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Abstract

The positive correlation between gun prevalence and homicide rates has been widely documented. But does this correlation reflect a causal relationship? This study seeks to answer the question of whether more guns cause more crime, and unlike nearly all previous such studies, we properly account for the endogeneity of gun ownership levels. We discuss the three main sources of endogeneity bias - reverse causality (higher crime rates lead people to acquire guns for self-protection), mismeasurement of gun levels, and omitted/confounding variables - and show how the Generalized Method of Moments (GMM) can provide an empirical researcher with both a clear modeling framework and a set of estimation and specification testing procedures that can address these problems. A county level cross-sectional analysis was performed using data on every US county with a population of at least 25,000 in 1990; the sample covers over 90% of the US population in that year. Gun ownership levels were measured using the percent of suicides committed with guns, which recent research indicates is the best measure of gun levels for cross-sectional research. We apply our procedures to these data, and find strong evidence of the existence of endogeneity problems. When the problem is ignored, gun levels are associated with higher rates of gun homicide; when the problem is addressed, this association disappears or reverses. Our results indicate that gun prevalence has no significant net positive effect on homicide rates: ceteris paribus, more guns do not mean more crime.
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No. 5357
GUN PREVALENCE, HOMICIDE
RATES AND CAUSALITY:
A GMM APPROACH TO
ENDOGENEITY BIAS
Tomislav Kovandzic,
Mark E Schaffer and Gary Kleck
PUBLIC POLICY
ISSN 0265-8003
GUN PREVALENCE, HOMICIDE
RATES AND CAUSALITY:
A GMM APPROACH TO
ENDOGENEITY BIAS
Tomislav Kovandzic, University of Alabama at Birmingham
Mark E Schaffer, Heriot-Watt University and CEPR
Gary Kleck, Florida State University
Discussion Paper No. 5357
November 2005
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Copyright: Tomislav Kovandzic, Mark E Schaffer and Gary Kleck
CEPR Discussion Paper No. 5357
November 2005
ABSTRACT
Gun Prevalence, Homicide Rates and Causality: A GMM Approach
to Endogeneity Bias*
The positive correlation between gun prevalence and homicide rates has been
widely documented. But does this correlation reflect a causal relationship?
This study seeks to answer the question of whether more guns cause more
homicide, and unlike nearly all previous such studies, we properly account for
the endogeneity of gun ownership levels. We discuss the three main sources
of endogeneity bias – reverse causality (higher crime rates lead people to
acquire guns for self-protection), mis-measurement of gun levels, and
omitted/confounding variables – and show how the Generalized Method of
Moments (GMM) can provide an empirical researcher with both a clear
modeling framework and a set of estimation and specification testing
procedures that can address these problems. A county level cross-sectional
analysis was performed using data on every US county with a population of at
least 25,000 in 1990; the sample covers over 90% of the US population in that
year. Gun ownership levels were measured using the percent of suicides
committed with guns, which recent research indicates is the best measure of
gun levels for cross-sectional research. We apply our procedures to these
data, and find strong evidence of the existence of endogeneity problems.
When the problem is ignored, gun levels are associated with higher rates of
gun homicide; when the problem is addressed, this association disappears or
reverses. Our results indicate that gun prevalence has no significant net
positive effect on homicide rates: ceteris paribus, more guns do not mean
more homicide.
JEL Classification: C51, C52 and K42
Keywords: counties, crime, endogeneity, GMM, gun levels and homicide
Tomislav V. Kovandzic
Department of Justice Sciences
University of Alabama at Birmingham
UBOB 210
1530 3rd Avenue South
Birmingham, Alabama 35294-4562
USA
Email: tkovan@uab.edu
For further Discussion Papers by this author see:
www.cepr.org/pubs/new-dps/dplist.asp?authorid=163631
Mark E Schaffer
Centre for Economic Reform
and Transformation, Dept of
Economics
Heriot-Watt University
Riccarton
EDINBURGH
EH14 4AS
Tel: (44 131) 451 3494
Fax: (44 131) 451 3294
Email: m.e.schaffer@hw.ac.uk
For further Discussion Papers by this author see:
www.cepr.org/pubs/new-dps/dplist.asp?authorid=110682
Gary Kleck
College of Criminology& Criminal
Justice
Florida State University
Tallahassee
Florida 32306-1127
USA
Email: gkleck@mailer.fsu.edu
For further Discussion Papers by this author see:
www.cepr.org/pubs/new-dps/dplist.asp?authorid=163630
*We are grateful to seminar audiences in Edinburgh, Moscow and Aberdeen
for helpful comments and suggestions. The usual caveat applies.
Submitted 02 November 2005
1. Introduction
As is well known, guns are heavily involved in violence in America, especially homicide. In
2002, 63.4 percent of homicides were committed by criminals armed with guns (U.S. Federal Bureau of
Investigation 2002, p. 23). Probably an additional 100,000 to 150,000 individuals were medically treated
for nonfatal gunshot wounds (Kleck, 1997, p. 5; Annest et al., 1995). Further, relative to other
industrialized nations, the United States has higher rates of violent crime, both fatal and nonfatal, a larger
private civilian gun stock (about 90 guns of all types for every 100 Americans), and a higher fraction of
its violent acts committed with guns (Killias, 1993; Kleck, 1997, p. 64). These simple facts have led many
to the logical conclusion that America's high rate of gun ownership must be at least partially responsible
for the nation's high rates of violence, or at least its high homicide rate (e.g., Sloan et al., 1990; Killias,
1993; Zimring and Hawkins, 1999).
1
This belief in a causal effect of gun levels on violence rates, and not
merely on criminals' choice of weaponry, has likewise inclined some to conclude that limiting the
availability of guns would substantially reduce violent crime, especially the homicide rate (e.g., Clarke
and Mayhew, 1988, p. 106).
While there is a considerable body of individual-level research relevant to these questions
(summarized in Kleck, 1997), macro-level research on the possible links between gun availability and
homicide is also essential to assessing these assumptions. This is true partly because it is obviously useful
to have multiple approaches to testing a given hypothesis. Perhaps more importantly, macro-level analysis
enables estimation of the net effects of community gun availability on homicide rates. While gun
possession among aggressors in violent incidents may serve to increase the probability of a victim’s
death, gun possession among victims may reduce their chances of injury or death. Individual-level
research (e.g. Kleck and McElrath, 1990; Kleck and DeLone, 1993; Tark and Kleck 2004) can assess such
effects of gun use in crime incidents, but it is less useful for detecting deterrent effects of gun ownership
among prospective victims. Because criminals usually cannot visually distinguish people carrying
1
Detailed studies using cross-national data are, however, generally unsupportive of this conclusion, and suggest
instead that there is no significant association between national gun ownership rates and rates of homicide, suicide,
robbery, or assault (Kleck, 1997, p. 254; Killias, van Kesteren, and Rindlisbacher, 2001, pp. 436, 440).
1
concealed weapons from other people, or residences with gun-owning occupants from other residences,
deterrent effects would not be limited to gun owners, and might not even differ between owners and
nonowners (Kleck, 1988; Kleck and Kates, 2001, pp. 153-154; Lott, 2000). Because the protective effects
of gun ownership may spill over to nongun owners, the aggregate net impact of homicide-increasing and
homicide-decreasing effects of gun availability can be quantified only through macro-level research.
Such macro-level studies must, however, take account of a number of potential pitfalls. The most
important of these are reverse causality in the guns-crime relationship, errors in and validation of
measures of gun prevalence, and omitted and confounding variables.
First, gun levels may affect crime rates, but higher crime rates may also increase gun levels, by
stimulating people to acquire guns, especially handguns, for self-protection. At least ten macro-level
studies have found effects of crime rates on gun levels (Kleck, 1979; Bordua and Lizotte, 1979;
Clotfelter, 1981; McDowall and Loftin, 1983; Kleck, 1984; Magaddino and Medoff, 1984; Kleck and
Patterson, 1993; Southwick, 1997; Duggan, 2001; Rice and Hemley, 2002), and individual-level survey
evidence (not afflicted by simultaneity problems) directly indicates that people buy guns in response to
higher crime rates (summarized in Kleck, 1997, pp. 74-79). Alternatively, higher violent crime rates,
especially gun crime rates, could discourage some people from owning guns, by reminding them of the
dangers of guns.
Thus, causality in the guns-crime relationship may run in either or both directions. If such a
simultaneous relationship exists, but analysts fail to take account of it using appropriate methods, their
results will be almost meaningless. What is asserted to be the impact of gun levels on crime rates will in
fact also include the impact of crime rates on gun levels. Indeed, in their estimations the crime=>guns
relationship could quantitatively dominate the guns=>crime relationship, in which case the analysts will
misinterpret an effect of crime on gun levels as an effect of gun levels on crime.
Second, direct measurement of gun levels is subject to well-documented problems (Kleck, 2004),
and many researchers have responded by using a diverse set of proxy measures. At the most basic level,
researchers must either validate their chosen proxy against other measures – i.e., establish that it is
correlated with other measures of gun levels – or rely on the validation investigations of others. Even a
2
valid proxy will, however, still suffer from measurement error. Measurement error can lead to biased
estimates of the impact of gun levels on crime. Again, unless appropriate variables and methods are used,
the analyst may commit either Type I or Type II errors when testing whether gun levels have an impact
on crime rates.
Third, analysts must be aware of and take measures to accommodate possible confounding
variables. Omitted variable bias is a particular problem for macro-level studies of the guns-crime
relationship. Omission of confounding variables that are known to be correlated with both gun prevalence
and crime rates (e.g., poverty and unemployment) will contaminate any estimate of the impact of gun
levels on crime. Investigators need at least to include an appropriate range of controls, and ideally should
adopt estimation methods that address the problem of confounding variables that are unobservable (e.g.,
“social capital”).
This study seeks to answer the question of whether there is a causal effect of gun levels on
violence rates. Unlike nearly all previous such studies, we properly account for the endogeneity of gun
ownership levels. We set out a formal analysis of the main sources of endogeneity bias, and discuss how
an empirical researcher can address these problems using estimation and specification testing procedures
in a Generalized Method of Moments (GMM) framework for a linear model. A county-level cross-
sectional analysis was performed using data on every U.S. county with a population of at least 25,000 in
1990. Gun ownership levels were measured using the percent of suicides committed with guns, which
recent research indicates is the best measure of gun levels for cross-sectional research. Our estimation
techniques allow us to address the problems of reverse causality, measurement error and unobservable
confounding variables, and we include a wide range of controls in our estimations.
The paper is organized as follows. Section 2 formalizes the three sets of problems discussed
above – reverse causality, mismeasurement of gun ownership levels, and omitted/confounding variables –
using a simple modeling framework, and discusses how to address these problems. Section 3 critically
reviews the macro-level research on the gun-homicide relationship in light of these three sets of problems.
Section 4 sets out a GMM-based estimation strategy and describes the tests to be used, and Section 5
3
discusses the data and the specific estimation strategy used in this study. The results are presented in
Section 6, and Section 7 concludes.
2. Reverse Causality, Mismeasurement, and Confounding Variables
Consider a researcher who wants to estimate the impact of gun availability on the homicide rate.
The researcher has available cross-sectional data on localities (we consider the potential alternative of
longitudinal data in the next section). The researcher estimates the following simple linear model using
ordinary least squares,
hom
i
= β
0
guns
i
+ β
1
control
i
+ u
i
(1)
where, in self-evident notation, hom
i
is the homicide rate in locality i, guns
i
is the level of gun ownership,
control
i
is a variable that controls for some characteristic of locality i, u
i
is the error term for the homicide
equation, and for expositional convenience the constant term is suppressed. The key parameter of interest
to the researcher in equation (1) is β
0
, the impact of gun levels on the homicide rate. What are the
potential pitfalls facing this estimation strategy?
Reverse causality
Say, for the moment, that equation (1) is well-specified, but also that it captures only part of the
picture – causality in the guns-crime relationship also runs from crime to guns. In equation (2),
guns
i
= γ
0
hom
i
+ γ
3
X
i
+ u
gi
(2)
gun levels are influenced both by homicide rates – we expect γ
0
>0, i.e., people buy guns in response to
higher crime rates – and by some other covariate X.
If the researcher estimates (1) by OLS, but the true set of relationships is captured by (1) and (2)
together, then the estimated
will not be “consistent” – it will suffer from “endogeneity” or
“simultaneity” bias.
0
β
ˆ
2
The reason is that the regressor guns is itself endogenous in a system of
2
The term “bias” is used here as a shorthand for “asymptotic bias”, i.e., the difference between the probability limit
(as the sample size goes to infinity) of an estimator and the true value of the parameter. An estimator is “consistent”
if its asymptotic bias is zero. IV/GMM estimators are in general unbiased only asymptotically. See e.g., Hayashi
(2000), pp. 94-5 and chapter 3.
4
simultaneous equations, making it correlated with the error term u
i
in (1). In this case, will be biased
upwards by the positive γ
0
β
ˆ
0
. Indeed, if the reverse causality is strong enough, i.e., γ
0
is large relative to β
0
,
the researcher could find that
>0 and conclude that more guns means more crime even if the true
impact of guns on crime is negligible or negative.
0
β
ˆ
The standard answer to this problem is to estimate equation (1) using the method of instrumental
variables (IV) or the more modern framework of GMM. This requires the researcher to have a variable
that is correlated with guns (“instrument relevance”) and that is also uncorrelated with the error term u
i
in
the homicide equation (“instrument validity”). The covariate X is potentially such a variable because it
appears in equation (2) as a determinant of gun levels, but is excluded from equation (1) (hence the term
“exclusion restriction”). Note that even if equation (2) is misspecified and itself suffers from endogeneity
or other problems, the researcher can still obtain consistent estimates of the parameters of equation (1) so
long as X satisfies these requirements.
Measurement and mismeasurement of gun levels
Let us maintain the assumption that equation (1) is a well-specified description of the impact of
guns on homicide rates. Say also that there is no reverse causality issue – homicide levels have no impact
on the propensity of people in the locality to acquire guns, i.e., γ
0
=0. However, the level of gun ownership
cannot be measured exactly, and the researcher must make use of a proxy. Instead of estimating
equation (1), the researcher estimates equation (1a),
hom
i
= b
0
prox
i
+ b
1
control
i
+ u
i
(1a)
again by OLS. The (unobservable) relationship between guns and prox is given by equation (3):
prox
i
= δ
0
guns
i
+ u
pi
(3)
where the term u
pi
is the measurement error that degrades the proxy.
The consequences of measurement error for the OLS estimate
depend on the nature of u
0
b
ˆ
pi
. If it
is a textbook case of purely random measurement error, then the estimated relationship between the gun
proxy and homicide will be biased towards zero. It is also possible, however, that the proxy for guns is
5
itself endogenous, via its direct dependence on an endogenous guns or some other route that generates a
correlation between prox and u
i
.
3
If so, the researcher faces an endogeneity bias problem as well, and the
net bias on the OLS estimate
can be positive or negative.
0
b
ˆ
The researcher must in any case bear in mind that the coefficient b
0
is not the quantitative impact
of gun levels on crime rates; this is given by b
0
δ
0
, and of course δ
0
is typically not observed directly. A
test of the estimated
may enable the researcher to say if there is a statistically significant non-zero
impact of guns on crime; but without an estimate of δ
0
b
ˆ
0
, the researcher will be unable to say anything
about the practical significance of the impact.
The usual approach when employing a proxy subject to measurement error is threefold. First, the
researcher needs to validate the proxy against other, albeit imperfect, measures of gun availability.
Second, estimating equation (1a) using IV/GMM techniques will generate a consistent estimate
,
assuming that instruments for guns are available that satisfy the conditions of relevance and validity.
Third, if the estimated coefficient on the guns proxy
is significantly different from zero, the researcher
will have a qualitative estimate of the impact of guns on crime; but s/he must also have some idea of the
magnitude of δ
0
b
ˆ
0
b
ˆ
0
(e.g., from a validation exercise) in order to obtain a quantitative estimate of the impact.
Omitted/confounding variables
Now let us abandon the assumption that equation (1) is a well-specified description of the impact
of guns on homicide rates. The true relationship is one in which there is an additional characteristic of
localities that determines of homicide rates, confound, as shown in equation (1b):
hom
i
= β
0
guns
i
+ β
1
control
i
+ β
2
confound
i
+ u
i
(1b)
Say again that there is no reverse causality issue. Gun levels are, however, also influenced by the variable
confound, as in equation (2a):
guns
i
=
γ
2
confound
i
+ γ
3
X
i
+ u
gi
(2b)
3
For example, omitted variable bias as discussed below could also operate via a confounder that is omitted from the
homicide and proxy equations.
6
If the researcher estimates the original equation (1) using OLS, the estimated will again be
biased. This time, the endogeneity bias is an omitted variable bias. The absence of confound from the
estimated homicide equation (1) and its role as a determinant of guns in equation (2b) means that guns
will be correlated with the error term in (1). In other words, omitting confound from the homicide
equation makes guns an endogenous regressor.
0
β
ˆ
How to address this problem depends on whether the omitted variable is observable. If confound
is a variable that is available to the researcher, then equation (1b) may be estimated using OLS; the
researcher simply includes it alongside control as a second control variable. Often, however, confounding
variables are unobservable (e.g., pro-violence subcultural norms or social capital) and hence cannot be
included as explicit regressors. In this case, the standard approach would be the same as that for the
reverse causality problem: estimate (1) using IV/GMM, with the covariate X as the excluded instrument.
Specification testing
In all three sets of problems discussed above – reverse causality, measurement error, and
omitted/confounding variables – IV/GMM methods can, in principle, enable the researcher to avoid the
biases that would contaminate the OLS estimate of the impact of guns levels on homicide rates. Given the
mass of empirical evidence and theoretical considerations cited above, the natural starting point of the
researcher should be that these biases are likely to be present and that IV or GMM estimation is the
appropriate technique.
For the results to have any credibility, the IV specification should be both plausible and subject to
rigorous testing. The ex ante exclusion restrictions that identify the model must be consistent with prior
theory and evidence – here, the exclusion of the covariate X from the homicide equation and its presumed
correlation with guns or prox. For example, in a model of burglary rates, the percent of an area’s
population that resides in rural areas should not be omitted if prior research and theory indicates that this
variable influences burglary rates (e.g., Cook and Ludwig 2003, pp. 106-107). The ex post specification
7
testing should include tests of both instrument relevance and, if the model is overidentified,
4
instrument
validity; the latter test is sometimes called a test of overidentifying restrictions.
Although the presumption of the researcher should be that OLS estimates are likely to be biased,
the possibility that these biases are small or negligible cannot be ruled out. If this is indeed the case, then
guns (or prox) can be treated as an exogenous regressor, and estimation by OLS would be preferred to IV
because it is the more efficient (lower variance) estimator. The standard approach to this question is to
conduct a test of the endogeneity of guns. Such a test relies implicitly on a comparison of an estimation in
which guns is treated as exogenous and one in which it is treated as endogenous. For the test to have any
meaning, it is therefore essential that the OLS estimation be contrasted with a well-specified IV
estimation.
Summary
The discussion above indicates that macro-level investigations of the guns-homicide relationship
need to take account of a range of potential pitfalls. Both the empirical evidence and standard practice
suggest that the starting point should be the presumption of possible reverse causality, measurement error,
and omitted variables. We can summarize the basic requirements and procedures for addressing these
pitfalls as follows:
1. The researcher requires a proxy for gun levels that has been properly validated against other
available measures.
2. One or more instruments for guns is required. Any such instrument needs to satisfy the two
requirements of instrument validity and instrument relevance.
3. Instrument validity means an instrument should be exogenous in the econometric sense of the
term, i.e., uncorrelated with the error term in the homicide equation. Prior reasoning should also
suggest that the variable has no direct impact on homicide rates, i.e., that the variable is properly
excluded from the homicide equation. If the researcher has more than one instrument available
and the model is overidentified, then the validity of the instruments can and should be tested and
the results reported.
4. Instrument relevance means an instrument should be plausibly correlated with gun levels. The
relevance should be tested and results reported.
4
I.e., the number of excluded instruments exceeds the number of endogenous regressors.
8
5. If gun levels are to be considered exogenous, such a specification should be supported by a
properly conducted endogeneity test that uses a comparison with a well-specified IV/GMM
estimation, i.e., one that uses instruments for guns that are both relevant and valid. Testing for the
endogeneity of guns by comparing OLS to a misspecified IV estimation cannot provide evidence
that OLS is acceptable.
6. The homicide equation should include a reasonably full set of control variables, so as to reduce
the problem of omitted variables and confounding factors.
In the next section, we use these criteria to review the macro-level studies that investigate the
guns-homicide relationship.
3. Prior Research
Table 1 summarizes macro-level studies of the impact of gun ownership levels on crime rates.
Many of these studies found a significant positive association between crime or violence rates and some
measure of gun ownership, but all of these studies share at least one, and usually several, of the
methodological problems we have outlined (see Kleck, 1997, Chapter 7 for a more extensive review of
the pre-1997 research). The studies are also commonly characterized by small samples and other
problems, but it is the flaws in measurement and modeling that are most clearly consequential.
Invalid measurement of levels and changes in gun ownership
Table 1 (see note b) shows that past macro-level guns-violence studies have used a large and
diverse set of proxies for gun levels. With few exceptions (e.g., Cook, 1979; Kleck and Patterson, 1993),
researchers using these measures failed to validate them using any criterion, such as establishing that they
correlate well with more direct survey measures of gun prevalence. The validity of over two dozen of
these measures has recently been systematically assessed by measuring correlations between the proxies
and direct survey measures (Kleck, 2004). The results indicate that most of the measures used in prior
cross-sectional research and all of those used in time-series or pooled cross-section studies have poor
validity. The best indicator of gun levels was the percent of suicides committed with guns (PSG), which
correlated strongly (with correlations ranging between 0.85 to 0.95) with direct survey measures across
cities, states, and nations.
9
Despite its excellence as an indicator of cross-sectional variation in gun levels, PSG has no
validity whatsoever as a cross-temporal indicator. Kleck (2004, p. 24) demonstrated that not only do
changes in PSG fail to strongly correlate with direct survey measures of changes in gun prevalence over
time; PSG actually generally has weak negative correlations with these criterion measures. Further, Kleck
found that none of the measures used in past research or any of the rest of the two dozen indicators he
assessed were valid measures of cross-temporal variation in gun levels (pp. 20-21). The implication for
the potential alternative approach of longitudinal analysis is clear: unless some new, heretofore unknown
proxies are developed that are valid indicators of gun trends, meaningful longitudinal analysis of the
impact of gun levels on violence rates is impossible.
The recent study by Moody and Marvell (2005) illustrates this. The authors generated a state-
level panel dataset covering 1977-98 by combining direct survey measures of gun levels taken from the
General Social Surveys (GSS) with imputed values based on PSG. Their analysis used both IV methods
and Granger causality tests to detect whether changes in gun levels led to changes in violence rates or
visa-versa. This use of direct survey measures of gun levels fails, however, because (a) some states
contribute few or no respondents to the GSS sample in a given year, (b) the GSS asked gun ownership
questions in only 17 of the 22 years analyzed, and (c) since only about 1,400 people are asked the gun
questions in a typical year (not 3,000, as the authors report), GSS samples for any one state in any one
year average only about 29. As a result, random sampling and response error could easily account for
virtually all observed cross-temporal variation in the state gun prevalence figures; indeed, it is unlikely
that any of the year-to-year changes in state gun prevalence are statistically meaningful.
This becomes apparent if we examine and extend the validation exercise the authors use to justify
imputing missing state-level GSS data on percent of households with a gun (HHG) or handgun (HHGG)
for a given year using state-level data on PSG;
5
the exercise is crucial to their study since imputation of
missing HHG and HHGG observations effectively doubles their estimation sample. The authors report
that in their state-level panel, PSG is highly correlated with both HHG and HHGG, and much more
5
The data were downloaded from http://cemood.people.wm.edu/research.html.
10
correlated than alternative proxies such as gun magazine subscriptions. What the authors fail to note is
that this correlation is driven entirely by the cross-sectional correlation between PSG and the GSS gun
measures; the cross-temporal correlations are tiny. This can be easily seen by examining separately the
cross-sectional and cross-temporal correlations of HHG and PSG using their data. The left-hand panel of
Figure 1 shows that state-average PSG and state-average HHG are highly correlated – the correlation
coefficient is 0.83 and statistically highly significant. The right-hand panel, on the other hand, shows that
the correlation of annual changes (first-differences) in state PSG and state HHG is essentially nil – the
correlation coefficient is 0.06 and statistically insignificant. Note also that the very small GSS state
sample sizes mean that most of the annual changes in GSS state-level gun prevalence are implausibly
large (the standard deviation is 18). Since the authors’ analysis is based entirely on cross-temporal
variation in HHG/HHGG
6
with missing values imputed from the cross-temporal variation in PSG, their
null findings on the guns/crime link are not surprising. The authors were essentially modeling noise in the
gun data, and their analysis says little about the merits of the guns-cause-crime hypothesis.
7
Figure 1: PSG and General Social Survey HHG, State-level Data 1977-98
r = 0.8311
30
40
50
60
70
80
PSG
Average Level 1977-98
0
20
40
60
80
GSS HHG
Average Level 1977-98
r = 0.0589
-10
0
10
20
PSG
Annual Changes 1977-98
-100
-5 0
0
50
GSS HHG
Annual Changes 1977-98
6
The estimations are either in first-differences or in levels with fixed effects; in the latter case, the fixed effects
absorb all the between-state variation and leave only the within-state (cross-temporal) variation in crime levels to be
explained by the corresponding variation in guns.
7
The authors try in the paper to address the issue of attenuation bias with a calibration exercise, but they
underestimate the scale of the bias by calibrating to the wrong gun measure (gun levels, instead of changes in gun
levels as used in their regressions.)
11
In sum, with the exception of the few studies that used PSG, indexes including PSG, or direct
survey measures in cross-sectional research (e.g., Cook, 1979; Kleck and Patterson, 1993), the supposed
gun-crime associations estimated in nearly all past research are uninterpretable on the simple grounds that
gun levels were not actually measured.
Many measures have flaws that go beyond merely being imperfect indicators of gun levels.
Measures such as the percent of homicides (or robberies, or aggravated assaults) committed with guns are
vulnerable to the possibility of artifactual associations with crime rates. For example, Hemenway and
Miller (2000) used Cook’s (1979) “gun density” index, which is the average of (1) the percent of
homicides committed with guns, and (2) PSG. The reason for the significant associations found between
the Cook measure and homicide rates across 26 nations (and the absence of such when just PSG was
used), is that both national homicide rates ([gun homicides + nongun homicides]/population) and the
percent of homicides committed with guns ([gun homicides/total homicides] x 100%) contain a common
component in their numerators: the number of gun homicides. In other words, the “gun density” index is
endogenous: when used as a proxy for gun levels, u
p
, the error term that degrades the proxy in
equation (3), is correlated by construction with the homicide rate hom, and hence with u, the error term in
the homicide equation (1). Had the authors employed instrumental variables or a related technique, they
might, in principle, have been able to obtain unbiased estimates. But of course the better approach,
regardless of estimation technique employed, is to use a proxy that is not biased by construction.
The “percent of crimes with a gun” proxy has another flaw. This indicator reflects not only the
availability of guns but also the preference of the criminal population for using guns (Brill, 1977, pp. 19-
20). While availability certainly affects how often criminals use guns, the “lethality” of offenders, i.e.,
their willingness to inflict potentially lethal injury on others, affects weapon choice as well – criminals
willing to use lethal weapons are also more willing to inflict lethal injury (Cook, 1982, p. 248; Wright and
Rossi, 1983, pp. 189-211). Consequently, these macro-level indicators can confound gun availability with
the average lethality of the criminal population, producing guns/homicide associations that are virtual
tautologies, reflecting nothing more than the truism that populations that are more lethal are more likely
12
to commit lethal acts. Here we have an example in which the same problem can be described as either
measurement error or omitted variable bias. Average lethality is an omitted and unobservable variable
(confound in equation (1b)), and is also a component of the measurement error that degrades the proxy (u
p
in equation (3)). Again, this problem can be countered using instrumental variable estimation techniques,
but again, it is preferable to use a better proxy whatever the estimation technique employed.
Finally, virtually all studies using a proxy for gun levels have failed to calibrate the proxy used to
a survey-based measure of gun prevalence. That is, they failed to adjust for the fact that there is not
necessarily a one-to-one correspondence between the gun proxy and actual gun levels. Moody and
Marvell (2003) showed that the failure of two such studies (Duggan, 2000; Cook and Ludwig, 2003) to
calibrate their proxy led the authors to make claims of policy relevance that were simply unfounded.
Endogeneity and reverse causality
Most guns-violence studies do nothing whatsoever to deal with this problem (e.g., Hemenway
and Miller, 2000; Killias, 1993; Miller, Azrael, and Hemenway, 2002). Table 1 shows that of 31 total
studies, twenty had no research design features that would help the analyst distinguish the possible
positive effects of gun levels on crime rates from the possible positive effects of crime rates on gun levels.
Three studies (Southwick, 1999; Duggan, 2003; Moody and Marvell, 2005) used the weaker notion of
Granger causality, in which longitudinal data are used to establish whether past gun levels help predict
current crime rates, but their findings are uninterpretable for the reasons cited above: there are no useable
longitudinal data on gun levels that have been shown to be reliable enough for statistical analysis.
Of the 10 studies that attempted to address the causality problem using a structural approach,
eight clearly failed because they used inappropriate methods, e.g., estimating unidentified models. This
means that if crime rates do influence decisions to acquire guns, the findings of all but a handful of prior
studies (e.g., Kleck and Patterson, 1993) are uninterpretable on the grounds that the statistical models on
which they were implicitly based were unidentified. Even the studies that did estimate identified models
using appropriate techniques failed to report tests of instrument relevance and instrument validity, a
problem that we might label “underreporting” of structural causality methods.
13
Hoskin (2001), for example, estimated a simultaneous equations model of homicide rates and gun
availability across 36 nations, but the model was almost certainly underidentified. The exclusion
restrictions used to identify the model were arbitrary and implausible (indeed, he never made them
explicit), and directly contradicted the author’s own theoretical assertions.
8
Nor did Hoskin report any
tests of instrument validity that would indicate their adequacy, or provide a discussion of the requirement
of instrument relevance.
The Stolzenberg and D’Alessio (2000) study is another example of the underreporting problem.
They used an appropriate test for endogeneity, the Hausman test, to support a specification of a crime
equation in which gun levels is treated as exogenous, but the meaning of their test is doubtful (p. 1475).
The test’s utility depends crucially on the specification of the IV estimation in which gun levels are
instrumented, and these authors did not report what instrumental variables they used, let alone whether
they passed tests of validity and relevance. As a result, it is impossible to place any confidence in their
Hausman test results, and therefore in the conclusions they draw from their estimated crime equation.
Omitted/confounding variables
Most studies also use minimal or no controls for possible confounding variables. As a point of
reference, Kleck and Patterson (1993, pp. 259-260) controlled for as many as 36 potential confounders,
beyond their gun level measure and 19 dummy variables representing gun laws. In contrast, Cook and
Ludwig’s (2003) county-level instrumental variable analysis included just three control variables (beyond
county and year dummies), Hoskin (2001, p. 586) included just three controls in his homicide equation,
and Hemenway and Miller (2000) did not control for a single confounding variable in their homicide
models.
Due to uncertainty about exactly which macro-level attributes of places affect crime rates, it is
impossible to know exactly which variables in a guns-violence study might be confounding variables, i.e.,
8
To achieve identification in his homicide equation, Hoskin excluded (1) population density, (2) the percent of the
population that was male and aged 15 to 34 (p. 584), and (3) an East Asia dummy. Yet just a few pages earlier he
had asserted, quite plausibly, that the first two of these variables should affect homicide rates, and his discussion of
the third is limited to the remark that both homicide and firearms ownership rates are low in East Asia (pp. 580-1).
14
factors that affect crime rates but are also correlated with gun levels or gun control laws. That is, it is
uncertain which variables might either generate spurious associations among these variables or suppress
or distort genuine causal effects. The consequences of failing to control confounders can be quite serious
– biased parameter estimates – while the consequences of wrongly including irrelevant variables are more
mild – somewhat inflated standard errors of coefficients. Thus, the most sensible procedure is to control
for as many likely and observable crime determinants as is reasonable, within the limits imposed by
sample size and assuming that multicollinearity does not preclude doing so, and to employ IV/GMM
techniques in order to address the problem of unobservable and hence omitted confounders.
4. IV/GMM, Instrument Validity, and Instrument Relevance
In this section we outline an estimation strategy using modern econometric techniques and GMM
methods in particular. GMM can be applied to nonlinear as well as linear problems; we use a linear model
for simplicity of exposition as well as ease of implementation. We begin by illustrating the two
requirements of instrument validity and instrument relevance in the simplest version of model (1). There
is a single explanatory variable, guns,
hom
i
= β
0
guns
i
+ u
i
(1c)
and a single excluded instrument, X. The standard IV estimator of β
0
is =
0
ˆ
β
iii
gunsXhomX
i
.
The proof that
is a consistent estimator of β
0
ˆ
β
0
is straightforward:
0
ˆ
plimβ
)plim(
ii
= gunsXhomX
ii
))(plim(
0
+β=
iiiii
gunsXugunsX
)plim(
i0
+β=
iii
gunsXuX
)plim()plim(
N
1
i
N
1
0
+β=
iii
gunsXuX
. This will be equal
to β
0
if the second term is zero, which will be the case if X satisfies two conditions. First, if E(X
i
u
i
)=0 (X
is uncorrelated with the error term; validity), then
0plim
N
1
=
ii
uX
. Second, if E(X
i
guns
i
)0 (X is
correlated with guns; relevance), then
0plim
N
1
ii
gunsX
. Both of these are “moment conditions”;
they relate to statistical moments of guns, X and u.
15
A modern and increasingly popular approach to the problem of estimation with endogenous
regressors is the Generalized Method of Moments or GMM (Hansen, 1982).
9
GMM provides a unified
framework for estimation and testing that is naturally suited to empirical problems where endogeneity and
instrument validity are central. The issue of instrument relevance is one that has attracted a great deal of
econometric research in recent years and new findings are appearing regularly. Nevertheless, there are
enough established results to provide empirical researchers with some practical guidelines for how to
detect and address problems of instrument relevance.
Estimation, testing and instrument validity in the Generalized Method of Moments
As its name implies, GMM is a generalization of the method of moments (MM), a much older
technique introduced by Karl Pearson in 1894. The essence of MM is straightforward. The researcher has
theoretical priors which imply theoretical or population moments, i.e., characteristics of the population
that are implied by the researcher’s model. The researcher also has data available, and can calculate
sample moments using these data. The sample moments depend not only on the data, but also on the
unknown parameters of the model that the researcher wants to estimate. The researcher’s estimates of the
parameters are the values that make the sample moments match the assumed population moments.
We use model (1c) to illustrate MM estimation. There is a single explanatory variable, guns. The
researcher also has a single theoretical moment condition, namely that the variable X is exogenous: it is
orthogonal to, i.e., uncorrelated with, the error term u, E(X
i
u
i
)=0. This is referred to as an “orthogonality
condition”. Note that the researcher has not imposed any priors about the exogeneity of guns; in
particular, by choosing E(X
i
u
i
)=0 as the single theoretical orthogonality condition, the researcher is
allowing for the possibility that that guns may be endogenous, i.e., E(guns
i
u
i
)0. The MM estimate of the
parameter β
0
, is the value that makes the sample moment corresponding to E(X
0
ˆ
β
i
u
i
)=0 also equal to
zero. The sample counterpart to the error term u
i
is the residual, defined in the usual way as
9
The literature on GMM is now vast and many good expositions are available. Wooldridge (2001) provides an
easily accessible introduction to GMM and its applications. Hayashi (2000) is an advanced text that sets out many of
the tests and results used and cited in this paper. Baum et al. (2003) set out the basics of IV and GMM estimation
and specification testing, and describe the set of extended Stata estimation and testing routines used here.
16
i0ii
ˆ
ˆ
gunshomu β
. The sample moment condition is therefore that the sample mean of ( ) is
zero, i.e.,
ii
uX
ˆ
0
ˆ
N
1
=
ii
uX
. This is just one equation in one unknown, i.e., the model is exactly identified.
To solve the equation for
we substitute for the residual to obtain
0
ˆ
β
0)
ˆ
(
0i
N
1
=β
gunshomX
i
, and
after simplifying and rearranging, we have the MM estimate of the impact of guns on homicide:
=β
iii
gunsXhomX
i0
ˆ
. The MM estimator in this single-regressor model allowing for possible
endogeneity of guns is, in fact, the standard IV estimator.
The above illustrates two features of MM which carry over to GMM and which make the method
attractive to empirical researchers and to users of their work. First, many commonly used estimators are
special cases of GMM estimators, and the apparatus of GMM can be used with these estimators. Both IV
and OLS, for example, are GMM estimators. Second, the MM/GMM approach makes very clear what the
assumptions of the researcher are. Thus estimating model (1) above with two regressors using OLS is
equivalent to using MM with two theoretical orthogonality conditions, namely E(guns
i
u
i
)=0 and
E(control
i
u
i
)=0. These conditions must hold – both guns and the control variable must be exogenous – if
consistent estimates of the parameters β
0
and β
1
are to be obtained in this way. If either theoretical
orthogonality condition does not hold, then the estimates of both parameters will be inconsistent.
A natural question is, what if there are more orthogonality conditions than there are parameters to
be estimated? Say that the researcher wants to estimate (1), believes that control (but not guns) is
exogenous, and has two more variables, X1 and X2, that s/he believes are also exogenous. (In the
terminology of IV estimation, control is an “included instrument” and X1 and X2 are “excluded
instruments”.) This gives three orthogonality conditions, E(control
i
u
i
)=0, E(X1
i
u
i
)=0 and E(X2
i
u
i
)=0,
but still only two parameters to estimate, β
0
and β
1
. Because the model is overidentified – there are three
sample moment equations but only two unknowns – in general it will be impossible to find estimates of β
0
and β
1
that set the sample moment conditions exactly to zero.
In GMM, estimates of β
0
and β
1
are chosen such that the three sample moment conditions are as
“close” to zero as possible. More precisely, GMM proceeds by defining an objective function J(.) that is a
function of the data, the parameters and a set of weights in a weighting matrix W. The GMM objective
function is a quadratic form in the sample moment conditions, i.e., the sample moment conditions are
17
weighted using the weights in W and summed to produce a scalar that is minimized. J(.) can be thought of
as the “GMM distance” – the distance from zero, which is the value the objective function would take if
all the sample moment conditions were satisfied – and the definitions of the GMM estimators of β
0
and β
1
are those values that minimize J given W and the data.
There are as many different GMM estimators as there are different possible Ws to use in J, and in
fact any GMM estimator using a non-trivial W will generate consistent estimates of the parameters.
Where GMM comes into its own is when an optimal weighting matrix is chosen. The optimal GMM
weighting matrix is the inverse of the covariance matrix of moment conditions S; in our example, the
variances and covariances of (control
i
u
i
), (X1
i
u
i
) and (X2
i
u
i
). GMM estimation with an optimal
weighting matrix has the following features. First, when S
-1
is used as the optimal weighting matrix, the
GMM estimator is efficient, i.e., it has the smallest asymptotic variance. Although the true covariance
matrix S is unknown, it can be easily estimated in a prior step,
10
and the two-step GMM estimator that
uses the estimated
as the weighting matrix is also efficient. Second, more orthogonality conditions
mean more efficient estimation, as long as the additional orthogonality conditions are satisfied. Third,
efficient GMM readily accommodates forms of errors that are often encountered by empirical researchers
in social science: heteroskedasticity, autocorrelation, and clustering (spatial correlation). Thus if the
estimated
is robust to arbitrary heteroskedasticity, i.e., heteroskedasticity of unknown form, the
efficient GMM estimator that uses
as the weighting matrix will be efficient in the presence of
arbitrary heteroskedasticity, and the GMM standard errors of the parameters will be robust to arbitrary
heteroskedasticity. The same applies to autocorrelation and clustering. This robustness to arbitrary
violations of homoskedasticity and independence is appealing to empirical researchers, not least because
it means obtaining valid estimation results does not require a researcher to model these violations
explicitly and correctly.
1
S
ˆ
S
ˆ
1
S
ˆ
10
The reason that it is easy is that an estimate of S can be obtained from any consistent estimator of the equation.
The usual GMM estimator is therefore “two-step feasible efficient GMM”: (1) in the first step, some consistent but
possibly inefficient estimator of the parameters (e.g., IV) is used to obtain
S ; in (2) in the second step, is used
to minimize J and obtain the efficient GMM estimates of the parameters.
ˆ
1
S
ˆ
18
Fourth, and most importantly for this paper, efficient GMM provides a straightforward
framework for testing the validity of orthogonality conditions when the equation is overidentified, i.e.,
when there are more orthogonality conditions than there are parameters to be estimated. Under the null
hypothesis that the all the orthogonality conditions are valid – all the variables that were assumed to be
exogenous are indeed exogenous – the minimized value of J is distributed as χ
2
with degrees of freedom
equal to the degree of overidentification.
11
This test of overidentifying restrictions is known in the
literature as the Hansen or Sargan-Hansen J statistic and is, conveniently, an automatic by-product of
GMM estimation.
Note that the orthogonality condition corresponding to an excluded instrument may fail because
the exclusion restriction itself is invalid. Say the model of equation (1) is misspecified in the sense that X1
should actually be an included exogenous regressor because it has a direct impact on homicide rates. If
the researcher estimates equation (1) and uses X1 and X2 as excluded instruments, X1 will be correlated
with the error term of (1), and the J statistic will be tend to be large, indicating a failure of orthogonality
conditions. In other words, the incorrect exclusion of X1 from equation (1) makes X1 endogenous.
The same framework can be used to test the validity of a subset of orthogonality conditions, i.e.,
to test whether or not selected instruments are exogenous. Consider the J statistic resulting from two
different efficient GMM estimations: J1 is the J statistic from an efficient GMM estimation that uses all
the moment conditions, and J2 is the J statistic from an efficient GMM estimation that does not use the
moment conditions corresponding to the suspect instruments (if the suspect variables are included
instruments, i.e., regressors, in the J2 estimation they are treated as endogenous; if they are excluded
instruments, in the J2 estimation they are not used at all). Under the null hypothesis that the suspect
variables are valid instruments, the quantity J1-J2 is distributed as χ
2
with degrees of freedom equal to the
number of instruments being tested. This test is known variously in the literature as a C test, a distance
GMM test, or a difference-in-Sargan test. It is important to note that for the C test to be valid, the
11
In the exactly-identified case, the minimized value of J is zero, and the orthogonality conditions cannot be tested.
19
orthogonality conditions corresponding to the instruments not being tested must also be valid, i.e., the J2
statistic (which is a test of the validity of these orthogonality conditions) should be small.
The GMM framework usefully encompasses and extends a number of older and well-known
procedures. For example, if the error term u is homoskedastic and independent:
12
(a) OLS is the efficient
GMM estimator when regressors are exogenous; (b) IV is the efficient GMM estimator when some
regressors are endogenous; (c) if regressors are exogenous, OLS is more efficient (has a lower variance)
than IV because it makes use of more orthogonality conditions;
13
(d) the J statistic for the IV estimator is
numerically identical to the Sargan’s (1958) NR
2
overidentification statistic;
14
(e) the Hausman-Wu test
for the endogeneity of regressors is numerically identical to the C test that uses the Sargan-Hansen J
statistics from IV and OLS estimations of a model. GMM provides a straightforward method to
generalizing the above estimators and tests to situations where homoskedasticity and/or independence do
not hold.
Useful as it is, GMM is not a panacea, and several caveats to its use should be mentioned. First,
the use of large numbers of orthogonality conditions in the form of excluded instruments can generate
finite sample bias problems, and the general advice here is to be parsimonious with excluded instruments.
Second, there is some evidence that the standard errors for some efficient GMM estimators may be biased
downwards in finite samples, i.e., testing coefficients may be prone to Type I errors. A conservative
estimation strategy adopted by some researchers is consequently to use inefficient GMM estimators (e.g.,
OLS or IV in the presence of heteroskedasticity), rely on robust standard errors for inference, and use the
efficient GMM J statistic for specification testing.
15
Third, Sargan-Hansen tests can have limited power,
i.e., may be prone to Type II errors, and a J or C test that fails to reject the null should be treated with
caution.
12
See Hayashi (2000) for details.
13
More precisely, when errors are homoskedastic and independent, the additional orthogonality conditions
corresponding to the endogenous regressors in IV improve the efficiency of OLS, and the conditions corresponding
to the excluded instruments in IV become redundant for OLS.
14
Basmann’s (1960) overidentification statistic is a close relative of, and asymptotically equivalent to, Sargan’s
statistic, and is also invalid when errors are not homoskedastic.
15
Thus Wooldridge’s (1995) robust overidentification statistic for IV estimation is numerically equal to the J
statistic for two-step efficient GMM (Baum et al. 2003).
20
The GMM procedure that our hypothetical researcher would employ for testing the exogeneity of
variables, and that we use below, is as follows:
1. Estimate equation (1) using the full set of four orthogonality conditions: E(guns
i
u
i
)=0,
E(control
i
u
i
)=0, E(X1
i
u
i
)=0 and E(X2
i
u
i
)=0, and obtain the J statistic for the efficient GMM
estimator. Allow for possible heteroskedasticity or spatial correlation if suggested by priors or
evidence from the data. (The corresponding efficient GMM estimator is due to Cragg (1983) and
is also known as HOLS, “heteroskedastic OLS”.) If the J statistic is large, take this as evidence
that one or more moment conditions is invalid, i.e., one or more of the four variables is
endogenous, and proceed to Step 2. If the J statistic is small, take this as evidence that the
orthgonality conditions are jointly valid – all the variables are exogenous. However, prior
research suggests that the assumption that guns is exogenous is questionable, so proceed to Steps
2 and 3.
2. Estimate equation (1) without the assumption that guns is exogenous, i.e., using the three
orthogonality conditions E(control
i
u
i
)=0, E(X1
i
u
i
)=0 and E(X2
i
u
i
)=0, and obtain the J statistic
for the efficient GMM estimator. Allow for possible heteroskedasticity or spatial correlation. If
the J statistic is small, take this as evidence that the moment conditions are valid – control, X1,
and X2 are all exogenous – and proceed to Step 3. If the J statistic is large, take this as evidence
that one or more of the remaining orthogonality conditions is invalid, i.e., either the control
variable or one of the excluded instruments is invalid, and stop – consistent estimation is not
possible.
3. Test whether guns is endogenous using a C test using J1-J2, where J1 is the J statistic using the
full set of orthogonality conditions (Step 1) and J2 is the J statistic that does not assume
exogeneity for guns. If the C statistic is small, take this as evidence that guns may be exogenous
along with the other variables, and proceed to Step 4. If the C statistic is large, take this as
evidence that guns is endogenous and go to Step 5.
4. (guns is exogenous) Consider estimating the equation by efficient GMM (i.e., HOLS) or OLS.
The former is consistent and efficient; the latter is consistent, but inefficient if errors are not
homoskedastic and independent. Alternatively, because of the danger of a Type II error and
because prior evidence and research suggests that gun levels may be subject to endogeneity bias
from various sources, treat guns as endogenous and go to Step 5.
5. (guns is endogenous) Estimate the equation by efficient GMM or by IV. The former is consistent
and efficient, but may be more prone to Type I errors; the latter is consistent, but inefficient if
errors are not homoskedastic and independent.
Instrument relevance and the weak instruments problem
As the simple IV example above showed, instrument relevance is another type of moment
condition required for an IV-type estimator to be consistent. The minimal relevance requirement is just
the rank condition for identification of the model; if the rank condition is not satisfied, the model is
unidentified. The intuition behind instrument relevance is simply that the excluded instruments must be
21
correlated with any endogenous regressors. If there are multiple endogenous regressors, measuring
instrument relevance is not straightforward because it requires estimation of the rank of the covariance
matrix of regressors and instruments.
16
In the case of a single endogenous regressor, however, the
recommendation in the literature is straightforward and easy to implement: the statistic for instrument
relevance is the F test of the excluded instruments in the “first-stage” regression, i.e.,
guns
i
=
θ
1
control
i
+ θ
3
X1
i
+ θ
4
X2
i
+ v
i
(4)
and the researcher examines θ
3
and θ
4
for their consistency with theory and prior evidence, and for their
joint significance using a standard F statistic; a large value indicates that the model is identified. If
heteroskedasticity or clustering is suspected, a heteroskedastic- or cluster-robust test statistic can be used.
The researcher should also examine the individual significance of both θ
3
and θ
4
in the estimation of the
first-stage equation (4). Adding instruments does not come without a cost; in particular, the finite sample
bias of the IV/GMM estimator is increasing in the number of instruments. If the first-stage regression
suggests that one instrument is strongly relevant and the other is irrelevant, the researcher should consider
dropping the irrelevant instrument.
17
An important practical problem arises if the excluded instrumental variables are correlated with
the endogenous regressor but only weakly. Recent research (e.g., Bound et al., 1995; Staiger and Stock,
1997; Stock et al. 2002 provide a survey) has shown that when instruments are weak, IV/GMM estimates
of parameters will be badly biased (in the same direction as OLS), estimated standard errors will be
unreliable, and therefore so will the Wald-based hypothesis tests and confidence intervals that use these
estimates; in particular, standard errors will be too small and the null will be rejected too often. This is an
area of ongoing research in econometrics, and guidelines for how to detect a “weak instrument” problem
are not yet well established. There is, however, a consensus that it is not enough for the first-stage F
16
Two statistics that have been suggested for this purpose are the Cragg-Donald statistic and Anderson’s canonical
correlations statistic. Both statistics require homoskedastic and independent errors to be valid. See Hall et al. (1996)
and Stock and Yogo (2002) for further discussion.
17
The formal approach would be to test the instrument for “redundancy”. An excluded instrument is redundant if the
efficiency of the estimation is not improved by its use. See Hall and Peixe (2000) for further discussion.
22
statistic to be significant at conventional levels of 5% or 1%; higher values are required. Staiger and Stock
(1997) recommend an F statistic of at least 10 as a rule of thumb for the standard IV estimator
.
18
If weak instruments are detected or suspected, recent research suggests two possible approaches.
The investigator may use an estimator that is relatively robust to weak instruments. These estimators are
often non-standard and not widely available in commercial software packages, they may not be robust to
heteroskedasticity or clustering, their performance in the presence of weak instruments is still being
explored, and so we do not go down this route here. The second approach is to employ a procedure for
construction of a confidence interval that is robust to weak instruments. Various such methods have been
proposed; see, e.g., Dufour (2003) and Andrews and Stock (2005). One method that is easy to implement
for the single-endogenous-regressor case using standard regression software packages is based on the
Anderson-Rubin (1949) test.
19
The method is as follows. Consider a specific hypothesized value
0
~
β
for the coefficient on guns
in model (1). Subtract the quantity
i0
~
gunsβ
from both sides of (1) and then substitute using (4) to obtain
])
~
[(
)
~
()
~
(])
~
[()
~
(
00
40030011000
ii
iiiii
uv
X2X1controlgunshom
+ββ+
θββ+θββ+β+θββ=β
(5)
If the null hypothesis H
0
:
00
~
β=β
is correct, both X1 and X2 will drop out, and equation (5) simplifies to
iiii
ucontrolgunshom +β=β
10
)( (6)
The AR test of the null hypothesis is therefore to estimate
iiiiii
ηX2X1controlgunshom +π+π+π=β
4310
)
~
(
(7)
and employ a standard F test of whether the coefficients on the excluded instruments π
3
and π
4
are indeed
both equal to zero. The AR test is suitable when a model is just-identified or the degree of
18
Stock and Yogo (2002) provide more detailed advice based on Monte Carlo studies, and show inter alia that the
Staiger-Stock rule of thumb is a reasonable guideline to follow for the single-endogenous-regressor case when the
number of excluded instruments is small.
19
Not to be confused with the Anderson-Rubin overidentification test, which is the test analogous to the Sargan-
Hansen J test for maximum-likelihood estimation.
23
overidentification is low, and it can easily be made heteroskedastic- or cluster-robust by using the
appropriate covariance estimator for (7).
20
Note that the AR test assumes that the orthogonality conditions
E(X1
i
u
i
)=0 and E(X2
i
u
i
)=0 are satisfied; if these did not hold, the AR test statistic would be significant,
not because
00
~
ββ
, but because the excluded instruments were correlated with the composite error term
η
i
. If either X1 or X2 is endogenous, the AR test is invalid.
An AR confidence interval is simply the region where the AR test fails to reject the null. For
example, an AR 95% confidence interval for the coefficient on guns β
0
would be the range of specific
values for
0
~
β
such that the AR test statistic is below the 5% critical value for the F distribution. An AR
confidence interval is fully robust to weak instruments, and the intuition for this is clear from inspection
of equations (5) and (7). Note that π
3
=
300
)
~
( θββ
and similarly for π
4
. If X1 and X2 are only weakly
correlated with guns, then θ
3
and θ
4
will be small, so will π
3
and π
4
, and a test of H
0
: π
3
=π
4
=0 can fail to
reject the null even if the hypothesized
0
~
β
is far from the true β
0
. Weak instruments will therefore tend to
widen the AR confidence interval for the impact of guns β
0
, i.e., low instrument relevance will be
properly reflected in the imprecision of the estimated impact of gun levels on homicide.
21
5. DATA, MODEL AND ESTIMATION STRATEGY
Data
To estimate the impact of gun availability on homicide rates, we use cross-sectional data for all
U.S. counties which had a population of 25,000 or greater in 1990, and for which relevant data were
available (N=1,462). These counties account for about half of all U.S. counties but over 90% of the U.S.
population in that year. The use of 1990 data is dictated by two factors. First, most of the control variables
included in the homicide equations to mitigate omitted variable bias are available at the county-level only
during census years. A second reason for choosing 1990 is the fact that the firearm crime rate (homicide,
robbery, and assault) had reached its highest level in nearly 30 years by 1990. It is reasonably argued that
20
The AR test loses power as the number of excluded instruments goes up. More powerful tests have recently been
proposed; see Andrews and Stock (2005) for a survey.
21
We calculate our AR confidence intervals with a simple grid search over possible values β
0
. Note that some care
in calculating AR confidence intervals may be needed in practice because the AR test can sometimes generate
confidence intervals that are either empty or disjoint. See Zivot et al. (1998).
24
if gun availability is responsible for higher homicide rates, the high levels of firearm crime in 1990 should
provide one of the best opportunities to date for testing the gun availability-homicide relationship.
County-level data were chosen for several reasons. First, the use of counties provides for a
diverse sample of ecological units, including urban, suburban, and rural areas. Second, counties are more
internally homogenous than nations, states, or metropolitan areas, thereby reducing potential aggregation
bias. Third, counties exhibit great between-unit variability in both gun availability and homicide rates,
which is precisely what gun availability and homicide research is trying to explain. Fourth, county data
provide a much larger sample than previous gun level studies, which have focused mainly on nations,
states, or large urban cities (almost all with 50 or fewer cases; see Table 1). The large sample size
provides us with greater statistical power to detect more modest effects of gun availability on homicide
rates, while still permitting us to enter numerous control variables in the homicide equations to minimize
omitted variable bias. A large sample size is particularly important when IV/GMM methods are used,
because these estimators are only consistent, i.e., bias approaches zero only as the sample size increases.
Model
We follow the convention for crime policy studies and use a linear model in which most variables
are specified in logs. The dependent variables in our model are the gun, nongun, and total homicide rates
per 100,000 county population. Homicide data for each county were obtained using special Mortality
Detail File computer tapes (not the public use tapes) made available by the National Center for Health
Statistics (U.S. NCHS 1997). The data include all intentional homicides in the county with the exception
of those due to legal intervention (e.g., police shootings and executions). Homicide rates are averages for
the seven years 1987 to 1993, thus bracketing the census year of 1990 for which data on many of the
control variables were available. Seven years were covered to reduce the influence of random year-to-
year aberrations, e.g., misclassification of homicides as other kinds of deaths such as suicides or
unintentional deaths, and to allow the use of rates in a linear model as an approximation for count data
(see below).
25
It is desirable to separately assess rates of homicide with and without guns, to provide sharper
tests of the hypothesis that gun levels affect homicide rates. The decision criteria upon which we rely for
determining whether gun levels causes a net increase in homicide rates are as follows. If the gun level has
a net positive impact on homicide rates, it should have (1) a significant positive association with the gun
homicide rate, (2) a significant positive association with the total homicide rate, and (3) be less strongly
positively correlated with the nongun homicide rate than with the gun homicide rate. On the other hand, if
gun levels are as strongly positively associated with nongun homicides rates as with gun homicide rates
(or more so), this suggests that the gun level is merely a correlate of some omitted variable that affects
homicide in general, but the gun level has no effect of its own, since there is no strong reason why gun
levels should increase the rate of homicides committed without guns. If (1) is true, but (2) is not, it would
generally indicate that gun availability merely shifts criminals from nongun weapons to guns, but has no
net effect on the number of people murdered. If (2) is true, but (1) is not, it suggests that gun levels are
merely associated with some omitted variables that have an effect on total homicide rates but that gun
levels themselves have no effect, since they should have their effects by, at minimum, increasing
homicides committed with guns.
In our main regressions, the crime rate variables are specified in logs. This poses some minor
problems, because even though we are using 7-year averages and excluding the smallest counties, a small
number of counties have zero murders: of the 1,462 counties in the sample, 20 had no gun murders (about
1% of the sample), 52 had no nongun murders (about 4%), and 3 had no murders at all. Our approach is to
report in detail the results using the logged crime rates and dropping the observations for which the
dependent variable is undefined. Histograms of the logged crime rates after dropping zero-crime-rate
counties are shown in Figure 2; simple visual inspection suggests no particular skewness or outlier
problems after log transformation.
26
Figure 2: Distributions of Log Crime Rates
0
1
2
3
4
5
6
Percent
-3
-2
-1
0
1
2
3
4
5
Log gun homicide rate
0
1
2
3
4
5
6
Percent
-3
-2
-1
0
1
2
3
4
5
Log non-gun homicide rate
0
1
2
3
4
5
6
Percent
-3
-2
-1
0
1
2
3
4
5
Log total homicide rate
To check the robustness of the results, we also estimated using a variety of transformations of the
dependent variable that do not require us to drop observations: (1) logged “add 1” crime rates, where the
number of murders for the 7-year period has 1 added to it; (2) “one-sided winsorized”
22
log crime rates,
where prior to taking logs the zero crime rate counties are assigned a crime rate equal to the lowest non-
zero-crime-rate county; (3) “two-sided winsorized” log crime rates, where the treatment of the zero crime
rate counties is as in (2), and the same number of the highest crime counties are, prior to logging, assigned
a crime rate equal to that of the next highest (i.e., the highest non-transformed) county; (4) raw crime
rates (murders per 1,000 population).
While it might be desirable to measure gun ownership levels directly using survey-based
estimates, surveys asking people directly whether they own guns are usually limited to a single large area,
such as a nation or state. Instead, we use the best indirect measure of gun availability for cross-sectional
research, the percent of suicides committed with guns (PSG). Some of the smaller counties typically have
few or no suicides in a given year, and misclassification of a few suicides as homicides or accidents in
small counties could produce substantial measurement error in a single year’s PSG. Therefore, as was
22
See the help file for the Stata command “winsor” by Nick Cox (2003) for a discussion of “winsorizing” and for
references to the relevant statistical literature.
27
done with homicide rates, PSG was computed for the 7-year period 1987 to 1993, bracketing the
decennial census year of 1990. Similar to homicide, data for the percent of suicides committed with guns
were obtained using special Part III Mortality Detail File computer tapes made available by the National
Center for Health Statistics. Unlike widely available public use versions, the tapes permit the aggregation
of death counts for even the smallest counties (U.S. NCHS 1997).
Figure 3 shows histograms of our gun proxy PSG in raw percentage form and after logging.
There are no problems of zeros here; rather, the issue is whether the skewness to the left seen in the
distribution of log PSG is of any concern. Our approach is to report detailed results using log PSG, and to
confirm robustness of the findings with regressions using PSG in raw percentage form.
Figure 3: Distributions of PSG and Log PSG
0
1
2
3
4
5
6
7
Percent
0
25
50
75
100
PSG
0
1
2
3
4
5
6
7
Percent
3
4
5
Log PSG
We also need to calibrate our proxy to available survey-based measures of gun levels. The most
convenient calibration is to the mean percentage of households with guns (HHG) according to the General
Social Surveys (GSS). National gun survey prevalence figures have been available since 1959, though not
for every year. The mean HHG for 1959-2003 is 44.2% while the mean PSG for 1959-2002 (the latest
year available) is 54.9%. These figures imply a value of 54.9/44.2=1.24 for the calibration factor δ
0
by
which we should inflate or deflate the estimated coefficient on PSG b
0
so as to obtain an estimate of β
0
,
the impact of gun levels on homicide rates (see equation 3). Neither PSG nor HHG varied greatly during
this period, and the use of a different reference period would matter little.
Using state-level measures from surveys conducted by the Centers for Disease Control (CDC) in
2002 (Okoro et al., 2005) and PSG data for 1995-2002 taken from CDC’s WONDER service, simple OLS
28
regressions (based on 50 states) of PSG and log PSG and the corresponding HHG and log HHG measures
are as follows (standard errors are in parentheses):
Log PSG = 2.31 + 0.481 Log HHG + e
(0.12) (0.035)
PSG = 30.11 + 0.706 HHG + e
(2.85) (0.069)
The coefficients on log HHG and HHG can be interpreted as estimates of the log-log and level-level
calibration δ
0
, respectively. The figures suggest that in our main log-log estimations, the coefficient on
log PSG should be approximately halved (δ
0
=0.481) in order to be interpreted as the HHG-homicide
elasticity. In a levels-levels estimation, the calibration should be in the neighborhood of 0.706 (based on
the 50 states regression) to 1.24 (based on national means). These are, however, only approximations
based on limited data and simple linear calibrations. A more cautious conclusion would be that PSG is,
within an order of magnitude, already calibrated to HHG, and that interpretations of the estimated
coefficient on gun levels will be most robust in the neighborhood of mean PSG.
In addition to the gun prevalence measure, we included numerous county-level control variables,
paying particular attention to those that prior theory and research suggest are important determinants of
both gun ownership levels and homicide rates. Failing to control for confounders that affect both gun
availability and homicide rates would generate an endogeneity bias in the coefficient on PSG, as
discussed earlier. Decisions as to which control variables to include in the homicide equations were based
on a review of previous macro-level studies linking homicide rates to structural characteristics of
ecological units (see Kleck, 1997, Chapter 3; Kovandzic et al., 1998; Land et al., 1990; Sampson, 1986;
Vieraitis, 2000 and the studies reviewed therein).
We were particularly concerned to control for variables that had opposite-sign associations with
gun levels and homicide rates because such variables could suppress evidence of any positive effect of
gun levels on homicide rates. Thus, we controlled for the percent of the population that is rural because
rural people are more likely to own guns, but less likely to commit homicide. Likewise, we controlled for
the poverty rate, the share of the population in the high-homicide ages of 18 to 24 and 25 to 34, and the
29
African-American share of the population because people in these groups are less likely to own guns, but
more likely to commit homicide, than other people (Kleck, 1997; Cook and Ludwig, 1997; U.S. FBI,
2000). The other controls used were percent Hispanic, population density, average education level,
unemployment rate, transient population (born out-of-state), vacant housing units, female-headed
households with children, median household income, households earning less than $15,000, and
inequality (ratio of households earning more than $75,000 to households earning less than $15,000).
The sets of controls for rurality and age structure are, exceptionally, used in percentage rather
than log form. Because the raw percentages sum to 100, including all categories would generate a perfect
collinearity problem, and so one category must be omitted. Using raw percentages therefore has the
appealing feature that the results are invariant to whichever percentage is the omitted category. We omit
the percentage rural and the percentage aged 65+.
The use of county-level data has an additional advantage: by including state fixed effects, i.e.,
state dummy variables, we are able to control for any unobserved or unmeasured county characteristics
that vary at the state level and that could be expected to influence both gun levels and homicide rates.
Examples of such confounders would be state laws and judicial practice relating directly or indirectly to
homicide and gun ownership, state-level resources devoted to law enforcement, and incarceration rates in
state prisons. Testing of the fixed effects in the estimations below strongly supported their inclusion as
controls.
23
The disadvantage of this approach is that only variables available at the county level can be
used in the estimations, because state-level measures would be perfectly collinear with the fixed effects.
24
We do not include explicit state dummies and instead use an estimation routine that obtains numerically
equivalent results by applying the “within” transformation to all variables, i.e., expressing them as
deviations from state means. The R
2
reported with the regressions is the “within R
2
”, and measures how
much of the within-state variation in homicide rates our models explain.
The key challenge in using IV methods is finding a source of identifying variation: here, variables
that are correlated with gun levels, but that are exogenous with respect to homicide and that a priori
23
F tests of the significance of the state fixed effects vs. a specification using a set of 9 regional dummies.
24
It also means that the single observation for Washington, D.C. drops out of the fixed-effects regressions.
30
reasoning and evidence suggest should be excluded from the homicide equation. The excluded
instrumental variables used in this paper are (1) an index (RGUNMAG) comprised of subscriptions to
each of the three most popular outdoor/sport magazines (Field and Stream, Outdoor Life, and Sports
Afield) in 1993, per 100,000 county population (Audit Bureau of Circulations, 1993), and (2) the percent
of the county population voting for the Democratic candidate in the 1988 Presidential election
(PCTDEM88). The gun magazine index was created using principal components analysis; the analysis
yielded a factor that explained 84 percent of the cumulative variance in this latent construct.
25
Both excluded instruments are theoretically important correlates of gun ownership that are
plausibly otherwise unrelated to homicide. RGUNMAG serves as a measure of interest in outdoor sports
such as hunting and fishing, or perhaps as a measure of a firearms-related “sporting/outdoor culture”
(Bordua and Lizotte, 1979). PCTDEM88 serves as a measure of political liberalism and hence should be
negatively correlated with gun ownership. The 1988 election results were chosen in preference to the
1992 results because the date precedes the census year from which most our data are taken (and hence is
more plausibly exogenous), and because the choice between the two main candidates in 1988 maps more
closely to attitudes towards gun ownership.
26
Prior research suggests that both variables are important
predictors of gun ownership (Kleck, 1997, pp. 70-72; Cook and Ludwig, 1997, p. 35).
Table 2 lists and provides a brief description of each variable used along with their means and
standard deviations. Data for the control variables were obtained from the U.S. Bureau of the Census,
County and City Data Book, 1994, except for PCTDEM88, which is from ICPSR (1995), and rurality,
which is from U.S. Census Bureau (2000).
Estimation strategy
The estimation and testing procedure we follow is the GMM approach outlined above in
Section 4. It is natural to expect the presence of heteroskedasticity in a cross-sectional dataset, and indeed
25
The factor had an eigenvalue of 2.52, well above the conventional threshold of 1.00. The loading scores for each
magazine were as follows: SPAFIELD (0.824), LIFE (0.968), and STREAM (0.948).
26
In the 1992 election, unlike the 1988 election, the politically less conservative candidate (negatively correlated
with gun ownership) was also a southerner (positively correlated with gun ownership). The 1992 results are also less
easily interpreted because of the significant share of the vote that went to the third-party candidate, Ross Perot.
31
application of the Pagan-Hall (1983) test for heteroskedasticity in IV estimation to our data suggests it is
present here. We therefore use GMM estimation that is efficient in the presence of arbitrary
heteroskedasticity.
An oft-neglected issue with cross-sectional data on locations is the potential problem of spatial
correlation. It is reasonable to suspect that observations in two physically adjacent counties are more
likely to have correlated disturbance terms than two counties at opposite ends of the state or country. If
spatial correlation is present, standard errors that assume independence are likely to be underestimated
and test statistics will be invalid. A straightforward method of addressing this in the GMM context is the
“cluster-robust” approach, where clusters are defined as groups of counties – here, states.
27
The
corresponding GMM estimator is efficient in the presence of both arbitrary heteroskedasticity and
arbitrary within-state correlation of the disturbance term, and requires only the assumption of
independence across states, which is a reasonable assumption given our fixed-effects specification. The
main drawback to this approach is that we have only 50 clusters (states), and hence relatively few degrees
of freedom. Most of our regressions have 18 exogenous regressors and 2 excluded instruments, leaving us
with effectively only 50-18-2=30 observations on clusters for calculating cluster-robust standard errors.
We therefore use the fixed-effects GMM estimator that is efficient in the presence heteroskedasticity for
our benchmark results, and report the results using the cluster-robust fixed-effects GMM estimator as a
check on the sensitivity of the findings to the presence of spatial correlation.
Our initial specification treats PSG as exogenous; it is the two-step efficient GMM estimator with
exogenous regressors that allows for arbitrary heteroskedasticity (Cragg’s HOLS estimator). The
corresponding J statistic is a test of the full set of orthogonality conditions, i.e., the exogeneity of PSG,
RGUNMAG and PCTDEM88 (plus the other covariates). Our second specification is the two-step
efficient GMM estimator that treats PSG as endogenous, and the J statistic is a test of the reduced set of
orthogonality conditions, i.e., the exogeneity of RGUNMAG and PCTDEM88 (again plus the other
covariates). The C statistic reported with the initial specification is a test of the endogeneity of PSG and is
27
See Wooldridge (2003) for an overview and discussion of the case where the number of groups is small.
32
based on the difference of the two J statistics.
28
We test for instrument relevance using a heteroskedastic
or cluster-robust F test of the joint significance of the excluded instruments RGUNMAG and PCTDEM88
in an OLS estimation of the first-stage equation of the gun proxy (PSG or log PSG), and we also examine
the significance of RGUNMAG and PCTDEM separately using conventional t-statistics. Because these
instruments are, in some specifications, bordering on weak, we also report an Anderson-Rubin confidence
interval for the coefficient on PSG, and, for comparison, the usual Wald-based confidence interval
employing the GMM-estimated standard error. The versions of these tests that we use are all
heteroskedastic- or cluster-robust; non-robust test statistics would tend to be biased upwards and lead to
Type I errors. Lastly, as a check on the sensitivity of the results, we also estimate the main equations
using the corresponding inefficient GMM estimators, OLS and IV. With the exception of the F test-based
AR confidence intervals, we report large-sample standard errors and significance tests; i.e., we do not
make a finite-sample adjustment for the number of explicit regressors, and we use the normal or χ
2
distributions for significance tests, p-values and confidence intervals.
29
The statistical package Stata was used for all estimations. The main IV/GMM estimation
programs, ivreg2 and xtivreg2, were co-authored by one of us (Schaffer), and can be freely downloaded
via the software database of RePEc.
30
For further discussion of how the estimators and tests are
implemented, see Baum, Schaffer and Stillman (2003) and (2005), and the references therein.
6. RESULTS
Estimation results for the benchmark regressions using the logged gun homicide rate as the
dependent variable are in Table 3. Columns 1 and 2 report the results of 2-step GMM estimations that are
efficient in the presence of arbitrary heteroskedasticity and that treat PSG as exogenous and endogenous,
respectively, along with heteroskedastic-robust standard errors and test statistics. Columns 3 and 4 report
28
The difference in reported J statistics is not exactly equal to the reported C statistic, because we use a version of
the latter that is guaranteed to be non-negative in finite samples. See Hayashi (2000) and Baum et al. (2003).
29
The heteroskedastic-robust variances and statistics have a degrees-of-freedom adjustment for the number of fixed
effects (50); the adjustment is not required for the cluster-robust variances. See Wooldridge (2002), pp. 271-75.
30
http://ideas.repec.org/SoftwareSeries.html. ivreg2 is a general-purpose IV/GMM estimation routine for linear
models; xtivreg2 supports fixed-effects panel data models.
33
the corresponding estimates that are efficient in the presence of heteroskedasticity and within-state
clustering, plus heteroskedastic- and cluster-robust standard errors and statistics.
We consider first the heteroskedatic-robust results in columns 1 and 2. Most of the parameter
estimates for the 18 control variables are significant, and the significant coefficients have the expected
sign in both specifications. High gun murder rates are associated with high population density, lower
education levels, and the various poverty, low-income and inequality measures. The percentage of the
population that is black is associated with high gun crime rates, as is the percentage Hispanic, but in the
latter case only in the first specification, when PSG is treated as exogenous. The only modest surprise is
provided by the age structure controls; contrary to expectations, the 18-24 age group was associated with
relatively low gun homicide rates,
31
though this is a common finding (Marvell and Moody 1991). The
overall fit of the regressions is quite good, with the PSG-exogenous specification explaining 44% of the
within-state variation in county-level log gun homicide rates, and the PSG-endogenous specification
explaining 33%.
The key results concern the coefficient on and the exogeneity of PSG. Column 1 shows that in the
efficient GMM estimation where log PSG is treated as exogenous, the variable has a coefficient of 0.290
and is statistically significant at the 5% level. This confirms the oft-reported result that, when endogeneity
issues are ignored, gun levels are associated with higher gun crime rates. When log PSG is treated as
endogenous and instrumented with RGUNMAG and PCTDEM88, the picture changes dramatically.
Column 2 shows that log PSG has a negative coefficient of –1.50 that is statistically significant at the 1%
level.
We now apply the GMM-based procedure outlined in Section 4 for testing the exogeneity of
PSG. [Step 1] The J statistic in column 1 is 13.3. This is very large for a χ
2
(2) statistic; the p-value is only
0.001. We therefore reject the null hypothesis that the orthogonality conditions in the PSG-exogenous
estimation are satisfied, and take this as strong evidence that one or more variables – log PSG,
RGUNMAG, PCTDEM88, and/or the control variables – are endogenous. [Step 2] The J statistic for the
31
The effect is comparable to that of the omitted category of 65+ and lower than those for the remaining categories.
34
PSG-endogenous estimation in column 2 is 0.25, which small for a χ
2
(1) statistic – the corresponding p-
value is 0.61. We therefore cannot reject the null that RGUNMAG, PCTDEM88, and the control
variables are exogenous; in other words, the evidence suggests that our instruments are valid. [Step 3] We
now test explicitly whether log PSG is endogenous using a C test based on the J statistics for the PSG-
exogenous and PSG-endogenous estimations. The C statistic reported in column 1 is 13.0.
32
This is very
large for a χ
2
(1) statistic; the p-value is only 0.0003. We therefore have strong evidence that log PSG is
endogenous, and that some form of IV/GMM estimation is required. Before we turn to this last estimation
[Step 5], however, we must also consider whether our excluded instruments RGUNMAG and
PCTDEM88 are relevant as well as valid.
The first-stage heteroskedastic-robust F statistic reported in column 2 is 26.2, well above the
Staiger-Stock rule-of-thumb level of 10. Both the excluded instruments are correlated with log PSG in the
expected directions and at the 0.1% significance level: counties voting Democrat in 1988 tend to have
fewer guns as proxied by log PSG, and subscriptions to outdoor magazines are associated with higher gun
levels. We conclude that our instruments in this estimation are relevant and not weak. Nevertheless, as a
check we also report a heteroskedastic-robust AR 95% confidence interval for log PSG. The AR
confidence interval is [–3.05 , –0.34] only slightly wider than the conventional Wald-based confidence
interval of [–2.52 , –0.48].
Having shown that the GMM estimation in column 2 satisfies the requirements of both validity
and relevance, we turn to the issue of calibration. The calibration exercise above suggests we should
roughly halve coefficient estimate of –1.50 to obtain the elasticity of gun homicide with respect to HHG,
i.e., about -0.75. The estimate is therefore not only statistically significant, it is potentially also practically
significant. We hasten to add, however, that this is a very approximate estimate: after calibration to HHG
and allowing for uncertainty in the calibration itself, both the conventional Wald and weak-instrument-
robust AR confidence intervals would include low (practically insignificant albeit statistically significant)
HHG-gun homicide elasticities. In sum, we have strong evidence that gun levels are endogenous, and
32
The C statistic differs slightly from the difference between the relevant J statistics because we use a version of the
C test that guarantees a positive test statistic. See Hayashi (2000) or Baum et al. (2003) for details.
35
when this is accounted for in the estimation, the positive association of gun levels with gun homicide
completely disappears; if anything, gun levels are associated with lower, not higher, gun homicide rates.
These findings are essentially unchanged if we allow for intra-state spatial correlation as well as
heteroskedasticity. When we treat log PSG as endogenous (column 4), the two-step efficient GMM
estimate of the coefficient on log PSG is virtually the same as before: –1.53, again significant at the 1%
level. The large J statistic in the PSG-exogenous GMM estimation in column 3 again strongly suggests
that we should reject the hypothesis that PSG, RGUNMAG, PCTDEM88 and the controls are all
exogenous; the small J statistic in the PSG-endogenous GMM estimation in column 4 means we fail to
the reject the hypothesis that RGUNMAG, PCTDEM88 and the controls are all exogenous; and the large
C statistic in column 3 strongly implies we should reject the hypothesis that PSG in particular is
exogenous. Again, some form of IV/GMM estimation that treats PSG as endogenous is called for. With
respect to the requirement of instrument relevance, column 4 shows that both of the excluded instruments
are still significant in the first-stage regression. A potential cause for concern, however, is the first-stage F
statistic, which at 12.2 is somewhat low and indicative of a possible weak instruments problem. We
therefore refer to the Anderson-Rubin 95% confidence interval for log PSG. This is [–3.35 , –0.06], vs.
the Wald-based interval of [–2.52 , –0.48]. The reduced relevance of the excluded instruments when
allowing for spatial correlation noticeably widens the AR confidence interval, but we can still reject the
hypothesis that our estimated coefficient on log PSG is zero, albeit at a reduced level of statistical
significance. Our key finding is therefore clearly robust to within-state spatial correlation. We again
conclude that we must treat gun levels as endogenous, and when this is done we find that they are, if
anything, associated with lower, not higher, rates of gun homicide across counties.
Table 4 presents the corresponding results for the log nongun homicide rate. The patterns in the
coefficients on the covariates are similar to those for the gun homicide equations; the main differences are
that rurality is now significantly associated with lower nongun homicide rates, and the economic controls
are less significant. The main difference vis-à-vis the gun homicide coefficients is in the estimated impact
of gun levels: across all estimations for the nongun homicide rate, the coefficient on log PSG is
insignificantly different from zero. The tests of orthogonality conditions suggest, moreover, that guns
36
may be treated as exogenous in the nongun homicide equation: the J statistics are low for both the
specifications that treat guns as exogenous (columns 1 and 3) and the specifications that treat guns as
endogenous (columns 2 and 4), and the C statistics for the endogeneity of log PSG are also low. The
implication is that the estimates for nongun homicide that treat guns as exogenous are to be preferred on
efficiency grounds, and the estimates that treat guns as endogenous are preferable if we wish to avoid a
Type II error in concluding they are exogenous; but the choice matters little because both sets of
estimations suggest no impact of guns on nongun homicide rates. The tests of instrument relevance are
(naturally) very similar to those for the gun homicide equations. Again the low first-stage F statistic when
allowing for intra-state spatial correlation is a concern, and again the AR confidence intervals for log PSG
support the Wald test results: gun levels have no impact on nongun homicide rates.
If we take these estimates of gun effects seriously, they suggest that gun levels in the general
public may, on net, have a deterrent effect on gun homicide rates, but no such effect on nongun
homicides. Deterrent effects would be stronger for gun homicides if their perpetrators were more likely to
plan the killings (or crimes leading up to the attacks, such as robbery or a drug deal) than those who use
less lethal weapons. The fact that an aggressor chose a lethal weapon, better suited to lethal purposes,
rather than merely making use of whatever weapons happened to be available at the scene, may itself be
an indication of premeditation. Thus, people who kill with guns may be more easily deterred by the
prospect of confronting a gun-armed victim than those who kill with other weapons, because the former
are more likely to think about the potential costs of their actions.
The results in Table 5 are for the estimations using the log total homicide rate (gun+nongun) as
the dependent variable. The results are similar to, but slightly weaker than, those for the gun homicide
rate. In the specifications that treat log PSG as exogenous, its coefficient is positive and either
insignificant (column 1) or significant at the 5% level (column 3). When gun levels are treated as
endogenous, the coefficient on log PSG becomes negative (about –1.0) and significant at the 5% level,
and the AR and Wald confidence intervals are again similar. The J statistics for the PSG-exogenous
estimations are large and suggest that one or more orthogonality conditions is violated. When the
orthogonality condition for PSG is dropped the J statistics become very small, suggesting that the
37
remaining orthogonality conditions are valid, and the C test strongly rejects the hypothesis that gun levels
are exogenous. The first-stage statistics again indicate a possible weak instrument problem for the cluster-
robust specification, and in this case the weak-instrument-robust AR 95% confidence interval in
column 4, though mostly negative, includes zero, i.e., an AR test of the coefficient on log PSG fails to
reject a zero impact of gun levels on homicide at the 5% significance level.
33
Our key finding remains:
gun levels have at least no impact, and possibly a negative impact, on total homicide rates.
We tested the robustness of the coefficient estimates by using the corresponding inefficient but
consistent GMM estimators, OLS and IV, and heteroskedastic- and cluster-robust standard errors; the
results were essentially identical.
34
Finally, we checked robustness to the functional form by comparing
the results using the dependent variables in the four possible log measures (drop zero-crime-rate counties
as used in the results above, “add 1”, “one-sided winsorized”, and “two-sided winsorized”) plus a fifth,
unlogged crime rates, and by using both log PSG and unlogged PSG as our gun proxies. This gave us
5*2=10 possible combinations of specifications, and estimating with and without cluster-efficient GMM
gave us 10*2=20 estimations in total for each of the three categories of homicide rates. The qualitative
results were almost entirely unaffected by these variations in functional form with respect both to the
estimate of impact of gun levels and to the findings on endogeneity, instrument validity and instrument
relevance. When both crime rates and PSG were logged, the quantitative results were also essentially
unchanged, with estimated coefficients very similar to those reported above. The specifications that used
the unlogged nongun homicide rate (CRNGMUR) provided the sole exception to this pattern, and, if
anything, strengthen our general conclusions: both PSG and log PSG were found to be endogenous, and
when instrumented, the estimated coefficients were negative and statistically significant, suggesting that
higher gun levels are associated with lower nongun homicide rates.
With respect to calibration, in the level-level specifications using the heteroskedastic-robust
efficient GMM estimator, the coefficients on PSG in the gun, nongun, and total homicide equations were
33
The AR confidence interval is negative and excludes zero if the level of confidence is reduced from 95% to 89%.
34
The first-stage and J and C statistics were identical by construction, the latter two because efficient GMM was
needed to produce heteroskedastic- and cluster-robust J and C statistics.
38
–0.227, –0.066, and –0.294, all statistically significant with p-levels about 0.01 (the cluster-robust
estimates were very similar). Using the calibration to HHG suggested above (0.706<δ
0
<1.24) implies that
an increase in 10 percentage points in the number of households with guns in a county would reduce gun
homicides by about 2 persons per 100,000 population, nongun homicides by about 0.7 persons, and total
homicides by about 3 persons. The implied elasticities of homicide to gun levels are somewhat higher
those estimated directly with the log-log specifications in Tables 3-5.
35
Again, however, we hasten to add
that these are very approximate estimates, and confidence intervals would include low, i.e., practically
unimportant, impacts. Our main conclusions, after from all these robustness checks, remain that the
positive correlation between gun levels and homicide rates is driven by endogeneity bias, and when the
endogeneity of gun levels is properly addressed in the estimation, any positive correlation vanishes.
7. CONCLUSIONS
Most studies of the gun-crime relationship have ignored the endogeneity problem, and the few
that have tried to address it with IV methods have failed to perform the tests needed to tell whether their
estimation procedures were adequate. We have presented a formal analysis of the three main problems
facing researchers – reverse causality, mismeasurement of gun levels, and omitted/confounding variables
– and discussed how to address these problems using estimation and specification testing procedures in a
GMM framework. We applied these procedures to U.S. county level data, and found strong evidence of
the existence of endogeneity problems. When the problem is ignored, gun levels are associated with
higher rates of gun homicide; when the problem is addressed, this association disappears or reverses
(though the reversal, suggesting that higher gun levels lead to lower gun crime rates, should be treated
with caution).
Our findings provide no support for the more guns, more homicide thesis. The appearance of such
an effect in past research appears to be the product of methodological flaws, especially the failure to
35
E.g., mean county CRGMUR in the sample is 4.1 homicides per 100,000 (Table 2); average HHG in the U.S. is
44% (Section 5). With a 1:1 calibration of PSG to HHG, the implied elasticity is therefore (–0.227)*44/4.1 –2.4,
vs. about –1.5 in Table 3.
39
properly account for the possible effect of crime rates on gun ownership levels. Higher gun prevalence
may have a net violence-elevating effect, but one that is confined to criminals or perhaps other high-risk
subsets of the population. To be consistent with our generally null findings regarding the effects of gun
levels, however, if there were such a violence-increasing effect of guns among criminals, it would have to
be counterbalanced by violence-reducing effects among noncriminals. Guns among criminals may
increase homicide while guns among noncriminals decrease it, with the two opposite-sign effects
canceling each other out. The most straightforward policy implication of such a combination of effects
would be that gun control measures should focus on reducing gun prevalence among criminals while
avoiding reducing it among noncriminals.
It might be argued that we failed to find support for the more guns, more homicide thesis because
PSG serves primarily as an indicator of gun prevalence among noncriminals, especially in suburban/rural
counties. Even if this were true, however, one would still expect criminal gun prevalence to be positively
correlated with noncriminal gun prevalence, if for no other reason than that most criminals acquire guns
as a direct or indirect result of thefts from noncriminals (Wright and Rossi 1986, p. 196). Thus, PSG
would still measure criminal gun prevalence, but less strongly than more direct measures. Therefore, a
more precise variant of this speculation would be that PSG might be a weaker proxy for criminal gun
prevalence than it is for noncriminal gun prevalence, or that the excluded instruments that we use
(RGUNMAG and PCTDEM88) are more weakly correlated with criminal than with noncriminal gun
prevalence; either would lead to weaker associations between gun prevalence and violence rates than
would be obtained if we could more specifically measure criminal gun prevalence. It bears repeating,
however, that at this point this idea is nothing more than a plausible but empirically unsupported
speculation. Therefore, identifying proxies that can separately measure criminal and noncriminal gun
prevalence should be a top priority for future research.
40
Table 1. Macro-Level Studies of the Impact of Gun Levels on Crime Rates
a
Study Sample
Gun Measure
b
Crime Rates
c
Results
d
Simul?
e
Brearley (1932) 42 states PGH THR Yes No
Krug (1967) 50 states HLR ICR No No
Newton and Zimring (1969) 4 years, Detroit NPP THR,TRR,AAR,
GHR
Yes No
Seitz (1972) 50 states GHR,FGA,AAR THR Yes No
Murray (1975) 50 states SGR,SHR GHR,AAR,TRR No No
Fisher (1976) 9 years, Detroit NPP,GRR,PGH THR Yes (No)
Phillips et al. (1976) 18 years, U.S. PROD THR Yes No
Brill (1977) 11 cities PGC ICR
THR
TRR
No
Yes
No
No
Kleck (1979) 27 years, U.S. PROD THR Yes (No)
Cook (1979) 50 cities PGH,PSG TRR
RMR
No
Yes
No
Kleck (1984) 32 years, U.S. PROD THR
TRR
No
Yes
(No)
Maggadino and Medoff (1984) 31 years, U.S. PROD THR No (No)
Lester (1985) 37 cities PCS VCR No No
Bordua (1986) 102 counties
9 regions
GLR,SIR HAR,THR,GHR No No
McDowall (1986) 48 cities, 2 years PGH,PSG TRR No (No)
Lester (1988b) 9 regions SGR THR Yes No
McDowall (1991) 36 years, Detroit PSG,PGR THR Yes (No)
Killias (1993) 16 nations SGR THR,GHR Yes No
Kleck and Patterson (1993) 170 cities 5-item factor
incl. PSG
f
THR,GHR,TRR,
GRR,AAR,GAR
No Yes
Lester (1996) 12 nations PGH,PSG THR,GHR Yes No
Southwick (1997) 48 years, U.S. PROD THR,TPR,TRR,
AAR
No Yes
Southwick (1999) 34 years, U.S. HGS THR,TRR,AAR,
TPR,VCR,BUR
No No
Hemenway and Miller (2000) 26 nations PGH,PSG THR Yes No
Lott (2000) 15 states, 2 years
g
SGR THR,TPR,TRR,
AAR, 3 others
No No
Stolzenberg and D'Alessio
(2000)
4 years, 46
counties
CCW, GUNSTOL VCR Yes No
Duggan (2001) 19 years, 50 states GMR THR,TPR,TRR,
AAR
Yes No
Hoskin (2001) 36 nations PSG THR Yes (No)
Killias et al. (2001) 21 nations SGR THR,TRR,TAR,
GHR,GRR,GAR
No No
Sorenson and Berk (2001) 22 years, California HGS THR Yes (No)
Cook and Ludwig (2002) 22 years, 50 states PSG BUR Yes (No)
Miller et al. (2002) 10 years, 50 states
10 years, 9 regions
PSG,PHG
SGR
THR
THR
Yes
No
No
No
Ruddel and Mays (2005) 50 states 3-item factor incl.
PSG
h
THR Yes No
Moody and Marvell (2005) 50 states, 22 years PSG, SHR THR,TPR,TRR,
AAR,BUR
No Yes
41
Notes to Table 1:
a. Table covers only studies and findings where the dependent variable was a crime rate, as opposed to the
fraction of crimes committed with guns, and where gun ownership levels were actually measured, rather
than assumed. Studies that examined only gun violence rates (e.g., only gun homicides) are excluded.
b. Measures of Gun Level: CCW = concealed carry permits rate; FGA = Fatal gun accident rate; GLR =
Gun owners license rate; GMR = Gun magazine subscription rates; GRR = Gun registrations rate;
GUNSTOL = % of $ value of stolen property due to guns; HGS = handgun sales (retail); HLR = Hunting
license rate; NPP = Number of handgun purchase permits; PGA = % aggravated assaults committed with
guns; PGC = % homicides, aggravated assaults and robberies (combined together) committed with guns;
PCS = same as PGC, but with suicides lumped in as well; PGH = % homicides committed with guns;
PGR = % robberies committed with guns; PSG = % suicides committed with guns; PROD= Guns
produced minus exports plus imports, U.S.; SGR = Survey measure, % households with gun(s); SHR =
Survey measure, % households with handgun(s); SIR = Survey measure, % individuals with gun(s)
c. Crime Rates: AAR = Aggravated assault rate; BUR = burglary rate; GAR = Gun aggravated assault
rate; GHR = Gun homicide rate; GRR = Gun robbery rate; HAR = Homicide, assault and robbery index
(factor score); ICR = Index crime rate; RMR = Robbery murder rate; THR = Total homicide rate; TPR =
Total rape rate; TRR = Total robbery rate; VCR = Violent crime rate
d. Yes=Study found significant positive association between gun levels and violence; No=Study did not
find such a link.
e. Did research address possible simultaneous relationship between gun levels and crime rates with
properly identified model? (No) means researchers tried to address the issue, but model was still
underidentified.
f. Five-item factor composed of PSG, PGH, PGR, PGA, and the percent of dollar value of stolen property
due to stolen guns.
g. Panel design, two waves.
h. Three-item factor composed of PSG, the gun theft rate, and the fatal gun accident rate.
42
Table 2a: Descriptive Statistics Mean
Std.
Dev.
Min Max
Homicide variables, 1987-93 average
CRGMUR Gun homicides per 100,000 population 4.13 4.18 0.00 46.08
Log CRGMUR " logged 1.01 0.96 -2.02 3.83
CRNGMUR Nongun homicides per 100,000 pop. 2.17 1.73 0.00 13.39
Log CRNGMUR " logged 0.53 0.78 -1.74 2.59
CRMUR Total homicides per 100,000 pop. 6.30 5.62 0.00 57.67
Log CRMUR " logged 1.50 0.86 -1.01 4.05
Gun availability, 1987-93 average
PSG % suicides with guns 66.67 13.46 15.28 100.00
Log PSG " logged 4.18 0.23 2.73 4.61
Excluded instruments
PCTDEM88 % presidential vote Democrat, 1988 42.49 9.87 17.70 84.74
Log PCTDEM88 " logged 3.72 0.24 2.87 4.44
RGUNMAG
Principal components measure of 3 top
outdoor/sport magazine subscriptions
0.00 1.00 -4.79 2.39
Controls
DENSITY Persons per square mile 418 2075 2 53126
Log DENSITY " logged 4.78 1.27 0.47 10.88
PCTURBAN % urban (inside urbanized area) 28.32 36.95 0.00 100.00
PCTSUBURBAN % suburban (outside urbanized area) 25.52 22.22 0.00 100.00
PCTRURAL % rural (farm+nonfarm) 46.16 26.14 0.00 100.00
PCT0T17 % aged 17 and under 26.34 3.24 15.10 41.70
PCT18T24 % aged 18-24 10.70 3.72 5.10 37.10
PCT25T44 % aged 25-44 30.94 3.02 20.30 45.30
PCT45T64 % aged 45-64 18.95 2.13 8.40 27.10
PCT65PLUS % aged 65 and over 13.08 3.59 3.00 33.80
PCTBLK % African-American 9.24 12.67 0.01 72.13
Log PCTBLK " logged 1.05 1.82 -4.36 4.28
PCTHISP % Hispanic 4.43 10.25 0.14 97.22
Log PCTHISP " logged 0.41 1.30 -1.97 4.58
PCTFEM18 % female-headed HHs w/children < 18 58.54 7.11 33.40 84.10
Log PCTFEM18 " logged 4.06 0.12 3.51 4.43
PCTEDUC % aged 25+ with a BA degree or higher 16.06 7.36 4.60 52.30
Log PCTEDUC " logged 2.68 0.42 1.53 3.96
PCTTRANS % born out of state 31.22 15.85 5.09 86.54
Log PCTTRANS " logged 3.32 0.51 1.63 4.46
Log MEDHHINC Log median household income, 1989 10.18 0.24 9.23 10.99
PCTINCLT15K % households with income < $15,000 27.86 8.88 5.00 65.20
Log PCTINCLT15K " logged 3.27 0.36 1.61 4.18
INEQUALITY % HHs w/income <$15k / % income >$75k 0.32 0.50 0.02 6.74
Log INEQUALITY " logged -1.64 0.89 -4.08 1.91
PCTPOOR % persons below poverty line, 1989 14.26 6.89 2.20 60.00
Log PCTPOOR " logged 2.55 0.49 0.79 4.09
PCTUNEMP % persons unemployed 6.65 2.47 1.50 23.60
Log PCTUNEMP " logged 1.83 0.36 0.41 3.16
PCTVACANT % housing units vacant 11.03 7.65 2.70 66.20
Log PCTVACANT " logged 2.24 0.54 0.99 4.19
43
Table 2b: Alternative measures of logged homicide variables Obs Mean
Std.
Dev.
Min Max
Log CRGMUR
Logged, dropping zero-rate counties 1442 1.01 0.96 -2.02 3.83
"Add 1", logged 1462 1.11 0.88 -1.33 3.83
Winsorized lower tail, logged 1462 0.97 1.02 -2.02 3.83
Two-sided winsorized, logged 1462 0.96 1.01 -2.02 2.84
Log CRNGMUR
Logged, dropping zero-rate counties 1410 0.53 0.78 -1.74 2.59
"Add 1", logged 1462 0.65 0.70 -1.52 2.60
Winsorized lower tail, logged 1462 0.45 0.87 -1.74 2.59
Two-sided winsorized, logged 1462 0.44 0.86 -1.74 1.77
Log CRMUR
Logged, dropping zero-rate counties 1459 1.50 0.86 -1.01 4.05
"Add 1", logged 1462 1.58 0.79 -0.83 4.06
Winsorized lower tail, logged 1462 1.49 0.87 -1.01 4.05
Two-sided winsorized, logged 1462 1.49 0.87 -1.01 3.73
Sources for Tables 2a and 2b: U.S. Bureau of the Census, County and City Data Book (1994), except for
(a) homicide rates and PSG, from U.S. NCHS (1997); (b) PCTDEM88, from ICPSR (1995); (c) magazine
subscription rates used to construct RGUNMAG, from Audit Bureau of Circulations (1993); (d) rurality
measures, from U.S. Bureau of the Census (2000).
44
Table 3: Log gun homicide equation
Dependent variable: Log CRGMUR
2-step Efficient GMM
(heteroskedastic-efficient)
2-step Efficient GMM
(heteroskedastic- and cluster-efficient)
PSG-exogenous PSG-endogenous PSG-exogenous PSG-endogenous
Log PSG 0.290* -1.500** 0.389*** -1.530**
(0.115) (0.521) (0.112) (0.528)
Log DENSITY 0.241*** 0.145*** 0.226*** 0.143***
(0.027) (0.039) (0.030) (0.042)
PCTSUBURBAN -0.004* -0.005*** -0.003* -0.005***
(0.001) (0.002) (0.001) (0.001)
PCTURBAN -0.001 -0.002* -0.001 -0.002*
(0.001) (0.001) (0.001) (0.001)
PCT0T17 0.032** 0.043*** 0.030* 0.043**
(0.010) (0.012) (0.013) (0.015)
PCT18T24 -0.013 -0.003 -0.013 -0.003
(0.009) (0.010) (0.008) (0.009)
PCT25T44 0.026** 0.025** 0.024** 0.025**
(0.009) (0.010) (0.008) (0.008)
PCT45T64 0.053** 0.074*** 0.055*** 0.075***
(0.017) (0.020) (0.017) (0.016)
Log PCTBLK 0.149*** 0.161*** 0.150*** 0.161***
(0.014) (0.016) (0.016) (0.016)
Log PCTHISP 0.061* 0.016 0.041 0.015
(0.024) (0.030) (0.032) (0.033)
Log PCTFEM18 -0.118 0.393 -0.153 0.406
(0.192) (0.251) (0.262) (0.339)
Log PCTEDUC -0.375*** -0.468*** -0.333** -0.483***
(0.097) (0.108) (0.116) (0.124)
Log PCTTRANS -0.023 0.008 0.012 0.009
(0.055) (0.058) (0.065) (0.077)
Log MEDHHINC -0.294 -0.100 -0.297 -0.104
(0.310) (0.338) (0.411) (0.448)
Log PCTINCLT15K 0.508 0.900** 0.282 0.896*
(0.265) (0.302) (0.340) (0.402)
Log INEQUALITY 0.392*** 0.422*** 0.354** 0.433***
(0.093) (0.102) (0.112) (0.115)
Log PCTPOOR 0.726*** 0.519** 0.799*** 0.532**
(0.142) (0.162) (0.206) (0.206)
Log PCTUNEMP -0.020 0.097 0.060 0.090
(0.083) (0.096) (0.092) (0.092)
Log PCTVACANT 0.144*** 0.153*** 0.158*** 0.153***
(0.041) (0.045) (0.040) (0.045)
R
2
0.442 0.333 0.439 0.329
N 1441 1441 1441 1441
45
Table 3: Log gun homicide equation (continued)
Dependent variable: Log CRGMUR
2-step Efficient GMM
(heteroskedastic-efficient)
2-step Efficient GMM
(heteroskedastic- and cluster-efficient)
PSG-exogenous PSG-endogenous PSG-exogenous PSG-endogenous
J statistic χ
2
(2)=13.29** χ
2
(1)=0.254 χ
2
(2)=8.18* χ
2
(1)=0.162
p-value 0.0013 0.6145 0.0168 0.6874
C statistic χ
2
(1)=13.01*** χ
2
(1)=8.01**
p-value 0.0003 0.0047
95% confidence interval
for log PSG
Wald [-2.52, -0.48] [-2.56, -0.50]
Anderson-Rubin [-3.05 , -0.34] [-3.35 , -0.06]
First-stage regression:
F statistic 26.2 12.2
Log PCTDEM88 -0.075*** -0.075**
(0.022) (0.027)
RGUNMAG 0.046*** 0.046***
(0.008) (0.013)
Notes: * p<0.05, ** p<0.01, *** p<0.001.
Standard errors in parentheses.
Excluded instruments are log PCTDEM88 and RGUNMAG.
R
2
is the within-R
2
(see text).
All equations are estimated with 50 state fixed effects.
46
Table 4: Log nongun homicide equation
Dependent variable: Log CRNGMUR
2-step Efficient GMM
(heteroskedastic-efficient)
2-step Efficient GMM
(heteroskedastic- and cluster-efficient)
PSG-exogenous PSG-endogenous PSG-exogenous PSG-endogenous
Log PSG
-0.009 -0.490 0.013 -0.559
(0.107) (0.478) (0.111) (0.552)
Log DENSITY
0.135*** 0.110*** 0.134*** 0.107**
(0.022) (0.033) (0.021) (0.034)
PCTSUBURBAN
0.003* 0.002 0.003* 0.002
(0.001) (0.001) (0.001) (0.001)
PCTURBAN
0.003** 0.002* 0.003** 0.003**
(0.001) (0.001) (0.001) (0.001)
PCT0T17
0.017 0.020* 0.017 0.019*
(0.009) (0.010) (0.009) (0.009)
PCT18T24
-0.034*** -0.032*** -0.031*** -0.033***
(0.008) (0.009) (0.007) (0.008)
PCT25T44
0.004 0.003 0.007 0.005
(0.008) (0.008) (0.008) (0.009)
PCT45T64
-0.012 -0.007 -0.009 -0.010
(0.015) (0.016) (0.014) (0.014)
Log PCTBLK
0.152*** 0.154*** 0.150*** 0.154***
(0.013) (0.013) (0.010) (0.010)
Log PCTHISP
0.062** 0.046 0.061* 0.045
(0.023) (0.027) (0.030) (0.032)
Log PCTFEM18
0.073 0.229 0.042 0.235
(0.181) (0.238) (0.148) (0.256)
Log PCTEDUC
-0.196* -0.219* -0.232** -0.230**
(0.085) (0.089) (0.080) (0.084)
Log PCTTRANS
0.057 0.060 0.079 0.071
(0.048) (0.048) (0.050) (0.050)
Log MEDHHINC
0.324 0.395 0.334 0.377
(0.274) (0.283) (0.308) (0.303)
Log PCTINCLT15K
0.916*** 1.011*** 1.020*** 1.099***
(0.231) (0.251) (0.259) (0.270)
Log INEQUALITY
0.214* 0.220* 0.242* 0.228*
(0.092) (0.093) (0.101) (0.103)
Log PCTPOOR
0.355** 0.309* 0.320* 0.240
(0.124) (0.133) (0.138) (0.155)
Log PCTUNEMP
0.116 0.151 0.130 0.178
(0.083) (0.091) (0.095) (0.104)
Log PCTVACANT
0.045 0.044 0.047 0.039
(0.038) (0.038) (0.047) (0.046)
R
2
0.435 0.425 0.434 0.422
N
1409 1409 1409 1409
47
Table 4: Log nongun homicide equation (continued)
Dependent variable: Log CRNGMUR
2-step Efficient GMM
(heteroskedastic-efficient)
2-step Efficient GMM
(heteroskedastic- and cluster-efficient)
PSG-exogenous PSG-endogenous PSG-exogenous PSG-endogenous
J statistic
χ
2
(2)=1.99 χ
2
(1)=0.898 χ
2
(2)=2.43 χ
2
(1)=1.37
p-value
0.3703 0.3432 0.2964 0.2413
C statistic
χ
2
(1)=1.07 χ
2
(1)=0.977
p-value
0.3005 0.3230
95% confidence interval
for log PSG
Wald
[-1.43, 0.45] [-1.64, 0.52]
Anderson-Rubin
[-1.71, 0.62] [-2.10, 1.06]
First-stage regression:
F statistic
24.2 10.9
Log PCTDEM88
-0.071** -0.071*
(0.022) (0.027)
RGUNMAG
0.045*** 0.045**
(0.008) (0.013)
Notes: * p<0.05, ** p<0.01, *** p<0.001.
Standard errors in parentheses.
Excluded instruments are log PCTDEM88 and RGUNMAG.
R
2
is the within-R
2
(see text).
All equations are estimated with 50 state fixed effects.
48
Table 5: Log total homicide equation
Dependent variable: Log CRMUR
2-step Efficient GMM
(heteroskedastic-efficient)
2-step Efficient GMM
(heteroskedastic- and cluster-efficient)
PSG-exogenous PSG-endogenous PSG-exogenous PSG-endogenous
Log PSG
0.160 -1.023* 0.225* -1.023*
(0.095) (0.437) (0.094) (0.450)
Log DENSITY
0.212*** 0.147*** 0.200*** 0.147***
(0.021) (0.033) (0.023) (0.032)
PCTSUBURBAN
-0.001 -0.003* -0.001 -0.003*
(0.001) (0.001) (0.001) (0.001)
PCTURBAN
-0.000 -0.001 0.000 -0.001
(0.001) (0.001) (0.001) (0.001)
PCT0T17
0.024** 0.030** 0.022** 0.030**
(0.009) (0.010) (0.008) (0.010)
PCT18T24
-0.021** -0.015 -0.020** -0.015
(0.007) (0.008) (0.007) (0.008)
PCT25T44
0.020** 0.020* 0.023** 0.020*
(0.008) (0.008) (0.007) (0.008)
PCT45T64
0.034* 0.048** 0.037** 0.048***
(0.014) (0.016) (0.012) (0.013)
Log PCTBLK
0.154*** 0.161*** 0.153*** 0.161***
(0.012) (0.013) (0.013) (0.013)
Log PCTHISP
0.061** 0.027 0.041 0.027
(0.020) (0.025) (0.021) (0.024)
Log PCTFEM18
0.070 0.427 0.008 0.426
(0.166) (0.218) (0.185) (0.255)
Log PCTEDUC
-0.273*** -0.317*** -0.290** -0.317***
(0.081) (0.087) (0.088) (0.092)
Log PCTTRANS
-0.004 0.008 0.021 0.008
(0.047) (0.049) (0.058) (0.064)
Log MEDHHINC
-0.084 0.032 -0.126 0.032
(0.261) (0.276) (0.326) (0.343)
Log PCTINCLT15K
0.584** 0.848*** 0.502 0.848**
(0.223) (0.256) (0.279) (0.317)
Log INEQUALITY
0.309*** 0.325*** 0.340*** 0.325***
(0.080) (0.085) (0.088) (0.090)
Log PCTPOOR
0.599*** 0.441** 0.674*** 0.441*
(0.117) (0.137) (0.156) (0.175)
Log PCTUNEMP
0.115 0.207* 0.162* 0.208*
(0.073) (0.086) (0.081) (0.085)
Log PCTVACANT
0.080* 0.074 0.099** 0.074*
(0.036) (0.038) (0.031) (0.030)
R
2
0.527 0.463 0.525 0.463
N
1458 1458 1458 1458
49
Table 5: Log total homicide equation (continued)
Dependent variable: Log CRMUR
2-step Efficient GMM
(heteroskedastic-efficient)
2-step Efficient GMM
(heteroskedastic- and cluster-efficient)
PSG-exogenous PSG-endogenous PSG-exogenous PSG-endogenous
J statistic
χ
2
(2)=8.51 χ
2
(1)<0.001 χ
2
(2)=6.01 χ
2
(1)<0.001
p-value
0.0142 0.9907 0.0497 0.9922
C statistic
χ
2
(1)=8.51 χ
2
(1)=6.01
p-value
0.0035 0.0143
95% confidence interval
for log PSG
Wald
[-1.88, -0.17] [-1.90, -0.14]
Anderson-Rubin
[-2.35, -0.02] [-2.64, 0.21]
First-stage regression:
F statistic
24.8 11.3
Log PCTDEM88
-0.072*** -0.072*
(0.022) (0.027)
RGUNMAG
0.045*** 0.045***
(0.008) (0.013)
Notes: * p<0.05, ** p<0.01, *** p<0.001.
Standard errors in parentheses.
Excluded instruments are log PCTDEM88 and RGUNMAG.
R
2
is the within-R
2
(see text).
All equations are estimated with 50 state fixed effects.
50
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56
BIOGRAPHICAL SKETCHES
Tomislav Kovandzic is Assistant Professor of Criminal Justice in Department of Justice Sciences at the
University of Alabama at Birmingham. His current research interests include criminal justice policy and
gun-related violence. His most recent articles have appeared in Criminology & Public Policy,
Criminology, and Homicide Studies. He received his Ph.D. in Criminology from Florida State University
in 1999.
Mark E. Schaffer is Professor of Economics at Heriot-Watt University, Edinburgh, U.K. His research
interests include economic reform in transition and developing economies, and the implementation of
econometric estimators. He is a member of the Executive Committee of the Association for Comparative
Economic Studies (ACES) and is an Associate Editor of the Stata Journal.
Gary Kleck is Professor of Criminology and Criminal Justice at Florida State University. His research
focuses on the links between guns and violence and the deterrent effects of punishment. He is the author
of four books, including Point Blank, which won the 1993 Hindelang Award, and, most recently, Armed
(Prometheus, 2001).
57
... Despite these important differences, the larger gun-crime literature is informative, particularly regarding how best to approach examining this relationship from a methodological standpoint. More specifically, critiques of this trajectory of research have attributed the considerable variation in findings due to studies' limitations (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013. Such limitations include a reliance on descriptive and bivariate analyses despite the likelihood of feedback relationships (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013, the lack of non-firearm outcomes and other important controls (Britt et al. 1996;Kleck 2001), and measurement issues motivating the need for alternative variables (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013LaFree 1999). ...
... More specifically, critiques of this trajectory of research have attributed the considerable variation in findings due to studies' limitations (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013. Such limitations include a reliance on descriptive and bivariate analyses despite the likelihood of feedback relationships (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013, the lack of non-firearm outcomes and other important controls (Britt et al. 1996;Kleck 2001), and measurement issues motivating the need for alternative variables (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013LaFree 1999). The reliance on small sample sizes (Hemenway and Miller 2000;Killias 1993a;Kleck 2015) and less attention directed toward the potentially confounding influence of outliers (Rosenbaum 2012) have also been noted as important issues in prior research. ...
... More specifically, critiques of this trajectory of research have attributed the considerable variation in findings due to studies' limitations (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013. Such limitations include a reliance on descriptive and bivariate analyses despite the likelihood of feedback relationships (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013, the lack of non-firearm outcomes and other important controls (Britt et al. 1996;Kleck 2001), and measurement issues motivating the need for alternative variables (Kleck 2015;Kovandzic et al. 2012Kovandzic et al. , 2013LaFree 1999). The reliance on small sample sizes (Hemenway and Miller 2000;Killias 1993a;Kleck 2015) and less attention directed toward the potentially confounding influence of outliers (Rosenbaum 2012) have also been noted as important issues in prior research. ...
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... While some argue that significant public safety benefits may arise from increased firearm legislation, in the form of reduced accidental deaths and homicides (e.g., Chapdelaine & Maurice, 1996;Fisher & Drummond, 1999), others have questioned this and highlighted conceptual and methodological issues such as method substitution and endogeneity bias (e.g. Kates & Mauser, 2007;Kovandzic, Schaffer, & Kleck, 2005;Mauser, 2007). The United Kingdom, also, has not found consensus on this issue; Adshead, Fonagy, and Sarkar (2007) and Smith (2006) provide thoughtful overviews of factors driving that debate. ...
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