Evaluating a National Anti-Firearm Law and Estimating the Causal Effect of Guns on Crime

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No. 607

Evaluating a National Anti-Firearm
Law and Estimating the Causal Effect of
Guns on Crime
Daniel Cerqueira
João M. P. de Mello
TEXTO PARA DISCUSSÃO
DEPARTAMENTO DE ECONOMIA
www.econ.
p
uc-rio.b
r

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Evaluating a National Anti-Firearm Law and Estimating the
Causal Effect of Guns on Crime1
Daniel Cerqueira and João M. P. De Mello
ABSTRACT
We report two results. First, we evaluate the impact of a nationwide anti-firearm legislation passed
by the Brazilian Congress in December 2003 (Estatuto do Desarmamento, henceforth ED). Our identification
strategy hinges on the hypothesis that the law had stronger impact in places where gun prevalence was
higher in the baseline. We find evidence that homicides (reduced form) and firearms prevalence
(mechanism or first-stage) dropped faster in places with higher gun prevalence after the 2003. Using our
preferred estimates, the ED saved between 2,000 and 2,750 lives from 2004 through 2007 in cities with
more than 50,000 inhabitants in the state of São Paulo. Second, assuming the ED causes homicide only
through its impact on firearms prevalence, we recover a causal estimate of the impact of firearms on
homicides. One standard deviation in the prevalence of firearms reduces homicides by quarter of a
standard deviation. We find no impact of both ED and firearms on property crime in general or on
robberies.
Keywords: homicide; Brazil; firearms, gun violence; property crimes
JEL Classification: K42
1 Cerqueira: Instituto de Pesquisa Econômica Aplicada (IPEA). Email: daniel.cerqueira@ipea.gov.br. De Mello: Departamento de
Economia, PUC-Rio. Email: jmpm@econ.puc-rio.br. We are grateful to Tulio Kahn for kindly sharing the data. We thank Rodrigo
Soares, Leandro Piquet, Fernando Veloso, Claudio Ferraz and Leonardo Rezende for invaluable comments. Usual disclaimers apply.

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1. Introduction
Following the surge in violent crime in the second half of the 1980s, the role of guns as a criminogenic
factor has been hotly debated in the US. One side argues that firearms cause violence because they increase
the lethality of disputes, a statement mainly about violent crime, especially homicides. Several papers have
found empirical support for this lethality hypothesis. A non-exhaustive list includes Duggan (2001),
Sherman et al (1995), Stolzenberg and D´Alessio (2000), McDowall (1991), McDowall et al. (1995), Cook
and Ludwig (1998, 2002), Sloan et al. (1990), Ludwig (1998), and Newton and Zimring (1969).
Other scholars argue the opposite. The defensive gun use hypothesis states that the ability of law-
abiding citizens to carry firearms deters criminals. Thus, it is a statement mainly about property crime,
with only second-order implications for violent crime. Evidence on the deterrence role of firearms is
provided by Lott (1998), Lott and Mustard (1997), Kleck (1997), and Bartley and Cohen (1998).
The dispute over the causal impact of fire weapons availability on crime is still unsettled. In this
context, we make two contributions to the literature. First, we evaluate the impact of the Estatuto do
Desarmamento (henceforth ED).2 ED is a nationwide firearms legislation enacted in December 2003 by the
Brazilian Congress. It severely restricted the possibility of legal firearms possession, and increased the
penalties for the illegal possession. Our reduced-form estimates show that the ED caused a reduction on
homicides. According to our preferred estimate, the ED saved between 2,000 and 2,750 lives from 2004
through 2007. We find no systematic impact on property crime. We also document the mechanism. Using
suicides by firearms as a measure of prevalence of guns – Cook and Ludwig´s (2002) well validated
measure – we find that the ED reduced the availability of firearms.
These results are important per se. First, the literature on firearms is narrowly focused on the US,
while crime is arguably a more important in other countries such as Brazil. Most US inspired, the literature
has focused on local or state-level interventions. In contrast, we evaluate large scale intervention to control
fire weapons’ availability, which may inspire other similar policies. Nationwide interventions do pose
identification challenges for the lack of cross-section variation. On the other hand, nationwide interventions
are exogenous to states or municipalities, and differences in baseline variables may be used to identify the
causal impact of the intervention, under some assumptions.
The second contribution is recovering a causal estimate of firearms on crime, which has been an
ongoing challenge in the literature for two reasons. First, violence begets arms. Second, measurement is
hard because the prevalence of firearms is non-observable. Measures based on police reports, i.e. illegal
possession, capture not only prevalence but also enforcement, which, in turn, is typically difficult to control
for. Furthermore, one cannot sign the bias caused by police measures of fire guns prevalence.
We address the problem of reverse causality by assuming that the impact of the law is stronger
where firearms were more prevalent. Under this assumption, we can use cross-city differences in the
2 Law 10.826, from 12/22/2003.

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baseline prevalence of firearms as an instrument for within-city changes in prevalence of firearms. We
address the measurement problem using Cook and Ludwig’s (2002) well validated suicide by firearms
proxy. We find that firearms’ prevalence have a small but non-negligible impact on violence. Using our most
conservative estimate, a reduction in one standard deviation in firearms causes homicides to drop by ¼ of a
standard deviation. We find no impact on property crime.
The paper is organized as follows. Section 2 is a brief review of the large literature on the firearms-
crime nexus. We focus on the theoretical mechanisms behind the nexus and on the empirical challenges to
recover causal parameters and the methods employed to establish causality. Section 3 provides
background on crime and enforcement in the state of São Paulo. Section 4 describes the data. Section 5
describes the intervention, the Estatuto do Desarmamento. Section 6 outlines the empirical strategy. Results
are in Section 7. Section 8 discusses and concludes.
2. Literature Review: The Search for the Causal Impact of Firearms on Crime
The causal effect of the prevalence of firearms on crime has been on the holy grails of social science.
The interest in the subject is proportional to the controversy about the results obtained in several studies,
which, to some extent, reflect the limited data availability and the complexity of the phenomenon which
imposes methodological challenges to researchers.
The results that make clear the positive correlation between firearms, suicides, and homicides at an
international level have been less controversial. Based on information from 16 European nations, Lester
(1991) found a high correlation between firearm-related homicides and two proxy measures of the spread
of firearms in those countries. Using data from 14 countries, Killias (1993) also documented a positive
correlation between the availability of firearms and the rates of firearm-related homicides and suicides.
From a theoretical perspective, it is not clear whether firearms are criminogenic (Dezhbakshsh and
Rubin 2003, in Moody and Marvell, 2002). Two clear opposing forces are at work. On the one hand, the
spread of firearms among the population increases the lethality of the means used by individuals to solve
violent conflicts, conditional on the conflict happening; and facilitates the access and reduces the cost of
firearms for the criminal, either by increasing the supply in the black market or by increasing the quantity
of stolen guns. All these factors suggest that the availability of firearms will increase crime, especially (but
not only) violent crime. This is the lethality hypothesis. On the other hand, firearms have a deterrence effect.
Better armed law-abiding citizens, ceteris paribus, increases the expected cost of the committing a crime.
This is the defensive gun use hypothesis, mainly a statement about property crimes when the perpetrator
has contact with the victim, and only incidentally about violent crime. Finally, the effect of the increased
lethality of firearms on the number of conflicts is ambiguous. Increased lethality dissuades violent conflict-
resolution because of the increased cost of the violence. However, firearms increase the power to coerce
exerted by the bearer of the weapon, encouraging non-peaceful responses to solve conflicts. Consider a

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situation in which criminals have more weapons but all the sudden their average lethality is lower, i.e.,
because firearms are successfully banned. In this case, it is conceivable that the ability to coerce is
diminished, reducing the payoff of committing crimes. Theoretical ambiguity implies that the causal
relationship between firearms and crimes is an empirical question.
Most empirical studies find evidence that firearms are criminogenic, especially for violent crimes
such as homicides. Nevertheless, several authors who argue the opposite or even argue that there is no
causal relationship between firearms and crimes. Empirical ambiguity is hardly surprising when theory
does not resolve the issue.
The empirical literature struggles with on two identification issues: measurement and endogeneity
broadly understood confounding factor and reverse causation. Many a paper focus on providing good
proxies of firearms and the quantity of guns for defensive use in the hands of American households
(defensive gun use). Second, cross-sectional and time-series differences in the prevalence of firearms are
not exogenous, even if firearms’ prevalence was well measured.
Several strategies have been used to deal with endogeneity.3 McDowall (1991) – a pioneering attempt
to establish causality – uses instrumental variables strategy with aggregate data to compute firearms-
elasticities of crime. Duggan (2000) finds that past gun ownership and current homicides are strongly
positively related. Directly related to the deterrence hypothesis, Cook and Ludwig (2002) used data from
the Uniform Crime Reports (UCR) and the National Crime Victimization Survey (NCVS) and find that the
elasticity of the firearms in relation to burglaries vary in the range between 0.3 and 0.7.
The debate of the Shall Issue Concealed Handgun Laws stands on its own in the literature. Following
Florida in 1987, 31 states passed laws to allow citizens to obtain licenses to carry firearms. McDowall et al.
(1995) evaluate the effects on homicides in large cities from three US states of the amendment to the
Concealed Firearms Laws, in which the law changed from “may issue” to “shall issue”. They find that “shall
issue law” did not led to a reduction in overall homicides, at least in large urban areas; but did increase the
number of firearm-related homicides. One of the most discussed and controversial articles in this literature,
Lott and Mustard (1997) investigate the effect of the implementation of the “shall issue law” on both violent
and property crimes. They find that “shall issue laws” caused violent crimes to drop without an increase in
accidental deaths caused by firearms. They also found evidence that criminals substitute from “high
contact” property crimes, say armed robbery, “low-contact” offences. See also Lott (2000). Several authors
have shown that Lott and Mustard (1997) suffer from methodological deficiencies, and reach a different
conclusion using similar data or using other datasets. Ludwig (1998) finds that, if anything, “shall issue
laws” cause an increase in adult homicide rate. Using data similar to Lott and Mustard (1997), Dezhbakhsh
and Rubin (1998, 2003) find mixed results: a slight drop in homicides, an increase in robberies, but and
mostly ambiguous results on other crime categories.4
3 We postpone the discussion on how the literature has tried to solve the measurement problem to Section 6.1.
4 It is beyond the scope of this paper to review the whole controversy, which runs long. Among supports, see Barteley and Cohen
(1998), Plassmann and Tideman (2001), Moody (2001), and Olson and Maltz (2001). Among critics, see Ayres and Donohue (2003),

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Another point of contention is the legal and illegal use of firearms by young people to commit lethal
and nonlethal crimes. Stolzenberg and D'Alessio (2000) use of an unprecedented database from the
National Incident-Based Reporting System (NIBRS), for South Carolina, which identified, from 1991 to
1994, not only the number of violent crimes by county, but also those (even the non-lethal) crimes
committed with the use of a firearm and by young people. The y find that violent crimes, crimes committed
with firearms and crimes committed by young people were positively affected by the availability of illegal
firearms, but not by the availability of legal firearms. Furthermore, the authors found no evidence of
substitution of firearms for bladed weapons.
The literature finds mixed results on the firearm- crime nexus. While most papers find that guns are
criminogenic, especially for violent crime, there is non-negligible body of dissenting articles. Furthermore
identification is difficult because of omitted variables, reverse causality and measurement (section 6
below), which adds to the empirical ambiguity. In this context, our paper contributes by proposing a
different identification strategy, by using data from a country other than the US, and by focusing on a large-
scale restrictive intervention which is quite different from the Right-to-Carry US state-level interventions
typically evaluated in the literature.
3. The Empirical Setting: Crime and Law Enforcement in São Paulo
The state of São Paulo had 41.3 million inhabitants in 2009. It is the largest and most important
economically state in Brazil. It is comparable to a middle income country, with GDP per capita of around
U$15,000 in 2009.5 After the troublesome 1990s, the years 2000s brought better economic performance
and improving social indicators. However, social indicators still lag behind countries with comparable
income. Income is poorly distributed (Gini coefficient of 0.49 in 2009) and almost 5% of the adult
population was illiterate in 2009.
Violence was at moderate level in the end of the decade 2000s, after reaching high levels in the late
1990s. Homicides were a little more than 10 per 100,000 inhabitants in 2010, down from 33 per 100,000
inhabitants in 1999. Murders have dropped steadily for over a decade (see De Mello and Schneider, 2010).
In Brazil, law enforcement is primarily the attribution of state governments. Executive and
administrative authority rests with the state-level secretaries of security (the Secretarias Estaduais de
Segurança Pública), which respond directly to the governor, who allocates the budget to the secretary. The
administrative and strategic decisions are made by the state security secretary, who is appointed by the
governor. The institutional and administrative structure of law enforcement is determined by
constitutional law. Enforcement is shared between two police forces that respond directly to the secretary:
Webster et al (1997), Zimring and Hawkins (1997), Black and Nagin (1998). For a more complete account of the debate, containing
Lott’s responses to his critics, we refer to David Friedman’s website
(http://www.daviddfriedman.com/Lott_v_Teret/Lott_Mustard_Controversy.html).
5 Aggregate data cited here are from IPEADATA (http://www.ipeadata.gov.br/) and Fundação SEADE (http://www.seade.gov.br/).

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the military police, responsible for patrolling and crime prevention, and the civil police, an investigative
agency. The commanders of the two police forces are also appointed by the governor. Differently from the
US, sheriffs are not elected but appointed after passing competitive public examinations.
The federal and municipal levels have a secondary participation in law enforcement. Repression of
drug trafficking is shared between the federal police force – Polícia Federal, equivalent to the American FBI
– and the state-level Secretarias. The Polícia Federal is responsible for dealing with cross-state and
international traffic. The state-level police forces have jurisdiction within state borders. Unlike the state-
level Secretarias, municipal police forces (Guardas Municipais) are not mandated by the constitution but
rather a choice of the municipality. As of 2006, 28% of municipalities in São Paulo state had a municipal
police force. Of those police forces, 52% carried firearms and were involved in street-level policing.
4. Data
We use information from two data sources. From the Secretaria de Segurança do Estado de São Paulo
we have annual data at the municipal level on the total number of property crime, car robbery, theft,
attempted homicides, apprehension of firearms and assault. The data runs on an annual frequency from
2001 through 2007. The state of São Paulo is one of the few to have high quality police report data. Under-
reporting on car robbery is residual because of insurance and legal liability reasons (Biderman et al, 2010).
For categories such as assault and attempted murder, victimization survey data suggest that under-
reporting – which is high - has been declining over time, which lead us to take results using this data with a
grain of salt (De Mello and Schneider, 2010). For minor felonies such as theft under-reporting is still
rampant. Data on illegal firearms possession are available but we choose not to use it in the regression
analysis because it is contaminated with enforcement (De Mello and Schneider, 2010).
Data on violent deaths are from the DATASUS, the hospital dataset from the Ministry of Health. The
data follow the taxonomy from the World Health Organization. From DATSUS we use homicides, homicides
by firearms, suicides and suicides by firearms. Brazilian hospital data is generally considered high quality,
especially the one from São Paulo (Cerqueira, 2011). Data on population and age distribution are also from
DATASUS. Hospital data is available starting in early 1990s. For the regression analysis we use only data
running from 2001 because this is the period available for the other types of crimes. For the preliminary
graphical analysis of homicides and suicides we go to back to 1998 to have a longer view (see Section 5
below). This is important because homicides and suicides –relatively rare events – are noisy.
We focus on a window of four years after and three years before the establishment of the ED. The
choice is partially data driven, and partially conceptual. Municipal-level data police-report data are only
available starting in 2001. The new, tougher restriction on firearms registration, possession, and carrying
was effective with the sanctioning by the president in December 2003. Four years should be enough time to
capture the impact of the law, and we cut the sample in 2007.

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Because our main variables of interest are very noisy in smaller cities, we focus on cities with more
than 50,000 inhabitants on average in the baseline (2001 through 2003). In particular, the main proxy for
the prevalence of firearms – suicides by firearms – is particularly noisy because it is rare event (see Section
7.1 below). 6
5. The Intervention and the Theoretical Mechanisms
In Brazil, individual rights are legislated at the federal level. In December 2003, the Brazilian
Congress passed Lei Nº 10.826, the Estatuto do Desarmamento (Disarmament Act, henceforth ED). The ED
legislates on many aspects of firearms possession, such as right-to-carry, procedures to apply for
possession, and penalties for violation. Among other things, it creates a National Registry (SINARM) where
all fire weapons sold have to be registered, and it establishes that licenses are to be issued by the Polícia
Federal. It also significantly increases the requirements and the red tape for applying to a fire gun permit. In
order to possess a gun, the applicant cannot have a criminal record, must have a formal job, show proof of
residency, pass a psychological exam, take a course on handling guns, and pay a fee close to U$1,000.00
(Article 4). Registration (i.e., possession) only allows for possession inside one’s residency (or place of
business). Article 6, which regulates the right-to-carry, forbids carrying fire arms except in special cases.7
Before the ED, registration implied the right-to-carry.
The ED changed the penal status of illegal possession and illegal carry of fire arms from misdemeanor
to felony. Before ED the penalty for illegal possession and carrying was 1 to 3 months of incarceration or a
fine; typically, the offender was out on bail. The ED establishes a penalty from 2 to 4 years and fine; the
offender does not have the right to bail if the gun is not properly registered (Article 14).
We have no direct evidence on enforcement. São Paulo’s police force is known as one of the best in
Brazil, and often credited with the having played a significant role in the reduction of violence after the late
1990s (Kahn and Zanetic, 2007; De Mello and Schneider, 2010). Kahn and Zanetic (2007) document a major
enforcement effort starting in the mid 1990s to crack down on illegal possession and carrying of fire arms.
We expect the ED to impact the prevalence of firearms through several channels. First, a demand
channel: people will demand less legal arms because of the increased red tape and requirements in
applying, and the reduced benefit from possessing a legal gun (no longer being able to carry outside one’s
residence). Second, because once legal firearms are a source for the illegal market, the reduction in the
demand for legal firearms will reduce the supply of illegal firearms available for criminals and non-
criminals alike. Thus, the impact of the ED on prices will depend on the relative sizes of the supply and
demand shifts. Third, non-criminal owners of illegal registered and unregistered firearms will carry less
6 Robustness analysis was performed using all cities and is available upon request.
7 Exceptions: military personnel, state and federal police officers during work hours, municipal police officers in cities with
population over 50,0000 inhabitants, private security employees (properly registered with the SINARM), sportive hunters
(properly registered with both the official league and the SINARM), rural dwellers whose subsistence depends on hunting.

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because of the increased penalty for illegal possession. Finally, it is not clear theoretically how the number
of guns carried by criminals changes in equilibrium. It depends on whether guns carried by criminals and
non-criminals are strategic substitutes or complements, and on the effect on prices of illegal firearms.
Some anecdotal evidence on prices is available. According to the Polícia Federal, the price of illegal
firearms has increased dramatically after 2003. Federal Marshall Marcos Dantas, in a 2008 interview,
reports that the price of the AK-15 jumped from US$ 2,500 in 2005 to more than U$10,000 in 2008.8 The
black market price 9mm pistol in 2008 was U$1,250, up from U$400 in 2005.9 In addition, a Parliamentary
Commission on Firearms from the Rio de Janeiro State Assembly gathered information on the type of fire
arms apprehended from 2000 onwards. The proportion of homemade firearms, which remained constant
at a negligible 0.2% from 2000 through 2003, starts to rise in 2004, reaching almost 11% in 2007. On the
other hand, the proportion of handguns (pistols and revolvers) among apprehended guns dropped from
roughly 79% in the 2000-2003 period to 68% in 2007. Assuming homemade firearms are a substitute for
non-homemade, this evidence suggests an increase in the price of non-homemade weapons after 2003.10
Increases in prices are only compatible with a large inward shift in supply, because the demand effect
would tend to reduce prices.11
Before proceeding with the empirical strategy, we investigate whether the aggregate pattern of the
data suggest that the ED did in fact have an impact on the prevalence or availability of firearms. Figure 1
depicts illegal carrying of firearms per 100,000 inhabitants at the state level from 2001 through 2007. The
figure shows two facts: 1) illegal carrying had been declining before the law; 2) the decline accelerated after
2004. Illegal carrying confounds enforcement and the prevalence of arms. However, it is not theoretically
clear whether illegal possession should go down with the ED, especially in the short run. Apprehension
could have gone up because ED turned carrying fire weapons (even registered) into a felony.
8 See the newspaper article (in Portuguese) at http://agenciabrasil.ebc.com.br/noticia/2008-10-24/aumento-da-repressao-faz-
preco-de-armas-quadruplicar-no-mercado-ilegal-avalia-pf
99 A demand shift for unregistered firearms due to the increased penalties for illegal possession and carrying would have
caused a reduction in prices.
10 Source: compilation by Julio Pucerna based on the information on the Relatório da Comissão Parlamentar de Inquérito das Armasi,
Assembléia Legislativa do Estado do Rio de Janeiro (2010). Of course, this pattern could also be rationalized by an advancement in
the technology of household production of firearms, or by an improvement in apprehension of homemade firearms. There is no
evidence on neither of these alternative explanations.
11 It is conceivable that the demand for illegal arms by criminals increases after the ED if arms on the hands of non-criminals
and in the hands of criminals are strategic substitutes. In this case, two empirical facts should follow: a reduction in the
prevalence of firearms and, through the deterrence effect, an increase in “contact” property crimes. Both hypothesis are
testable, and are tested for below.

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Figure 2 depicts our two main measures of firearms prevalence: suicides by firearms per 100,000
inhabitants and the ratio suicides by firearms-to-suicides by other means (see Section 6.1). Suicide data is
noisy. Panel A shows that suicides by firearms per 100,000 inhabitants were all over the place before 2004,
but seemed to be dropping since 2001. However, a larger drop occurs is 2004 (starting from a lower level),
and suicides by firearms stabilizes at a low level thereafter. Panel B depicts the ratio of suicides by firearms
to suicides by other means. The 2003 - 2004 drop is now even more pronounced. The ratio, quite noisy
before 2004, drops steadily thereafter. Bearing in mind the micronumerosity problem of this graphical
analysis, the data generating process seem to have changed after 2003.
60 70 80 90 100 110
2001 2002 2003 2004 2005 2006 2007
Source: Secretaria de Segurança - Estado de São Paulo
2001 through 2007
Fig 1: Firearms Apprehended per 100 thousand inhabitants
ED passed

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Figure 3 depicts homicides by firearms per 100,000 inhabitants over the same period. It shows two
facts: 1) homicides increased sharply in the 1990s, reaching a peak in 2001, and then dropped steadily; 2)
the reduction in homicides accelerated after 2003. Figure 4 depicts homicides perpetrated not by firearms.
Again, two facts emerge. First, homicides not perpetrated by firearms have been dropping since 1998. The
surge in homicides of the 1990s seems to be an epidemic of violence perpetrated by firearms. Second, and
in contrast with homicides by firearms, there is no increase in the pace of reduction after 2003.
.55 .6 .65 .7 .75
By 100 thousand inhabitants
1998 1999 2000 2001 2002 2003 2004 2005 2006 2007
Source: Ministério da Saúde
1998 through 2007
Panel A: Suicides by Firearms
.15 .16 .17 .18 .19 .2
1998 1999 2000 2001 2002 2003 2004 2005 2006 2007
Source: Ministério da Saúde
1998 through 2007
Panel B: Suicides: Firearms/Other Means
Fig. 2: Suicides
ED Passed

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10 15 20 25 30
100 thousand inhabitants
1998 1999 2000 2001 2002 2003 2004 2005 2006 2007
Source: Ministério da Saúde
1998 through 2007
Fig. 3: Homicides by Firearms
510 15 20 25
100 thousand inhabitants
1998 1999 2000 2001 2002 2003 2004 2005 2006 2007
Source: Ministério da Saúde
1998 through 2007
Fig. 4: Homicides by non-Firearms
ED passed
ED passed

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Figure 5 depicts the dynamics of the index of property crime. The first noticeable feature is the jump
in 2003, which illustrates the perils in interpreting pure time-series variation in property crimes. Reporting
of thefts of cellular phones, which increased strongly in the beginning of the 2000s, is the main culprit for
explaining the jump. Second, no distinguishable pattern arises between 2003 and 2004/2005. Figure 6
2600 2700 2800 2900 3000
2001 2002 2003 2004 2005 2006 2007
Source: Secretaria de Segurança Pública do Estado de São Paulo
2001 through 2007
Fig 5: Property Crime per 100 thousand inhabitants
160 180 200 220 240 260
2001 2002 2003 2004 2005 2006 2007
Source: Secretaria de Segurança Pública do Estado de São Paulo
2001 through 2007
Fig 6: Car Robbery per 100 thousand inhabitants
ED passed
ED passed

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depicts the trends in car robbery. Besides the secular decline throughout the 2000s, no other feature is
noticeable. In particular, no visible change occurs after 2003.
6. The Empirical Strategy
6.1 The Causal Impact of the ED (Reduced-Form)
We use a strategy inspired in Cook and Durrance (2011). Identification comes from assuming that the
ED had a stronger impact in places where firearms were more prevalent when the policy was established.
We assume that the impact of the ED is moderated by the proportion of crime that is attributable (or
prevented by) to fire guns.
Let  be the crime rate per 100,000 inhabitants at city i in year t. We decompose  into crimes
attributable to firearms (
) and crimes non-attributable to firearms (
):
  
 
 (1)
The formulation allows firearms to save crimes, i.e.,
 , although this is clearly a counterfactual object.
Let  the homicide rate at city i at the baseline year b. Let 
 be the fraction of crimes attributable to
firearms prevented by (or induced by) the ED between the baseline year b and year t. Assuming that the
fraction of homicides prevented by the ED is constant across cities, we postulate that:

  
 (2)

󰇛  
󰇜
 (3)

󰇛󰇜 means that the ED reduces the number of crimes between years b and t (the lethality hypothesis
is dominant). If 
 , then ED causes increase in crime. First-differencing (3) and (2) we have:

 
  
   (4)

 
 
 

 (5)
Adding (4) and (5):
  

 (6)

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Note that all time-invariant heterogeneity in the levels of crime will be accounted for by the
differencing procedure. We do not assume that the amount of crimes attributable and non-attributable to
firearms would stay constant in the absence of the ED. In fact, we allow changes in crimes attributable and
not attributable to firearms have a common component  (year fixed effect), depend on changes in
controls, on baseline crime, and on a random unobservable city-year specific shock that is common for
crimes attributable and non-attributable to firearms ():
  

       (7)
where  includes changes in population and crime-prone population (ages 15 through 24). More
importantly,  is the baseline level of crime. Its inclusion is crucial for causal
interpretation. Aggregate crime is dropping in the state of São Paulo. It is conceivable that it will drop more
where violence was higher to start with because of mean reversion, or because of unobserved policy
interventions, which are more likely to be implemented in more violent places. Including 
mitigates the possibility that 
 captures these spurious effects.
We have four cross-sections: four equations (7), one for each year from 2004 through 2007. We
stack them and estimate an average . We do estimate year effects separately.
  
       (8)
If the ED reduced crime, then   . Otherwise   .
Implementing the estimation of (8) requires observing 
. For homicides, we could use the number
of murders perpetrated with firearms, which we observe. We do not follow this path for two reasons. First,
we do not want to attribute all homicides perpetrated by firearms to firearms.12 Second, we have no
equivalent information for other crimes. We assume that the baseline number of crimes attributable to
firearms depends linearly on the availability of firearms:

       (9)
Combining (8) and (9), we have:
            (10)
12 We will use the information on homicides by firearms to corroborate the idea that the relative importance of firearms in
homicides depends on our measure of the prevalence of firearms, and as a robustness check.

15
where    and   . We cannot identify  because b is not identifiable. However,
knowledge of  (which is identifiable) helps us quantify the impact of the ED assuming b is positive. If the
deterrence hypothesis is dominant, then  ; on the other hand, availability of firearms increases crime
postulates that   .
is also unobservable. We adapt Cook and Ludwig’s (2002) and use the number of suicides
perpetrated by firearms per 100,000 inhabitants. A small digression on the choice of proxy is warranted.
No direct measure of the number of legal firearms circulating is available in Brazil. Let alone illegal
firearms. Not even good quality survey data are available at the aggregate level. For the US, the suicide by
firearms measure is well validated. Suicides by firearms outperform all other measured used in the
literature. Using aggregate survey data as a benchmark, Azrael et al (2001) show that the correlation
between survey-based data and the proportion of suicides by firearms is higher than two other clean
measures: membership in the National Rifle Association, and subscription to Guns & Ammo (Duggan,
2001).
Evidence suggests that suicides by firearms are related to crime, which poses challenges to
identification. Potash et al. (2000) show that suicides are related to psychological and social characteristics,
such as bipolar disorder or substance abuse.13 However, Figure 7 shows that suicides in general show little
resemblance with homicides or suicides by firearms.
13 Insofar as substance abuse causes both suicides and homicides, one could be concerned that suicides may captures changes in
substance abuse at the local level. The literature normally deals with this issue by using the proportion of suicides by PAF,
assuming implicitly that substance abuse increase the odds of suicide in general, not suicides by firearms in particular.
3.2 3.4 3.6 3.8 44.2
By 100 thousand inhabitants
1998 1999 2000 2001 2002 2003 2004 2005 2006 2007
Source: Ministério da Saúde
1998 through 2007
Fig 7: Suicides not by Firearms
ED passed

16
There is a concern with the use of suicides by firearms in the context of the Estatuto do
Desarmamento. The ED has sharply increased the penalties for illegal possession. It is conceivable that
following the ED people that would surrender the guns kept at home, reducing suicides by firearms.
However, one may be skeptical of this mechanism because the chances of getting caught at home with an
illegal firearm are slim. The “ease-of-acquiring-guns” is a more convincing reason why less availability of
firearms translates into fewer suicides by firearms (Ludwig and Cook, 2002). The ED has made it more
difficult to acquire a legal weapon, i.e., an inward shift in the supply of legal firearms. The legal and illegal
markets have communicating vases; thus, the general equilibrium effect is an increase in prices in both
markets, and an overall reduction in equilibrium quantity of firearms. Higher prices mean fewer suicides
with firearms. In fact anecdotal evidence presented in section 5 suggests that prices in the illegal market
increased sharply after 2003.
The literature normally uses the proportion of suicides by firearms. In our case, it is natural to use the
number suicides by firearms (per 100,000 inhabitants) because the specification calls for a variable that
resembles the absolute number, not a relative measure. In all regressions we include the total number of
suicides per 100,000 inhabitants as a control to avoid capturing spurious effects due to substance abuse for
example. We also use the ratio of suicides by firearms to probe the robustness of results.
We also measure firearms prevalence by the number of firearms apprehended per 100,000
inhabitants. Because apprehensions are contaminated with enforcement, the apprehension data has limited
usefulness. We use it for robustness purposes only.14
6.2 The Causal Impact of the ED on Firearms Availability (Mechanism or First-Stage)
We first estimate the impact of ED gun availability. The credibility of any estimate of the causal
impact of ED on crime rests on documenting the mechanism. The ED must have had an impact on the
availability of firearms. Incidentally, the impact of the ED on availability will serve as the first stage when
estimating the causal impact of firearms on crime.
The estimation strategy is similar to the one we use to recover the causal impact of the ED on crime.
We postulate that any intervention to reduce the availability of firearms has a larger impact in reducing the
number of guns per capita depends on the prevalence of guns at the baseline. Let 
 be the fraction of guns
out of circulation at year t because of the ED. We postulate that
 󰇛  
󰇜 (11)
14 We could control for the number of policemen at the city level, an imperfect measure of enforcement intensity. Because
enforcement is endogenous to crime, its inclusion would solve one problem by creating another, possibly harder to solve.

17
Taking differences between t and the baseline year b in (11), we have:
      
 (12)
We do not estimate 
, but stack the four cross-sections and estimate an average . The estimated
model is
          (13)
where  is a random shock. Again, guns are proxied by the number of suicides by firearms per 100,000
inhabitants. We cannot control for the baseline level of dependent variable as we do in the crime equations.
We control for the baseline level of homicides, the best measured crime category, to account for mechanical
drops in guns in places that were more violent to begin with. We hypothesize that the ED reduced the
prevalence of firearms, i.e.,   .
6.3 Estimating the Causal Effect of Firearms on Crimes
Under the identification assumption that the ED caused a change in crime only through its impact on
the availability of arms, changes in firearms explained by the baseline number of firearms are exogenous
variation to estimate the causal impact of firearms on crime. Equation (13) is the first stage.
The crucial identification assumption is that baseline firearms does not belong to the structural crime
equation (exclusion restriction). The inclusion assumption (i.e., what justifies the first stage) is that the
impact of the ED is stronger where there were more arms in the baseline. Sure enough, firearms in 2003
cannot cause crime in 2007 above and beyond firearms in 2007. Still, baseline firearms can be
systematically related to unobserved factors that belong to the structural equation of crime. Violence was
particularly high where baseline arms were high, and bound to drop anyway because of mean reversion or
because of stronger enforcement reaction at the local level. Both issues can be dealt with by controlling for
the baseline level of crime.
7. Results
7.1 Summary Statistics
Table 1 contains the summary statistics on the crime categories investigated both for the 118 cities
included in the main sample (more than 50,000 inhabitants on average during years 2001-2003), and
statewide. Some relevant facts emerge. The typical city in the main sample was violent in the years 2001-

18
2003: 21.09 homicides per 100,000 inhabitants on average, with a standard deviation of homicides across
cities of 12.01.15 Statewide violence was considerably higher: 37.66 homicides per 100,000 inhabitants.16
From 2001 through 2003, 94% of homicides were perpetrated by firearms in a typical city in the main
sample. Statewide, “only” 67% of homicides were perpetrated by firearms. From 2004 through 2007,
homicides perpetrated by firearms dropped in the main sample more than homicides by other means. In
2007, homicides by firearms represented no more than 60% of all homicides in a typical city in the main
sample.17 In contrast, most suicides are committed through means other than firearms. Suicides by firearms
are not only rare – only 0.70 per 100,000 inhabitants –, but also very volatile across cities, with most noise
coming from smaller cities. In about 8% of the cities no suicides occurred during the 2001-2003 period.
Interestingly, averages suggest that suicides by firearms dropped by more than 20% over period, while
suicides in general remained flat. Property crime and vehicle robbery also dropped after 2003, suggesting a
general reduction in crime during the period. However, they dropped much less than homicides.
[TABLE 1 HERE]
7.3 The Causal Effect of the ED on Crime (the Reduced Form)
7.3.1 Homicides
Table 2 contains estimates of the parameters in equation (10) and a few variants. The main
outcome is homicides by firearms. But we also gauge the impact of the ED on homicides non-firearms,
which could serve both as a placebo and to capture any substitution effect away from firearms. All reported
standard errors are computed by clustering observations at the city level.18 First, we regress the difference
between homicides by firearms at t and the baseline on the measure of firearms prevalence at the baseline,
i.e., suicides by firearms per 100,000 inhabitants (Column 1). Because suicides by firearms are quite noisy,
the baseline is the average from 2001 through 2003. The estimated coefficient on firearms proxy () is -
2.842 and statistically significant at the 10 percent level. The ED reduced the number of homicides.
[TABLE 2 HERE]
15 The World Health Organization considers endemic violence rates above 10 homicides.
16 Averages for the main sample treat cities with different populations equally. Larger cities, which are more violent, have more
impact on aggregate statewide violence.
17 Figure not reported in Table 1. In 2007, there were 8.21 and 13.67 homicides by firearms and overall homicides in the main
sample.
18 Clustering is important in our case. The model is a stacked cross-section, and the main regressor only varies between, not within,
city.

19
In Column (2) we include the baseline homicides. Firearms are more prevalent in more violent
places. It is plausible that homicides dropped more sharply where violence was higher because of mean
reversion or unobserved crime reducing policies. Indeed, the coefficient on baseline homicides is highly
significant statistically. As expected, the impact of the ED is now smaller, but only slightly (-2.637), but is
more precisely estimated (statistically significant at the 5% level). In Column (3) we define treatment not
continuously but as a dummy that assumes the 1 if the city had suicides by firearms above the median in
the baseline, 0 otherwise. Defining treatment as a dichotomous variable simplifies the computation of the
number of lives saved by the ED. The coefficient associated with the treatment dummy is -2.500 (p-value <
3%), similar to the coefficient associated with the continuous treatment variable in column 3. The baseline
homicide rate in the “treatment” group was 19.81. Thus the impact of the ED is to reduce the homicide rate
by 12.6%. This represents 2,000 lives from 2004 through 2007.
In Column (4), the dependent variable is homicides not perpetrated by firearms. The impact of the
baseline prevalence of firearms is now indistinguishable from zero (point estimate is positive but
negligible, and statistically insignificant). In Column (5) we weight the observations by population, a
common procedure in the literature because homicides are noisier is smaller cities (and suicides by
firearms even noisier). In addition, weighing observation by population yields an estimate that is
representative of the aggregate impact of the ED. The estimated coefficient is now -4.075. Performing the
same exercise that we did in Column (3) (omitted for conciseness), the ED caused an 11% drop in
homicides. Because larger cities are more violent, weighing by population represents a higher number of
lives saved: 2,750 lives. In Columns (6) through (9) we re-estimate the same models using another
commonly used in the literature: the ratio suicides by firearms/suicides by other means. If anything,
estimates are more precise.19
Table 3 contains robustness exercises. We first report estimates when we include the lag of the
dependent variable, which we hope will pick up any additional mean reversion, or unobserved policy
reactions, not captured by baseline homicides.20 Columns (1) and (2) have the results for the un-weighted
and weighted samples. The coefficient associated with the lagged dependent variable is positive and highly
statistically significant, even after the inclusion of baseline homicides. The model is becoming close to
saturated, with an R2 of almost 80%. The inclusion of the lagged dependent variable does absorb some of
the effect due to the baseline firearms measure (and the baseline homicides). But homicides still dropped
more where there were more firearms in 2003 (and more precisely estimated than in Table 2). We then
run two specification robustness test: Deltas-in-Logs and Logs-in-Logs, for the weighted and un-weighted
procedures. Coefficients are more precisely estimated and, in terms of practical significance, results are in
line with Table 2.
19 In terms of practical significance, magnitudes are similar. We omit the discussion for conciseness.
20 We do not dwell into the difficulties in identifying lagged dependent variable models, especially because we have a time-series of
four years.

20
7.3.3 Property Crime and Car Robbery
We now change the dependent variable to an index of property crime per 100,000 thousand
inhabitants (Table 4).21 The right-hand side specifications are the same as in Table 2. Columns (1), (2) and
(3) replicate Columns (1), (2), (4) in Table 2 (Column 3 – homicides by non-firearms – is not replicable for
property crimes). In all three cases the estimated coefficient is positive, meaning property crime increased
where arms were more prevalent in the baseline, in line with the deterrence hypothesis. However, none of
the results are statistically significant. The property crime index is not particularly imprecise in small cities
due to the rarity of the event. Thus, we take a leap and estimate the model for the sample of all 648 cities in
the state of São Paulo, both weighting and un-weighting observations by population (Columns 4 and 5). The
estimated coefficients are small and oscillate around zero. In both cases they are insignificant statistically.
The remainder of the table replicates the results using the ratio of suicides-by-firearms-to-suicides-by-
other-means measure of firearms prevalence. Results are similar.
Absence of statistical significant could be due to lack of precision. However, the coefficients are not
large in magnitude. We cannot gauge practical significance in terms of contribution to the drop in property
crimes because most coefficients suggest that, if anything, the ED has caused an increase in property crimes.
Thus we measure it in terms of standard deviations. The largest positive estimated coefficient is in Column
(3), 53.186, and represents roughly 13% of the standard deviation of the change in property crimes (396 in
Table 1). In contrast, the equivalent coefficient associated with homicides – -4.075 (Table 2, Column 5) –
amounts to 38% of standard deviation of the change in homicides by firearms (10.69 in Table 1).
The use of the property crime index is problematic for two reasons. First, there is time-varying
under-report. Survey data suggest that property crime under-reporting is rampant in São Paulo.22 In
addition, under-reporting may be changing over time, and we cannot guarantee that the dynamics across
cities are similar. The second reason lies in the composition of the index. The deterrence hypothesis
applies more naturally for robberies. The Brazilian Penal Code defines thefts as occurring without the use
of physical threat. Thus, guns should play less of a role in deterring thefts.
We mitigate both problems by focusing on car robberies, which are perpetrated by use of physical
threat and are fairly well-reported to the police.23 Table 5 has the results of the same models in Table 4. The
sign of the coefficient associated with baseline car robberies is positive across the board, in line with the
deterrence hypothesis. However, we can never reject the zero-null at standard significance levels. In terms
21 The property crime index is the sum of all property crimes. It includes robberies, thefts, larceny and burglaries.
22 Total property Crime rates in São Paulo are a little lower than the US. Car theft and car robbery are less susceptible to under-
reporting because of insurance and legal liability reasons. Not surprisingly, they are significantly higher than in the US. See
Biderman et al (2010).
23 Car robbery and theft are well reported for insurance and to avoid having one’s name associated with crimes perpetrated with
stolen cars (Biderman et al, 2010).

21
of magnitudes, the largest estimated coefficient represents roughly 39% of a standard deviation in the
change in car robberies, about the same as the largest estimated impact on homicides. All other coefficients
are smaller in magnitude (in terms of standard deviations) than their homicide counterparts. Results in
Columns (5) through (10) show essentially the same facts.
[TABLE 4 HERE]
[TABLE 5 HERE]
In summary, we have no evidence that the ED caused an increase in property crimes in general. If
one is willing to interpret statistically insignificant estimated coefficients, in the best case there is weak
evidence that the ED caused an increase in car robberies.
7.4 The Causal Effect of the ED on Gun Availability (the Mechanism or First-Stage)
Table 6 shows estimates of several specifications of the model in equation (13). Column (1), show
that firearms’ prevalence dropped more pronouncedly where they were more prevalent in the baseline.
Cities with higher baseline arms were also more violent to begin with. In Column (2) we include baseline
homicides to account for baseline differences in violence. Results are unchanged.
Reversion of the mean could rationalize results. In Column (3) we include the lag of the dependent
variable as a regressor, which will capture reversion of the mean, at least partially. The estimated impact of
the ED on firearms availability is now smaller, but still negative and statistically significant.24 In Column (4)
we perform a placebo exercise by changing the dependent variable to the suicides perpetrated with means
other than firearms. We find no impact of ED. In columns (5) and (6) we weight estimates by population
and run the same model as in Column (2) for the whole sample and for our preferred sample of cities with
more than 50,000 thousand inhabitants. Results are similar. In Columns (7) through (9) we repeat some of
the exercises for the alternative measure of baseline firearms prevalence. Results are unchanged.25
[TABLE 6 HERE]
24 Given the difficulties in identifying dynamic models, we only report OLS regressions from Table 4, column 7.
25 For conciseness we do not report all exercises. Results always remain similar.

22
7.4 The Causal Effect of Firearms on Homicide (the structural equation)
Table 6 shows that the enactment of the ED reduced the availability of arms as measured by the
prevalence of suicides by firearms. Assuming the impact of the ED on homicides is intermediated by its
impact on the availability of firearms, we can use the baseline prevalence of firearms instrument for
changes in firearms prevalence and estimate the causal impact of firearms on crime.
The exclusion restriction is plausible in our data. It is hard to imagine any reason why criminals
would take into account the stricter gun law when deciding to commit a crime. The fact the ED is a national
legislation helps the credibility exclusion restriction because the ED was not implemented as a local
response to crime, thus is it exogenous to variation across cities.
The identifying exogenous variation is the differential drop in in the prevalence of firearms
depending on the initial baseline prevalence of firearms. Because prevalence was higher in more violent
cities, reversion to the mean in both variables, or unobserved local policy responses to high crime, could
both cause the instrument to capture unobserved heterogeneity in the structural equation relating arms to
crime. This possibility poses little threat to our identification strategy. Baseline prevalence of firearms is
associated with subsequent reductions in homicides even after controlling for baseline homicides (see Table
2). Thus, the reduced-form association between these two variables is not driven by reversion to the mean.
In addition, if more violent cities adopted other (unobserved) crime fighting policies circa 2003, the
baseline homicides will capture this variation in policy reactions.
[TABLE 7 HERE]
Estimated coefficients are in Table 7. Column (1) has our preferred specification, with all controls
included in the first-stage and the reduced form. A reduction of one suicide by firearms per 100,000
inhabitants causes a reduction of 2.155 homicides by firearms per 100,000 inhabitants. To assess practical
relevance, 1.15 is roughly one standard deviation in ΔSuicides by firearms per 100,000 inhabitants; the
standard deviation of ΔHomicides by firearms per 100,000 inhabitants is 10.69. Thus a one standard
deviation reduction in our measure of firearms prevalence causes a drop of roughly on fourth of a standard
deviation in homicides by firearms (󰇛  󰇜
). In Columns (2) and (3) we weight observations
according to population and estimate the model for the main sample and for all cities. Results, if anything,
are stronger. In Column (4) we change the dependent variable to all homicides (not only those perpetrated
by firearms). As expected the estimated coefficient is much lower. In Columns (5) through (10) we change
the instrument to the ratio suicides by firearms – to – suicides by other means. Results are similar.
Tables 8 and 9 contain the structural results for property crime and car robbery, which essentially
show that changes in the prevalence of firearms has no impact property crime and car robberies.26
26 This should not come as a surprise given that the reduced form showed no impact of the ED on property crime and car robbery.

23
[TABLE 8 HERE]
[TABLE 9 HERE]
7.5 An Alternative Measure of Firearms: Arms Apprehended by the Police
For robustness and validation purposes, we present a summary of previous results using an
alternative measure of firearms prevalence: the number of arms apprehended by the police per 100,000
inhabitants.27 Table 10 shows both the first-stage and the impact of firearms on suicide by firearms and
vice-versa. In Column (1) we see that the apprehension of firearms dropped faster where apprehension
were more frequent at the baseline (first-stage). In column (2) we include baseline homicides to control for
baseline violence. Results are unchanged. It is possible that enforcement increase more sharply where guns
were more prevalent. In column (3) we include the change in enforcement (which is admittedly
endogenous, but it is the best one can do to control for enforcement). Results are unchanged. In columns
(4) and (5) we weight by population and use the sample of more than 50,000 inhabitants and the whole
sample, respectively. Results are again similar.
Columns (6) and (7) present two validation exercises. First, we regress changes in firearms
prevalence on the baseline suicides by firearms (6), and then we regress changes in suicides by firearms on
baseline apprehension. In both cases, prevalence of firearms drops more intensely where prevalence was
higher when using the other proxy of baseline firearms prevalence. This increases our confidence that first-
stage estimates in Tables 6 and 8 are not driven mechanically by mean reversion, for example.
[TABLE 10 HERE]
Table 11 shows the reduced form and the structural estimates. Results should be viewed with a
grain of salt, as explained above: apprehension is contaminated by enforcement, which we cannot account
for. The dependent variable is changes in homicides. Column (1) shows a strong in impact of baseline
apprehensions on homicides. However, most of the impact is capturing the fact more arms were
apprehended where homicides were higher to begin with. Including baseline homicides reduces the impact
of baseline apprehension on homicides by two thirds. But we still find that homicides dropped more where
baseline apprehensions where higher. Results remain similar when we weight by population (Columns 3
and 4). Columns (5) through (7) show the structural estimates. The point estimate in column (5) is positive
as before, but precision is low and we cannot reject the zero-null. In columns (6) and (7) we weight by
population, and use both preferred sample (more than 50,000) and the whole sample. We also find that
27 For conciseness we do not present all results using the alternative measure. They are available upon request.

24
more arms cause more homicides. Now we are able to reject the zero-null at standard significance levels
(5% and 10%).
[TABLE 11 HERE]
Finally, Tables 12 and 13 present reduced-form and structural estimates for the impact on property
crime and car robbery. If results in Table 12 are interpretable at all, an increase in the prevalence of
firearms increases property crime. But in none of the cases estimates are significant statistically or
practically (except for the reduced-form when we do not control for baseline property crime, a result that is
clearly nor interpretable as causal). We find similar results when the dependent variable is car robberies
(Table 13).
In summary, when using firearms’ apprehension, we find similar results across the board: firearms
increase homicides, and estimates are mostly undistinguishable from zero for property crime and car
robberies.
[TABLE 12 HERE]
[TABLE 13 HERE]
8. Discussion
We estimate that the ED caused saved some 2,800 lives in the state of São Paulo over the course of a
four-year period (2004 through 2007). If we were to extrapolate this effect for the whole country, it would
have meant that the ED saved almost 14,000 lives, roughly 7.4% of the homicides over the period.
This paper has two main findings. First, the ED – a national-level policy that restricted the legal
possession of firearms and increased the penalties for illegal possession – reduced the prevalence of
firearms. The enactment of the ED is also associated with a non-negligible reduction in homicides, with no
discernible impact on an index of property crime and car robbery. Second, we recover a causal impact of
firearms on homicide, confirming previous findings that firearms cause homicides. We find no systematic,
interpretable impact on property crime and car robbery

25
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27
Table 1 Summary Statistics
Mean Std Deviation
Homicides (Baseline 2001-2003), main sample
21.09
12.01
Homicides (Baseline 2001-2003), statewide
37.66
103.08
Homicides by Firearms (Baseline 2001-2003), main sample
19.76
16.48
Source: Secretaria de Segurança do Estado de São Paulo and Ministério da Saúde. Main sample: Unweighted averages across the 118
cities with population over 50,000 inhabitants on average during years 2001-2003. Years in parentheses: averages across these
years. Statewide: all 635 cities in the state of São Paulo, weighted by population. All Δs with respect to baseline (2003). All figures
per 100,000 inhabitants.
ΔCar Robbery (Baseline 2004-2007), main sample
-10.83
49.98
Car Robbery (Baseline 2001-2003), statewide
230.33
226.29
Car Robbery (Baseline 2001-2003), main sample
0.70
0.49
110.14
157.88
Property Crime (Baseline 2001-2003), main sample
795.87
Property Crime (Baseline 2001-2003), statewide
2790.57
967.50
2561.10
ΔSuicides by non-Firearms (2004 - 2007), main sample
ΔProperty Crime (2004 - 2007), main sample
-212.64
396.35
Suicides by Firearms (Baseline 2001-2003), main sample
0.05
2.72
ΔSuicides by Firearms (2004 - 2007), main sample
-0.17
1.15
Homicides by Firearms (Baseline 2001-2003), statewide
25.39
16.66
Suicides by non-Firearms (Baseline 2001-2003), main sample
3.48
1.76
ΔHomicides By Firearms (2004-2007), main sample
-7.33
10.69
ΔHomicides By non-Firearms (2004-2007), main sample
-2.75
5.73

28
Table 2, Dependent Variable = ΔHomicides per 100,000 inhabitants†
(1) (2) (3) (4)
(5)a(6) (7) (8) (9)a
Homicides by
Firearms
Homicides by
Firearms
Homicides by
Firearms
Homicides by
non-Firearms
Homicides by
Firearms
Homicides by
Firearms
Homicides by
Firearms
Homicides by
non-Firearms
Homicides by
Firearms
-2.824 -2.637 -2.500 0.832 -4.075
[1.640]* [1.118]** (1.090)** [0.778] [1.647]**
-0.413 -0.416 -0.135 -0.399 -0.409 -0.127 -0.393
[0.044]*** [0.045]*** [0.035]*** [0.046]*** [0.0420]*** [0.034]*** [0.042]***
-9.510 -5.690 1.020 -11.290
[4.190]** [2.880]** [1.940] [4.500]***
-7.330 8.360 7.930 1.590 8.560 -11.880 -3.660 -1.440 -3.120
[1.850]*** [1.990]*** [1.930]*** [1.450] [2.310]*** [4.530]*** [2.950] [2.050] [3.740]
R20.197 0.554 0.552 0.197 0.656 0.147 0.550 0.182 0.660
No of Cities 118 118 118 118 118 117 117 117 117
Observations 472 472 472 472 472 468 468 468 468
Source: Secretaria de Estado da Segurança Pública and Ministério da Saúde. Standard errors in parentheses robust to clustering at the city level in all columns . †: Dependent variable is homicides at time t minus
homicides in 2003, t = 2004, 2005, 2006 and 2007. * significant at 10%; ** significant at 5%; *** significant at 1%. All specifications include Δpopulation, Δpopulation ages 15 through 24. Bas eline suicides (by any
means) included in all specifications. Columns (1) through (4) include the number of suicides not by firearms per 100,000 inhabitants at the baseline. Only cities with more than 50,000 thousand included in the sample
unless otherwise specified. All specidications include year fixed effects. Baseline means averages for the years 2001 through 2003. a = weighted by population.
Baseline Suicides by Firearms
(per 100,000 inhabitants)
Baseline Homicides (per
100,000 inhabitants)
100*Suicides,Firearms/Suicides,
non Firearms
Constant

29
Table 3, Dependent Variable = ΔHomicides by Firearms per 100,000 inhabitants†
(1)
(2)a(3) (4)a(5) (6)a
-1.790 -2.843 -2.955 -4.012 -0.195 -0.196
[0.631]*** [0.948]*** [1.005]*** [1.161]*** [0.077]** [0.063]***
-0.211 -0.190 -9.100 -10.010 -0.325 -0.256
[0.037]*** [0.039]*** [0.097]*** [0.739]*** [0.077]*** [0.064]***
0.691 0.691
[0.062]*** [0.062]***
1.301 0.285 -113.108 -118.709 -5.098 -3.747
[1.262] [1.500] [23.455]*** [19.318]*** [1.651]*** [1.231]***
R20.744 0.796 0.513 0.645 0.255 0.390
No of Cities 118 118 105 105 102 102
Observations 354 354 420 420 401 401
Constant
Source: Secretaria de Estado da Segurança Pública and Ministério da Saúde. Standard errors in parentheses robust to clustering at the city level in all
columns . †: Dependent variable is Homicides at time t minus homicides in 2003, t = 2004, 2005, 2006 and 2007. * significant at 10%; ** significant at 5%; ***
significant at 1%. All specifications include ΔLog(population), ΔLog(population ages 15 through 24). Baseline suicides (by any means ) included in all
specifications. Number of suicides not by firearms per 100,000 inhabitants at the baseline included in all specifications. Only cities with more than 50,000
thousand included in the sample unless otherwise specified. In columns (3) through (6), all regressors are in logs. All specidications include year fixed effects.
Baseline means averages for the years 2001 through 2003. a = weighted by population.
Lagged Dependent Variable
Delta-in-Logs
Lagged Dependent Variable
Baseline Suicides by Firearms by
100,000 inhabitants
Baseline Homicides per 100,000
inhabitants
Log-in-Logs

30
Table 4, Dependent Variable = ΔProperty Crime per 100,000 inhabitants†
(1) (2)
(3)a(4)b(5)a,b (6) (7) (8)a(9)b(10)a,b
28.168 41.600 53.186 -6.155 4.900
[71.185] [66.798] [80.287] [6.056] [16.185]
-16.108 0.012 -0.167 -0.057 -0.076 0.002 -0.164 -0.047
[19.148] [0.044] [0.020]*** [0.032]* [0.054] [0.042] [0.022]*** [0.034]
60.839 96.057 176.610 -36.126 57.387
[170.099] [168.098] [192.082] [60.737] [96.063]
-396.945 131.292 5.398 227.060 136.385 -480.135 94.346 -69.298 203.410 107.966
[ 157.662]** [ 131.761] [ 119.217] [48.284]*** [83.896]* [152.323] [144.333] [124.697] [61.455] [90.239]
R20.070 0.090 0.162 0.120 0.112 0.066 0.088 0.133 0.133 0.114
No of Cities 118 118 118 645 645 117 117 117 432 432
Observations 472 472 472 2580 2580 468 468 468 1728 1728
Baseline Suicides by Firearms
(per 100,000 inhabitants)
Baseline Property (per 100,000
inhabitants)
100*Suicides,Firearms/Suicides,
non Firearms
Constant
Source: Secretaria de Estado da Segurança Pública and Ministério da Saúde. Standard errors in parentheses robust to clustering at the city level in all columns . †: Dependent variable is property crime at time t minus property
crime in 2003, t = 2004, 2005, 2006 and 2007. * significant at 10%; ** significant at 5%; *** significant at 1%. All specifications include Δpopulation, Δpopulation ages 15 through 24. Bas eline suicides (by any means ) included in
all specifications. Columns (1) through (4) include the number of suicides not by firearms per 100,000 inhabitants at the baseline. Only cities with more than 50,000 thousand included in the sample unless otherwise specified. All
specidications include year fixed effects. Baseline means averages for the years 2001 through 2003. a = weighted by population. b = all cities included.

31
Table 5, Dependent Variable = ΔCar Robbery Crime per 100,000 inhabitants†
(1) (2)
(3)a(4)b(5)a,b (6) (7) (8)a(9)b(10)a,b
5.943 9.977 20.150 0.325 3.172
[7.865] [8.122] [13.498] [0.353] [2.414]
-0.153 -0.182 -0.178 -0.167 -0.155 -0.183 -0.149 -0.168
[0.076]** [0.060]** [0.060]*** [0.060]*** [0.068]*** [0.056]*** [0.063]** [0.058]***
24.966 44.822 70.530 5.064 25.969
[31.179] [35.363] [49.541] [4.977] [22.550]
-37.935 -26.342 47.012 -3.341 36.266 -35.178 -0.753 29.428 -9.132 29.013
[21.394]* [22.415] [21.910] [2.845] [17.562]** [24.228] [11.854] [24.051] [4.186] [19.141]
R20.038 0.233 0.443 0.170 0.397 0.040 0.251 0.454 0.170 0.408
No of Cities 118 118 118 645 645 117 117 117 432 432
Observations 472 472 472 2580 2580 468 468 468 1728 1728
Baseline Suicides by Firearms
(per 100,000 inhabitants)
Baseline Car Robbery (per
100,000 inhabitants)
100*Suicides,Firearms/Suicides,
non Firearms
Constant
Source: Secretaria de Estado da Segurança Pública and Ministério da Saúde. Standard errors in parentheses robus t to clustering at the city level in all columns . †: Dependent variable is car robberies at time t minus car
robberies in 2003, t = 2004, 2005, 2006 and 2007.* significant at 10%; ** significant at 5%; *** significant at 1%. All specifications include Δpopulation, Δpopulation ages 15 through 24. Baseline suicides (by any means)
included in all specifications. Columns (1) through (4) include the number of suicides not by firearms per 100,000 inhabitants at the baseline. Only cities with more than 50,000 thousand included in the sample unless otherwise
specified. All specidications include year fixed effects. Baseline means averages for the years 2001 through 2003. a = weighted by population. b = all cities included.

32
Table 6, Dependent Variable = ΔSuicides per 100,000 inhabitants†
(1) (2) (3) (4)
(5)a(6) (7) (8) (9)
Suicides by
Firearms
Suicides by
Firearms
Suicides by
Firearms
Suicides by
non-firearms
Suicides by
Firearms
Suicides by
Firearms
Suicides by
Firearms
Suicides by
Firearms
Suicides by
non-Firearms
-1.274 -1.278 -0.804 -0.066 -1.133
[0.266]*** [0.274]*** [0.135]*** [0.494] [0.210]***
0.001 -0.002 -0.011 0.002 -0.002 -0.044 -0.005
[0.004] [0.003] [0.009] [0.004] [0.491] [0.032] [0.038]
-2.594 -1.462 -2.304 0.495
[0.639]*** [0.303]*** [0.471]*** [0.767]
0.372 0.340 0.259 1.480 0.216 1.086 0.557 0.670 -0.013
[0.010]** [0.264] [0.176] [0.617]** [0.237] [0.394]*** [0.186]*** [0.342]* [0.009]
Lagged dependent variable? No No Yes No No No Yes Yes No
R20.248 0.249 0.403 0.042 0.221 0.195 0.378 0.181 0.391
Number of Cities 118 118 118 118 118 117 117 117 117
Observations 472 472 354 472 708 468 351 468 351
Source: Secretaria de Estado da Segurança Pública. Standard errors in parentheses robus t to clustering at the city level in all columns . †: Dependent variable is suicides at time t minus suicides in 2003, t =
2004, 2005, 2006 and 2007.* significant at 10%; ** significant at 5%; *** significant at 1%. Δpopulation and Δpopulation ages 15 through 24 included in all speficiations. Only cities with more than 50,000
thousand included in the sample, unless otherwise noted. All specidications include year fixed effects. Baseline means averages for the years 2001 through 2003. a = weighted by population.
Constant
Baseline Suicides by Firearms
(per 100,000 inhabitants)
Baseline Homicides (per
100,000 inhabitants)
100*Suicides,Firearms/Suicides,
non Firearms

33
Table 7, IV Regressions, Dependent Variable: ΔHomicides by Firearms per 100,000 inhabitants†
(1)
(2)a(3)§(4) (5)a(6)§
2.155 4.013 -0.779 2.280 4.994 -0.377
[1.135]* [1.936]** [0.655] [1.400]* [2.512]** [0.765]
-4.477 -4.805 -0.242 -4.801 7.902 -0.779
[0.048] [4.387] [2.350] [3.458] [1.667]*** [2.350]
Number of Cities 118 118 118 117 117 117
Observations 472 472 472 468 468 468
ΔSuicides by Firearms per
100,000 inhabitants
Constant
Instrument = baseline suicides by firearms per 100,000
Source: Secretaria de Estado da Segurança Pública. †: Dependent variable is homicides at time t minus homicides in 2003, t = 2004, 2005, 2006 and 2007. The Instrument is the baseline suicide by
firearms in columns (1) through (3), and baseline suicides by firearms times a dummy for 2004 onwards in columns (4) through (6). Baseline means averages for the years 2001 through 2003. Standard
errors in parentheses robust to clustering at the city level in all columns . * significant at 10%; ** significant at 5%; *** significant at 1%. Controls are the same as the 1st stage and the reduced form
(including baseline homicides and baseline (all) suicides) except for the lagged dependent variable. Only cities with more than 50,000 thousand included in the sample, unless otherwise specified. All
specidications include year fixed effects. a = weighted by population. §: homicides not perpetrated by firearms.
Instrument = baseline ratio suicides by firearms/suicides not by firearms

34
(1)
(2)a(3) (4)a
-28.803 -42.030 -27.299 -77.100
[52.974] [70.347] [60.576] [ 89.081]
-145.481 -472.462 -158.210 -49.711
[182.630] [159.881]** [180.860] [122.979]
Number of Cities 118 118 117 117
Observations 472 472 468 468
Instrument = baseline suicides by
firearms per 100,000
Instrument = baseline ratio suicides by
firearms/suicides not by firearms
Table 8, IV Regressions, Dependent Variable: ΔProperty Crime by Firearms per
100,000 inhabitants†
ΔSuicides by Firearms per
100,000 inhabitants
Constant
Source: Secretaria de Estado da Segurança Pública. †: Dependent variable is property crime at time t minus property crime in
2003, t = 2004, 2005, 2006 and 2007. The instrument is the baseline suicide by firearms in columns (1) through (3), and baseline
suicides by firearms times a dummy for 2004 onwards in columns (4) through (6). Baseline means averages for the years 2001
through 2003. Standard errors in parentheses robust to clustering at the city level in all columns . * significant at 10%; **
significant at 5%; *** significant at 1%. Controls are the same as the 1st stage and the reduced form (including baseline
property crime and baseline (all) suicides) except for the lagged dependent variable. Only cities with more than 50,000 thousand
included in the sample, unless otherwise specified. All specidications include year fixed effects. a = weighted by population.

35
(1)
(2)a(3) (4)a
-7.504 -17.005 -9.872 -30.321
[ 6.133] [12.176] [10.687] [ 22.572]
15.383 50.685 -36.926 41.354
[10.011] [22.023]** [25.627] [20.761]
Number of Cities 118 118 117 117
Observations 472 472 468 468
Table 9, IV Regressions, Dependent Variable: ΔAuto Robbery by Firearms per
100,000 inhabitants†
Constant
Source: Secretaria de Estado da Segurança Pública. †: Dependent variable is auto robbery at time t minus auto robbery in 2003, t
= 2004, 2005, 2006 and 2007. The instrument is the baseline suicide by firearms in columns (1) through (3), and baseline suicides
by firearms times a dummy for 2004 onwards in columns (4) through (6). Baseline means averages for the years 2001 through
2003. Standard errors in parentheses robust to clustering at the city level in all columns . * significant at 10%; ** significant at
5%; *** significant at 1%. Controls are the same as the 1st stage and the reduced form (including baseline auto robbery crime
and baseline (all) suicides) except for the lagged dependent variable. Only cities with more than 50,000 thousand included in the
sample, unless otherwise specified. All specidications include year fixed effects. a = weighted by population.
Instrument = baseline suicides by
firearms per 100,000
Instrument = baseline ratio suicides by
firearms/suicides not by firearms
ΔSuicides by Firearms per
100,000 inhabitants

36
Table 10, Dependent Variable = ΔFirearms Prevalence†
(1) (2) (3)
(4)a(5) (6)
ΔApprehension
of Firearms
ΔApprehension
of Firearms
ΔApprehension
of Firearms
ΔApprehension
of Firearms
ΔApprehension
of Firearms
ΔSuicides by
Firearms
-0.632 -0.610 -0.608 -0.497 -0.0048
[0.180]*** [0.274]*** [0.173]*** [0.116]*** [0.0028]*
-15.584
[6.294]***
48.120 48.930 10.410 37.490 10.210 0.236
[15.470]*** [15.610]*** [17.470] [10.800]*** [7.980]*** [0.293]
Baseline Homicides Included? No Yes Yes Yes Yes Yes
ΔNumber of Policemen No No Yes No No No
R20.433 0.435 0.436 0.507 0.204 0.026
Number of Cities 118 118 118 118 118 118
Observations 472 472 472 472 472 472
Baseline Suicides by Firearms
(per 100,000 inhabitants)
Baseline Apprehension of
Firearms (per 100,000
inhabitants)
Constant
Source: Secretaria de Estado da Segurança Pública. Standard errors in parenthes es robust to clustering at the city level in all columns . †: Unless otherwise
noted, dependent variable is firearms apprehended at time t minus firearms apprehended in 2003, t = 2004, 2005, 2006 and 2007. * significant at 10%; **
significant at 5%; *** significant at 1%. Δpopulation and Δpopulation ages 15 through 24 included in all speficiations. Only cities with more than 50,000
thousand included in the sample, unless otherwise noted. All specidications include year fixed effects. Baseline means averages for the years 2001 through
2003. a = weighted by population.

37
Table 11, Dependent Variable = ΔHomicides by Firearms per 100,000 inhabitants†
(1) (2)
(3)a(4) (5)a
Reduced-form Reduced-form Reduced-form
Structural form
(IV)
Structural form
(IV)
-0.101 -0.031 -0.058
[0.029]*** [0.019]* [0.023]**
5.030 11.751
[3.670] [5.095]**
6.660 -3.000 -1.900 6.737 -1.748
[2.600]*** [3.250] [4.030] [0.936]*** [4.333]
Baseline Homicides Included? No Yes Yes Yes Yes
R20.233 0.549 0.656
No of Cities 118 118 118 118 118
Observations 472 472 472 472 472
ΔFirearms Apprehended per
100,000 inhabitants
Baseline Firearms Apprehended
(per 100,000 inhabitants)
Constant
Source: Secretaria de Estado da Segurança Pública and Ministério da Saúde. Standard errors in parentheses robust to clustering at the city
level in all columns . †: Dependent variable is homicides at time t minus homicides in 2003, t = 2004, 2005, 2006 and 2007. * significant at
10%; ** significant at 5%; *** significant at 1%. All specifications include Δpopulation, Δpopulation ages 15 through 24. Bas eline suicides
(by any means) included in all specifications. Columns (1) through (4) include the number of suicides not by firearms per 100,000
inhabitants at the baseline. Only cities with more than 50,000 thousand included in the sample unless otherwise specified. All
specidications include year fixed effects. Baseline means averages for the years 2001 through 2003. a = weighted by population.

38
Table 12, Dependent Variable = ΔProperty Crime by Firearms per 100,000 inhabitants
(1) (2)
(3)a(4) (5)a
Reduced-form Reduced-form Reduced-form
Structural form
(IV)
Structural form
(IV)
-1.951 -1.579 -1.138
[0.947]** [0.965] [1.001]
2.208 2.087
[1.430] [1.780]
106.207 -308.120 -498.410 -307.745 -504.704
[94.115] [167.909]* [158.698]*** [175.491]* [160.137]***
Baseline Property Crime Included? No Yes Yes Yes Yes
R20.096 0.101 0.158
No of Cities 118 118 118 118 118
Observations 472 472 472 472 472
Baseline Firearms Apprehended
(per 100,000 inhabitants)
ΔFirearms Apprehended per
100,000 inhabitants
Constant
Source: Secretaria de Estado da Segurança Pública and Ministério da Saúde. Standard errors in parentheses robust to clustering at the city
level in all columns . †: Dependent variable is property crime at time t minus property crime in 2003, t = 2004, 2005, 2006 and 2007. *
significant at 10%; ** significant at 5%; *** significant at 1%. All specifications include Δpopulation, Δpopulation ages 15 through 24.
Baseline suicides (by any means) included in all specifications. Columns (1) through (4) include the number of suicides not by firearms per
100,000 inhabitants at the baseline. Only cities with more than 50,000 thousand included in the sample unless otherwise specified. All
specidications include year fixed effects. Baseline means averages for the years 2001 through 2003. a = weighted by population.

39
Table 13, Dependent Variable = ΔCar Robbery by Firearms per 100,000 inhabitants
(1) (2)
(3)a(4) (5)a
Reduced-form Reduced-form Reduced-form
Structural form
(IV)
Structural form
(IV)
-0.237 -0.174 0.022
[0.099]** [0.104]* [0.180]
0.274 -0.002
[0.188] [0.337]
15.986 -22.566 40.307 -26.924 -60.561
[9.157]* [19.884] [21.008] [20.400] [26.901]**
Baseline Auto Robbery Included? No Yes Yes Yes Yes
R20.059 0.239 0.435
No of Cities 118 118 118 118 118
Observations 472 472 472 472 472
Constant
Source: Secretaria de Estado da Segurança Pública and Ministério da Saúde. Standard errors in parentheses robust to clustering at the city
level in all columns . †: Dependent variable is car robbery at time t minus car robbery in 2003, t = 2004, 2005, 2006 and 2007.* significant at
10%; ** significant at 5%; *** significant at 1%. All specifications include Δpopulation, Δpopulation ages 15 through 24. Baseline suicides
(by any means) included in all specifications. Columns (1) through (4) include the number of suicides not by firearms per 100,000
inhabitants at the baseline. Only cities with more than 50,000 thousand included in the sample unless otherwise specified. All
specidications include year fixed effects. Baseline means averages for the years 2001 through 2003. a = weighted by population.
Baseline Firearms Apprehended
(per 100,000 inhabitants)
ΔFirearms Apprehended per
100,000 inhabitants

Departamento de Economia PUC-Rio
Pontifícia Universidade Católica do Rio de Janeiro
Rua Marques de Sâo Vicente 225 - Rio de Janeiro 22453-900, RJ
Tel.(21) 31141078 Fax (21) 31141084
www.econ.puc-rio.br
flavia@econ.puc-rio.br