6 8,388 848 1968-1992 23.4 S S
More Prisons and Police (Gallup) 5 5,224 370 1989-1994 7.58 S S
Stop Crimes Regardless (ANES) 5 9,815 949 1970-1978 30.6 C S
Death Penalty Deters (Gallup) 3 4,081 595 1985-1991 7.38 S S
Favor Death Penalty (Roper) 3 5,960 652 1978-1984 17.5 C S
Favor Harsher Sentencing (Roper) 3 5,958 653 1978-1984 14.5 C S
More Important to Punish (Gallup) 3 4,117 367 1955-1989 9.55 C S
Prefer Death Penalty (ABC) 3 3,091 381 2003-2006 33.2 S S
Put Criminals Away (LAT) 3 4,433 421 1993-1995 14.5 N/A µ
Criminals Cannot Rehabilitate (LAT) 2 3,007 284 1993-1994 4.02 N/A µ
Favor Crime Bill (Gallup) 2 2,033 142 1994-1994 19.2 M S
More Prisons and Police (LAT) 2 2,942 276 1994-1995 8.09 N/A µ
Too Little on Halting Rising Crime (GSS) 29 34,527 4,677 1973-2014 29.7 M S
Too Little on Law Enforcement (GSS) 20 21,456 3,102 1984-2014 39.0 C S
Spend More Halting Crime (Roper) 15 28,925 3,167 1971-1987 29.3 S S
Spend More on Crime (ANES) 9 20,454 3,064 1984-2012 32.2 S S
Feel Inadequately Protected (Time) 5 4,336 330 1989-1997 3.04 M µ
Worry About Crime (Time) 5 4,336 330 1989-1997 0.71 S S
Spend More on Police (GSS) 4 4,744 601 1985-2006 39.5 M S
Worry About Crime (CBS) 2 2,067 182 1994-2012 0.24 S µ
Too Little on Reducing Crime (GSS) 1 484 55 1984-1984 29.1 S S
No Confidence in Police (Gallup) 22 22,618 1,905 1993-2014 0.43 S S
No Confidence in Criminal Justice (Gallup) 21 21,607 1,818 1993-2014 0.99 M S
Cold Toward Police (ANES) 7 11,988 1,207 1966-1992 9.69 C S
No Confidence in Legal System (Roper) 7 13,161 1,328 1973-1983 52.7 C µ
No Confidence in Police Protection (Gallup) 6 6,533 763 1985-1999 1.18 C S
No Respect for Police (Gallup) 6 10,900 1,095 1965-1999 25.7 S S
Police Have Been Brutal (Gallup) 6 11,247 1,820 1965-1999 10.9 C S
Police Not Honest (Gallup) 5 5,111 461 2009-2013 31.9 S S
No Confidence in Courts (GSS) 3 4,008 517 1991-2008 51.5 C S
No Confidence in Conviction (Gallup) 2 2,244 185 1985-1989 2.36 S S
Police Not Honest (NBC) 2 2,426 400 1985-1995 47.9 N/A µ
1Questions are ordered by the three dimensions we identify: punitiveness, anxiety, and mistrust.
2‘Pr(P)’ and ‘Pr(NN )’ describe the models we fit to predict the probabilities of a punitive, anxious
or mistrustful response and a non-neutral response, respectively. C refers to the complex model, M
to the middling model, and S to the simple model (N/A means that none of these models fit, and so
the question is omitted from our estimates). µrefers to the mean (only applicable when estimating
the probability of giving a non-neutral response. ‘Neutrals’ gives the proportion of respondents
giving neutral responses out of all those in the sample.
18

Table 7: Results of Panel Unit Root Tests
TiTest Unit Root
Incarceration Rate 51 LLC No (0.00)
IPS No (0.00)
Madwu Yes (0.98)
Hadri Yes (0.00)
Officer Rate 42 LLC No (0.00)
IPS No (0.00)
Madwu No (0.00)
Hadri Yes (0.00)
Corrections Spending 49 LLC No (0.00)
IPS No (0.00)
Madwu No (0.01)
Hadri Yes (0.00)
Police Spending 49 LLC No (0.00)
IPS Yes (0.71)
Madwu No (0.00)
Hadri Yes (0.00)
Black Political Representation (%) 41 LLC No (0.00)
IPS No (0.00)
Madwu No (0.00)
Hadri Yes (0.00)
Violent Crimes per 100,000 51 LLC No (0.00)
IPS No (0.00)
Madwu No (0.00)
Hadri Yes (0.00)
Black Population (%) 42 LLC No (0.00)
IPS No (0.00)
Madwu No (0.00)
Hadri Yes (0.00)
GDP per capita (Log) 51 LLC No (0.00)
IPS No (0.00)
Madwu Yes (0.07)
Hadri Yes (0.00)
Growth Rate 51 LLC No (0.00)
IPS No (0.00)
Madwu Yes (0.07)
Hadri Yes (0.00)
Income Inequality 51 LLC Yes (0.24)
IPS No (0.00)
Madwu Yes (0.41)
Hadri Yes (0.00)
Tax Collection 39 LLC Yes (0.35)
IPS No (0.00)
Madwu Yes (0.53)
Hadri Yes (0.00)
Punitiveness (Enns) 51 LLC Yes (0.39)
IPS Yes (0.35)
Madwu No (0.00)
Hadri Yes (0.00)
19

Table 8: Test Details
Abbreviation Reference H0HA
Hadri Hadri 2001 All panels are stationary Panels are stationary
IPS Im, Pesaran and Shin 2003 All panels contain unit roots Some panels contain unit roots
LLC Levin, Lin and Chu 2002 Panels contain unit roots Some panels are stationary
Madwu Maddala and Wu 1999 All panels contain unit roots At least one panel is stationary
Table 9: Results from Panel Regressions: Unit Root Specifications
Incarceration Rate Officer Rate Corrections Spending
Lagged Dep. Vars
∆ Incarceration Ratet−10.116*
(0.057)
∆ Incarceration Ratet−20.031
(0.028)
Officer Ratet−10.568**
(0.071)
Officer Ratet−20.235**
(0.021)
Officer Ratet−30.116+
(0.067)
Officer Ratet−4-0.069*
(0.030)
Corrections Spendingt−10.820**
(0.020)
Short-Run Impact
Black Political Representation (%)t−10.001 0.863*-0.006+
(0.502) (0.425) (0.004)
Democratic Controlt−10.549 -0.004 -0.004
(0.439) (0.261) (0.003)
Violent Crimes per 100,000t−11.591** 0.897** 0.006
(0.582) (0.294) (0.004)
∆ GDP per capita (Log)t−1-2.432 -2.094 0.054
(2.134) (2.033) (0.034)
∆ Growth Ratet−1-0.574 2.237 0.037
(2.864) (2.086) (0.024)
∆ Income Inequalityt−1-1.462 1.152 0.008
(2.065) (1.550) (0.012)
∆ Tax Collectiont−11.378** 0.594*0.014**
(0.435) (0.235) (0.003)
Black Population (%)t−1-0.800 -0.509 0.001
(0.570) (0.361) (0.003)
∆ Punitiveness (Enns)t−1-5.774 -14.896 -0.059
(8.301) (9.313) (0.103)
Long-Run Multiplier
Black Political Representation (%) 0.009 5.749*-0.033+
(0.591) (2.589) (0.020)
Violent Crimes per 100,000 1.887** 5.971** 0.033
(0.697) (1.722) (0.022)
∆ Tax Collection 1.600** 3.972*0.076**
(0.528) (1.813) (0.020)
∆ Punitiveness (Enns) -6.432 -99.940+-0.347
(9.866) (67.248) (0.568)
Model Info
Observations 1802 1764 1813
States 49 49 49
Range 1972-2008 1973-2008 1972-2008
Avg. Ni36.8 36 37
State FE Yes Yes Yes
Year FE Yes Yes Yes
Lags of DV 2 4 1
Adj. R20.184 0.875 0.911
20