Impulse Purchases, Gun Ownership, and Homicides: Evidence from a Firearm Demand

Shock1

Christoph Koenig2

David Schindler3

Juli 23, 2021

Abstrakt: Do firearm purchase delay laws reduce aggregate homicide levels? Using

variation from a 6-month countrywide gun demand shock in 2012/2013, we show that

UNS. states with legislation preventing immediate handgun purchases experienced smaller

increases in handgun sales. Our findings indicate that this is likely driven by compar-

atively lower purchases among impulsive consumers. We then demonstrate that states

with purchase delays also witnessed comparatively 2% lower homicide rates during the

1This paper supersedes a previous version entitled “Dynamics in Gun Ownership

and Crime — Evidence from the Aftermath of Sandy Hook”. We thank participants

of numerous seminars and conferences for feedback. The paper benefited from helpful

comments by Bocar Ba, Sascha O. Becker, Aaron Chalfin, Amanda Chuan, Florian

Englmaier, Stephan Heblich, Alessandro Iaria, Judd Kessler, Martin Kocher, Botond

K˝oszegi, Florentin Kr¨amer, Katherine Milkman, Takeshi Murooka, Emily Owens, Arnaud

Philippe, Alex Rees-Jones, Marco Schwarz, Simeon Schudy, Peter Schwardmann, Hans H.

Sievertsen, Lisa Spantig, Uwe Sunde, Ben Vollaard, Fabian Waldinger, Mark Westcott,

Julia Wirtz, Daniel Wissmann, Noam Yuchtman and, insbesondere, Yanos Zylberberg.

The comments of Shachar Kariv and three referees substantially improved an earlier

Entwurf. David Schindler would like to thank the Department of Business Economics &

Public Policy at The Wharton School, where parts of this paper were written, for its

hospitality.

2University of Bristol & CAGE. Email: Christoph.Koenig@bristol.ac.uk

3Korrespondierender Autor, d.schindler@tilburguniversity.edu, Tilburg University

& CESifo Munich.

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0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology. Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz.

same period. Further evidence shows that lower handgun sales coincided primarily with

fewer impulsive assaults and points towards reduced acts of domestic violence.

JEL-Codes: K42, H76, H10, K14

Schlüsselwörter: Waffen, homicides, gun control

1 Einführung

The relationship between firearm ownership and criminal activity has been one of the

most polarizing topics in U.S. politics over the past decades. Supporters of gun rights

often claim that arming citizens will lead to decreases in crime, while supporters of gun

control point to the high numbers of victims of gun-related violence. Fowler et al. (2015)

report that 32,000 Americans are killed and another 67,000 injured by firearms every

Jahr. Based on their calculations, any policy measure effectively reducing these numbers

would thus have the potential for welfare gains of almost $50 billion each year. Curbing gun violence was also the intention behind many of the 130 gun control policy measures that have been enacted so far across U.S. Staaten (Siegel et al., 2017). One such group of policy measures, targeted explicitly at preventing impulsive acts of gun violence, are firearm purchase delay laws. These measures, by now in place in 15 UNS. Staaten, create a temporal distance between the decision to buy a gun and its eventual receipt. Delays can last from 2 days up to 6 months and occur through mandatory waiting periods or bureaucratic hurdles associated with obtaining purchasing permits. Both measures provide gun buyers with a “cooling-off period” during which those with short- lived suicidal or homicidal intentions may reconsider their planned actions (Cook, 1978; Andr´es and Hempstead, 2011). Since delay laws should also keep impulsive consumers without violent intentions from buying guns, they offer a unique avenue to investigate whether and how prevented firearm purchases by such individuals translate into reduced 2 l D o w n o a d e d von h t t p : / / Direkte . m i t . e du / r e s t / l a r t i c e – p d f / d o i / . / 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f by gu e s t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz. gun violence. Jedoch, such analysis would require a reasonably large shift in impulse purchases unrelated to local crime levels. In diesem Papier, we exploit one of the largest aggregate shocks to U.S. firearm demand to study the effects of handgun purchase delay laws. In a first step, we show that the existence of purchase delays led to a relative reduction in handgun sales during the six months after the 2012 Presidential election and the shooting at Sandy Hook Elementary School. Während dieser Zeit, fear of more restrictive gun control legislation and higher perceived need for self-defense capabilities led to record sales of firearms across the entire United States (Vox, 2016; CNBC, 2012). We use a difference in differences (DiD) Rahmen, comparing handgun sale background checks (BGCs) in states with handgun purchase delays to states without such delays during the six-month window of increased firearm demand. Our baseline results indicate that states with purchase delay laws witnessed a 7-8% relative decrease in handgun sales. Differences in gun popularity and other types of firearm legislation cannot explain these results. Nächste, we present evidence suggesting that lower purchasing levels were indeed more likely driven by impulsive buyers. We start by analyzing Google search data and show that delay laws did not lead to comparatively lower public interest in buying firearms during the demand shock. Handgun purchase delay laws thus did not seem to affect intentions to buy firearms, but only whether consumers’ interest translated into actual purchases. Using state variation in delay lengths, we also do not observe a relationship between our estimated effect size and delay length. For deliberate and exponentially discounting consumers, these should have been positively correlated since delays smoothly reduce the discounted net present value of owning a gun. This discontinuous impact of delay lengths on purchases lends further credibility to the presence of impulsive consumers. 3 l D o w n o a d e d von h t t p : / / Direkte . m i t . e du / r e s t / l a r t i c e – p d f / d o i / / . 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f by gu e s t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz. In the second part of our analysis, we investigate the effect of delay laws on homicides. Using the same DiD framework, we find that counties in states with purchasing delays experienced a relative 2% decrease in overall homicide rates during the demand spike, which is entirely driven by homicides involving handguns. Our baseline estimate implies that about 200 lives could have been saved in the six-month period alone if handgun purchase delays had been in place in all U.S. Staaten. An extensive set of robustness checks shows that our results are specific to the period of the demand hike and not driven by single states or the sample choice. Looking into the characteristics of the additional homicides in states without handgun purchase delays, we find evidence in line with the notion that gun ownership among impulsive buyers is associated with crimes of passion. 4 For female victims, the evidence points towards instances of domestic violence, as the majority of additional female homicides occurred inside the victim’s home and arose from an argument. The affected killings of males occurred mainly outside of their homes but were similarly strongly related to arguments. This study is related to three important streams of research. Erste, we add to the literature investigating the impact of firearm legislation, and in particular purchase delays, on crime rates. Previous studies found either decreases (Rudolph et al., 2015; Edwards et al., 2018; Luca, Malhotra, and Poliquin, 2017) or zero effects (Ludwig and Cook, 2000) on violent crime or homicides. As the adoption of firearm purchase delay laws may not be exogenous and law changes can be anticipated by prospective gun buyers, our paper substantially advances this literature by providing novel and credible identification through exploiting a sudden and unanticipated demand shock in conjunction with pre- 4All statements regarding a relative increase in handgun sales and homicides in states without handgun purchase delays are just the flip side of the relative decrease in handgun sales and homicides in states with such delays. 4 l D o w n o a d e d von h t t p : / / Direkte . m i t . e du / r e s t / l a r t i c e – p d f / d o i / / . 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f by gu e s t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz. existing delay laws.5 We also provide suggestive evidence that our empirical setup mainly picks up the behavior of impulsive consumers without violent intentions and offers insights into the types of homicides prevented through purchase delays. Zweite, we contribute to the extant literature in economics, criminology, and public health, studying the impact of firearm ownership on violent crime. The majority of studies find a positive relationship (sehen, z.B., Cook and Ludwig, 2006; Duggan, 2001; Müller, Azrael, and Hemenway, 2002; Müller, Hemenway, and Azrael, 2007; Siegel, Ross, and King, 2013). Some studies, Jedoch, also report no effect (Duggan, Hjalmarsson, and Jacob, 2011; Moody and Marvell, 2005; Kovandzic, Schaffer, and Kleck, 2013; Lang, 2016). A recent paper by Levine and McKnight (2017) shows with a different identification strategy that elevated gun exposure after the Sandy Hook shooting translated into higher rates of firearm-related accidents.6 We confirm the positive link between gun ownership and homicides found in previous studies but are the first to look specifically into firearm homicide characteristics and highlight the role of impulsiveness. Dritte, our evaluation of gun purchase delay laws contributes to the growing literature analyzing how policies can mitigate the consequences of behavioral biases (overviews are provided in Chetty, 2015; Bernheim and Taubinsky, 2018). To the best of our knowledge, we are the first to study impulsive behavior in the context of gun ownership. Few other studies at the intersection between behavioral economics and economics of crime have 5The identification strategy of overlaying cross-sectional variation in pre-existing characteristics with a common time-series shock has also been applied in other work (sehen, z.B., Nunn and Qian (2011). 6While gun-related accidents are not at the heart of our paper, supplementary results reported in the Appendix based on our own identification strategy cannot replicate those findings. Our main results suggest that the primary detrimental effect of increased gun ownership after the Sandy Hook shooting was an increase in gun-related homicides. 5 l D o w n o a d e d von h t t p : / / Direkte . m i t . e du / r e s t / l a r t i c e – p d f / d o i / . / 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f by gu e s t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz. also linked impulsiveness to criminal activity and acts of violence (Dahl and DellaVigna, 2009; Card and Dahl, 2011; Heller et al., 2017). We advance this literature by providing the first study to establish a link between firearm availability and the fatal consequences of impulsive behavior. 2 Hintergrund 2.1 Purchase Delay Laws in the United States The Second Amendment to the United States Constitution protects the fundamental right of citizens to keep and bear arms. Federal, state, and local governments, Jedoch, have enacted laws making it harder and more cumbersome for citizens to acquire firearms. On the federal level, two crucial pieces of legislation are the Gun Control Act of 1968 and the Brady Handgun Violence Prevention Act. The Gun Control Act requires all professional gun dealers to have a Federal Firearms License (FFL). Only they can engage in inter-state trade of handguns, are granted access to firearm wholesalers, and can receive firearms by mail. The Brady Act of November 1993 mandated BGCs for all gun purchases through FFL dealers and imposed a five-day waiting period to conduct these checks. Upon successful lobbying by the National Rifle Association (NRA), these waiting periods were set to expire when the FBI’s National Instant Criminal Background Check System (NICS) was introduced in 1998. Since then, the NICS handles all BGCs related to the sales of firearms. While there is comparatively little regulation on gun ownership at the federal level, there is substantial heterogeneity in restrictions imposed by U.S. Staaten. Constraints on private firearm ownership at the state level predominantly attempt to either prohibit potentially dangerous people such as convicted felons from acquiring guns or restrict the usefulness of firearms for unlawful purposes independent of the buyer. 6 l D o w n o a d e d von h t t p : / / Direkte . m i t . e du / r e s t / l a r t i c e – p d f / d o i / . / 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f by gu e s t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz. In this study, we focus on handguns since these, unlike long guns, have to be purchased in the state of residence, are a popular choice for self-defense, can be carried concealed, and are used in homicides substantially more often than long guns (Federal Bureau of Investigation, 2016). Our analyses utilize two types of delays between the decision to purchase and the moment the handgun is actually transferred. The first one is mandatory waiting periods. While the initial aim of waiting periods in the Brady Act was to give law enforcement agencies enough time to conduct BGCs, they also provide a “cooling-off” period and can thus help to prevent impulsive acts of violence (Cook, 1978; Andr´es and Hempstead, 2011). In der Praxis, buyers will perform a purchase (pass a NICS BGC and pay for the chosen gun) but can only receive their handgun after the waiting period has elapsed. The second measure is state requirements for licenses to lawfully possess or buy a handgun. Due to bureaucratic hurdles in the licensing process, these impose a de-facto waiting time. Prospective buyers have to request the permit at a local authority (z.B., a sheriff’s office), pass a NICS BGC, and pay the associated fee.7 Only after the permit has been processed and issued can they proceed with the purchase at their local dealer (usually without a renewed BGC). In order to accurately determine the presence of delay laws and minimize misclas- sification, we utilize several sources and apply a rigorous coding procedure outlined with all details in Appendix Section A.1. The final state classification is reported in Appendix Table 27, which shows that during the period of our study, from November 2009 bis Oktober 2013, 15 states and the District of Columbia had adopted some form of delay laws throughout. Nine states (Kalifornien, Florida, Hawaii, Illinois, Maryland, Minnesota, New Jersey, Rhode Island, Wisconsin) and the District of Columbia had 7Fees can range from $1 plus notary fee in Michigan to $340 in New York City ($100

in the state of New York). Siehe https://www.cga.ct.gov/2013/rpt/2013-R-0048.htm.

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imposed mandatory waiting periods on handgun purchases.8 Connecticut, Hawaii, Illinois,

Maryland, Massachusetts, New Jersey, New York, Nebraska, North Carolina, and Rhode

Island all require a purchasing permit during the period of our study. Michigan abolished

its handgun permit requirement in December 2012 and is thus the only state switching

its delay legislation during our study period. For the remainder of this paper, we will

refer to a state which implemented a mandatory waiting period, required a purchasing

permit, oder beides, as a Delay state.9 We refer to all other states as NoDelay states.

2.2 The Firearm Demand Shock of 2012/2013

Our analysis focuses on the firearm demand spike after the re-election of President Obama

in November 2012 and the Sandy Hook shooting in December 2012. We decided on these

two particular events to study the impact of delay laws on gun sales and homicides for

two main reasons: Zuerst, these events then marked the largest hike in handgun sales since

background data was collected in 1999. Such a strong shock is required in order to detect

any statistically significant effects on firearm purchases and homicides. Zweitens, nicht wie

the numerous later shootings that grabbed nationwide attention, our setup features a

pre-treatment period uncontaminated by other events, which is essential to accurately

account for the seasonal nature of the data. Im Folgenden, we briefly describe the two

events and the firearm demand hike of 2012/2013.

In the Presidential Election on 6 November 2012, President Barack Obama ran for

a second term against Republican candidate Mitt Romney. While Romney took a more

8Wisconsin repealed its 48-hour handgun waiting period in only 2015 and is thus part

of our sample.

9For purchasing permits, Tisch 27 states the maximum delay allowed by law. Dort

is no reliable information on average delays that we are aware of. As we binarize the

treatment, averaging would be inconsequential for our analysis.

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liberal position towards gun rights and was endorsed by the NRA, President Obama

favored stricter gun control laws. In October 2012, almost all polls showed the race as

within the margin of error, and President Obama’s victory came so unexpectedly for

Romney on election night that he had not even prepared a concession speech as internal

polls had shown him winning (International Business Times, 2012). Similar to President

Obama’s first election in 2008, gun sales increased after his re-election, but this time with

considerably larger magnitude (CNN, 2008; CNN Money, 2012; Depetris-Chauvin, 2015).

This was likely because the President had started to speak more openly about favoring

increased gun control measures in the wake of recent mass shootings, especially the one

at a movie theater in Aurora, Colorado, in July 2012.

About a month later, An 14 Dezember 2012, then 20-year-old Adam Lanza of Newtown,

Connecticut first shot and killed his mother at their home before driving to Sandy Hook

Elementary School. There he shot and killed six school employees and 20 students aged

six to seven years. Lanza committed suicide shortly after the first law enforcement officers

arrived at the scene. His motives are still not fully understood, but it has been suggested

that he had a history of mental illness (New Yorker, 2014). The massacre was the deadliest

ever U.S. school shooting and the third deadliest mass shooting in U.S. history at the

Zeit. This and the fact that most of the victims were defenseless children sparked a

renewed and unprecedented debate about gun control in the United States.

A few days after the shooting, President Barack Obama announced that he would

make gun control a central issue of his second term and quickly assembled a gun violence

task force led by then-Vice President Joe Biden to collect ideas on how to curb gun

violence and prevent future mass shootings. The task force presented their suggestions

to President Obama in January 2013, who announced to implement 23 executive actions.

These were aimed at expanding BGCs, addressing mental health issues and insurance

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0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz.

coverage of treatment, as well as enhancing safety measures for schools and law en-

forcement officers responding to active shooter situations. Zusätzlich, the task force

proposed twelve congressional actions, including renewing the Federal Assault Weapons

Ban, expanding criminal BGCs to private transactions, banning high-capacity magazines,

and increasing funds for law enforcement agencies.

The proposals were met by fierce opposition from the NRA and some Republican

legislators. At the end of January 2013, Senator Dianne Feinstein introduced a bill to

reinstate the Federal Assault Weapons Ban. While the bill passed the Senate Judiciary

Committee in March 2013, it eventually was struck down on 17 April 2013 by the Senate

40-60 with all but one Republican and some Democrats opposing the bill. A bipartisan

bill to be voted on that same day, introduced by Senators Joe Manchin and Pat Toomey,

aimed at introducing universal BGCs, also failed to find the necessary three-fifths majority

mit 54-46, leaving federal legislation eventually unaffected.

Even though no new federal regulations followed, gun sales soared further in the

months after the Sandy Hook shooting. Fear of stricter gun legislation and a higher

perceived need for self-protection drove up sales for both handguns and rifles (Vox,

2016). While gun sales had surged after every prior mass shooting during the Obama

administration, the surge after the shooting at Sandy Hook was unprecedented. Der

extreme demand shift even created supply problems for some dealers while others were

hoping for sales increases of a magnitude of up to 400% (CNBC, 2012; Huffington Post,

2013). Several executives in the gun industry have stated that they view mass shootings

as a boon to their business, attracting especially first-time gun owners (The Intercept,

2015). In line with these anecdotes, Figur 1 shows a clear spike in gun sales starting in

November/December 2012 after the Presidential election and the Sandy Hook shooting.

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While gun sales generally increase at the end of the year, this particular spike is far more

pronounced and prolonged than in the years immediately before and after.

FIGURE 1 ABOUT HERE

3 Data

3.1 Handgun Purchases

One of the main challenges in our analysis is the absence of a central database of gun

owners and firearm sales. To overcome this, researchers have often turned to proxy

variables from surveys, vital statistics, crime data, and gun magazine subscriptions.

While some of these indicators performed well in cross-sectional analyses, they have been

found unsuitable for tracking gun ownership over time (Kleck, 2004). Since Novem-

ber 1998, Federal law dictates that an electronic NICS BGC be carried out for every

firearm transaction through an FFL dealer. This publicly available data has the merit

of being comparable across time, providing high coverage at a monthly frequency, Und

distinguishes between different types of transactions and firearms. The main variable in

the first part of our analysis is NICS BGCs for handgun sales in a given state between

November 2010 und Oktober 2013, divided by the 2010 population in 100,000. In order to

interpret our results as semi-elasticities and reduce the influence of outliers while keeping

zero observations, we apply the inverse hyperbolic sine (IHS) transformation instead of

taking natural logarithms.10

As pointed out in recent studies, the NICS data also exhibits significant drawbacks

(Lang, 2013, 2016; Levine and McKnight, 2017). Erste, it can only measure flows of

10For convenience, we refer to the IHS transformation as log throughout the paper. Wir

provide robustness checks in levels for our main specifications in the Appendix.

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weapons but does not allow inferring the stock of firearms or ownership levels. Zweite,

flows might be substantially understated as about 22% of firearm sales are between private

parties and occur in states which do not require BGCs for private transactions (Müller,

Hepburn, and Azrael, 2017). Dritte, a BGC can occur for the purchase of multiple

weapons, as well as an exchange of an old for a new firearm. Vierte, the data does

not distinguish between approved and rejected BGCs, and even an approved check does

not guarantee the sale of a firearm. Endlich, some states require a BGC for a concealed

carry permit application but not for a handgun purchase itself. Other states are running

regular or irregular re-checks on existing permit holders and thereby inflate the counts or

produce outliers.

We believe that our setup mitigates some of these problems. To start with, Die

aforementioned anecdotes, as well as findings from California by Studdert et al. (2017),

indicate that many handgun purchases during the demand shock in late 2012 were made

by new gun owners. With few sales to pre-existing gun owners, this should strengthen the

correlation between handgun sale BGCs and changes in firearm ownership. Sales outside

the NICS through private transactions and particularly gun shows are a concern but

would only invalidate our results if they were more common in NoDelay states during

the sales hike. Since many consumers were first-time buyers, we deem it more likely

they were buying from a regular FFL dealer than privately.11 Multiple purchases are

unproblematic given our interest in the extensive margin of gun ownership. A boost in

exchanges of old for new guns in Delay states could also overstate increases in firearm

11In Appendix Section B.5, we show that neither the supply of nor the demand for gun

zeigt an (the latter measured by Google Search results) witnessed a more substantial impact

of the demand shock in NoDelay over Delay states, effectively showing that displacement

to these states does not seem to be a cause for concern.

12

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ownership in those states. Since the likelihood of such exchanges should be correlated

with pre-existing levels of gun ownership, we can control for this concern in additional

robustness checks. Außerdem, work by Mueller and Frandsen (2017) has shown that

only about 1.5% of BGCs across the U.S. are actually rejected, which severely limits the

impact of this potential source of error. There is also no strong indication that the demand

shock affected the rejection probability asymmetrically across Delay and NoDelay states.

Endlich, we add BGCs for permits to our measure of handgun sales to capture cases where

buyers obtain a permit to purchase a handgun.12

A closer investigation of the NICS data revealed several outliers and reporting issues.

Wir, daher, removed Hawaii, Illinois, Kentucky, Massachusetts, Pennsylvania, Und

Utah, as well as parts of the series for Iowa, Maryland, and Wisconsin from the sample.13

We also drop Connecticut and Michigan. Connecticut was host to the Sandy Hook

shooting and thus may have potentially experienced lower gun sales after the shooting

due to social pressure or psychological effects on residents. Michigan switched treatment

status during our period of observation from requiring a permit to not requiring a permit.

Performing the steps above yields our baseline sample consisting of 43 UNS. states for

12This procedure could not be applied for Hawaii, Illinois, and Massachusetts as permit

checks in these states may also include permits for long guns. Permits were also not added

to handgun sale checks for Florida where, for no apparent reason, almost all months

Bericht 0 permit checks (and single digits for non-zero months) until April 2013, Wann

they suddenly jump to 15,000-30,000 per month for the remainder of the sample period.

Any further reference to handgun BGCs implicitly includes BGCs made for permits unless

otherwise stated.

13Outliers are mainly due to permit re-checks and law changes associated with large

mechanic jumps in BGC activity. We provide explicit reasoning for these choices in

Appendix Section A.2.

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investigating the effect of delay laws on handgun sales (BL1 ). While we prefer this

restricted sample for our NICS analysis, robustness checks for our main results show that

alternative (and less restrictive) sample definitions generate qualitatively similar results.

3.2 Homicide and Mortality

For our primary outcome of interest, homicides, there are two main statistical sources in

Die Vereinigten Staaten: death certificates from the National Vital Statistics System (NVSS)

and police reports from the FBI’s Uniform Crime Reporting Program (UCR). Despite

the UCR data being widely used to study crime, they are known to suffer from reporting

issues that need to be taken into account by removing areas with unreliable data from

the sample (Targonski, 2011). Coverage is therefore not universal. The NVSS data, An

die andere Hand, contains all U.S. death certificates in a given year. We obtained the

data via the Center for Disease Control and Prevention (CDC) for the entire sample

period between November 2010 und Oktober 2013. The NVSS contains ICD-10 codes

for the underlying cause of each death, as well as the victim’s demographics, county

of residence, and injury circumstances, such as location and date. The ICD-10 codes

allow distinguishing not only between homicides, suicides, and fatal accidents but also

whether these were inflicted through a handgun or not.14 In order to increase the power

of our statistical analysis, we use the detailed geographical information in the NVSS

and collapse data at the county-month level. This provides us with a balanced panel

of homicide counts for 3,047 counties which we normalize by their 2010 population in

14Our measure of handgun-related incidents also encompasses instances when an

undetermined type of firearm was used. This should not bias our estimates in any way,

and it is corroborated by the fact that the vast majority of homicides are carried out with

handguns.

14

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100,000. This second baseline sample, denoted as BL2, covers every U.S. state apart

from Connecticut and Michigan for the same reasons as stated above, and we use it in all

analyses based on non-NICS data. Figur 2 shows the counties in our NVSS sample BL2

and highlights the states excluded in the NICS sample BL1. In robustness checks, Wir

show that applying more or less stringent sample restrictions yields very similar results.

FIGURE 2 ABOUT HERE

In order to cross-validate our results and delve deeper into homicide circumstances,

we also use the Supplementary Homicide Reports (SHR) series from the aforementioned

UCR data, bearing in mind the limitations of the data. These reports are compiled from

voluntary submissions by individual law enforcement agencies to the FBI and contain

detailed information such as demographics of victim and offender, the type of weapon

used as well as murder circumstances (z.B., argument or gang-related crime). We clean

the SHR data following the procedure described in Appendix A.4 and then collapse

observations into a balanced monthly panel for 2,091 counties. Counts are normalized

using the aggregate population in 100,000 covered by the reporting agencies within a

specific county in 2010. Both UCR and NVSS crime rates are converted into logs using

the same IHS transformation as for the NICS data.

3.3 Gun Interest and Controls

To assess whether consumers in states with and without handgun purchase delays have

similar preferences, one needs to separate initial intentions to buy handguns from actual

purchases. While we use NICS data to measure the latter, we rely on internet search data

from Google Trends to proxy for people’s intention to purchase firearms. We focus on

searches for the term “gun store,” which prior research has shown to be a good predictor

15

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of firearm purchasing intentions (Scott and Varian, 2014). Since the search data comes in

relative numbers, we adopt a technique similar to that used by Durante and Zhuravskaya

(2018) to construct a state-level panel of monthly Google searches for “gun store”.15

In addition to this, we use several control variables to account for potential con-

founders as well as differences in socio-economic characteristics across counties and states.

Our core set of covariates includes the log of population, the shares of the population

living in rural areas and below the poverty line, as well as the percentages of Black and

Hispanic inhabitants. All variables were obtained from the 2010 UNS. Decennial Census at

the county level (and aggregated for state-level analyses). Zusätzlich, we collected state-

level data on the percentage of households with internet access from the 2010 amerikanisch

Community Survey, which we include in regressions using Google search data. In selecting

these control variables, we broadly followed the choices made in prior studies which

have investigated the relationship between firearm prevalence and crime (z.B., Cook and

Ludwig, 2006; Duggan, 2001). Further variables used only for robustness checks, wie zum Beispiel

measures of gun popularity, are introduced and explained where appropriate.16

4 Empirical Strategy

4.1 Difference in Differences Approach

To estimate the effect of delay laws on handgun purchases and mortality during the

demand shock, we use a DiD regression model, which overlays the cross-sectional variation

in pre-existing purchase delay laws with time-series variation from the six-month surge in

15Further details on this procedure are reported in Appendix Section A.5.

16Summary statistics of all variables can be found in Appendix Table 30. Appendix

Tisch 31 performs mean difference tests on the primary outcome and control variables.

16

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firearm demand across the United States. To account for location-specific seasonality, alle

outcome variables are seasonally differenced by subtracting their 12-month lag (denoted

as ∆12). Seasonally differencing IHS-transformed variables approximate year-to-year

growth rates. Coefficients can thus be interpreted as either changes in (nominal) Wachstum

rates or proportional changes in the outcome variable. Similar transformations of crime

counts have, zum Beispiel, been applied in Draca, Machin, and Witt (2011). Our main

specifications thus read as follows:

∆12 log(HandgunSalesst) = α + b1(Delays × P ost1t) + B 2(Delays × P ost2t)

+ δtXs + λt + φs + ǫst

∆12 log(Homicidesct)

= α + b1(Delays × P ost1t) + B 2(Delays × P ost2t)

+ δtXc + λt + φc + ǫct

(1)

(2)

We use Equation 1 to estimate the effect of the demand surge on handgun sales in

Delay over NoDelay states. Gleichung 2 is effectively the county-level analog of Equation 1

but instead uses homicide rates as outcome variables. In these equations, the specific effect

of delay laws during the demand shock captured via Delays × P ost1t can be regarded as

a shifter for new gun owners. Delays is a dummy variable for states with delay laws as

described in Section 2.1 and summarized in Table 27, d.h., Kalifornien, Florida, Hawaii,

Illinois, Iowa, Maryland, Massachusetts, Minnesota, Nebraska, New Jersey, New York,

North Carolina, Rhode Island, Wisconsin, and the District of Columbia. P ost1t is a

dummy for time periods starting with President Obama’s re-election in November 2012

and ending after April 2013 when the proposals for a renewed assault weapons ban and

universal BGCs were defeated in the U.S. Senate. Our primary coefficient of interest

is β1 and captures the average proportionate difference in HandgunSales and Homicides

between Delay and NoDelay states during the demand shock. We also include a second

17

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interaction using the time dummy P ost2t for May 2013 bis Oktober 2013 to investigate

effects beyond the initial six months. This also allows testing whether Delay states

experience comparatively fewer handgun purchases over the entire time period or if this

is compensated by more sales later on.

Apart from time fixed-effects λt, the DiD regressions also allow for location-specific

linear trends φs and φc to account for the possibility that some areas may deviate from

general trends in BGCs and homicides. Außerdem, our regression models each also

feature a set of control variables X. We avoid concerns about “bad controls” by using

interactions of pre-determined, time-invariant factors and time fixed effects. The variables

included in this way are % Hispanic, % Black, % ländlich, the log of population, Und %

Armut. ǫ denotes the residual. The standard errors used for inference are clustered by

state as the level of treatment assignment to account for serial correlation in the error

Bedingungen. Regressions are weighted by the state/county population to reduce the impact of

less densely populated areas and to obtain U.S.-wide average effects.17

A potential alternative to our approach would be to estimate a gun owner-homicide

elasticity using Delays × P ost1t as an instrument. Our preference for the somewhat

cruder reduced-form relationship stems from two factors. The first is the limitations of

the NICS data discussed above. BGCs do not allow to draw direct inference on changes

in the existing population of gun owners, making an elasticity hardly comparable to other

Studien. This concern is compounded by issues of measurement error, as not all BGCs

lead to gun purchases, and not all purchases are reflected in the BGC counts. Our second

concern is that we do not expect the effect of gun owners on homicides to be overly large

since the vast majority of gun owners are law-abiding citizens (Fabio et al., 2016). To

17Each of these estimation decisions is reassessed in sections 5.1 Und 6.2, and we provide

supplementary results in the Appendix.

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precisely estimate such a small effect, one would need a fairly large sample at the county

level for which, Jedoch, no NICS data exists. We thus estimate the raw effect of handgun

purchase frictions on sales and homicide rates during the demand shock but do not pin

down a precise elasticity given the absence of reliable panel data on firearm ownership.

4.2 Validity of Identifying Assumptions

In order for our DiD design to yield causal effects, two assumptions need to be fulfilled.

Der Erste, commonly referred to as the parallel trends assumption, requires outcomes to

have evolved similarly in the absence of treatment. This may create valid concerns as

delay laws have not been exogenously assigned to states, and as such, any differential

reaction to the shock could just be an expression of differences in unobservables. Wir

take several measures to alleviate concerns that this assumption may be violated. Erste,

we show that our outcome measures were following similar trends in Delay and NoDelay

states prior to the demand shock to prevent that our estimates are simply picking up

pre-treatment divergence. As we can see from Panels A and B in Figure 3, handgun

sales and homicides in both groups of states are sharply diverging during the six-month

window of increased firearm demand. There is also a slight divergence for handgun sales

in preceding years which highlights the need for seasonal differencing.18 Second, Wir

report results with location-specific linear time trends for all our specifications as a first

robustness check. In order to credibly identify pre-existing trends, our baseline sample

length uses an asymmetric sample period 36 months before to 12 months after the 2012

18Appendix Figures 23/24 Und 25/26 depict the evolution of both variables in levels

and 12-month growth rates.

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election (November 2009 bis Oktober 2013) in the spirit of Wolfers (2006).19 Endlich, Wir

also perform an event-study analysis to investigate concerns about non-linear pre-trends.

FIGURE 3 ABOUT HERE

The second prerequisite is the absence of correlated shocks, d.h., other events coinciding

with the demand hike and being positively (negatively) correlated with the existence of

delay laws but negatively (positively) with BGCs and homicide rates. As argued above,

the outcome of the 2012 election, as well as the timing of the Sandy Hook shooting, Sind

unrelated to any relevant outcome variables and were arguably the most notable events at

that time. We tackle the remaining concerns in three ways: Erste, all regressions control

for socio-demographic factors known to be correlated with both gun ownership and crime.

Zweite, we corroborate the role of delay laws by running horserace regressions where we

add interactions of time dummies with potential confounders related to political leanings

as well as preferences for and supply of firearms. Endlich, in Section 5.3, we use Google

search data to show that the divergence in gun sales after the shock does not coincide

with a similar divergence in the interest to purchase a firearm.

5 The Effect of Delay Laws on Firearm Purchases

5.1 Ergebnisse

TABLE 1 ABOUT HERE

19Note that after applying seasonal differencing, the nominal sample period starts in

November 2010 and covers 24 months before and 12 months after treatment onset.

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In Table 1, we estimate the differential impact of the 6-month demand hike in Delay

states on our handgun sale measure as well as total and non-handgun sale BGCs per

capita. The main coefficient of interest is β1 from Equation 1, which represents the

percentage difference of the sales rate response to the demand shock in Delay states

compared to NoDelay states. Column 1 shows a significant negative effect in the first six

months after the Presidential election and a positive non-significant effect in the second

Zeitraum. This potential postponement effect, Jedoch, disappears when adding controls

in column 2, while the coefficient for the Post1 period remains marginally significant.

After adding state-specific linear time trends in column 3 and accounting for potential

pre-trends, the estimate for β1 gains precision while β2 decreases further. A very likely

explanation for this result would be that this specification reduces noise from diverging

trends in smaller states without significantly influencing the overall (weighted) coefficient.

Our preferred estimate is the more conservative specification in column 3.20 Der

results imply that sales rates were 7.3% lower in Delay states during the first six months

than in NoDelay states.21 Columns 4 Zu 7 show that delay laws did not significantly affect

overall BGCs or other gun-related transactions like long gun sales.

5.2 Robustness Checks

As highlighted in Section 4.2, our identification strategy hinges on the validity of the

parallel trends assumption and the absence of correlated shocks. Even though our results

20Both specifications are informative, Jedoch, in our view. As we do not know whether

the ‘true’ model exhibits trends, it is ex-ante unclear whether column 2 oder 3 sollte sein

bevorzugt. Wir, daher, report specifications with and without trends for all results in

order to provide a more complete picture.

21Note that for all results in logs (IHS), the interpretation of the coefficients is a change

in percentages. In levels, the coefficients represent percentage point changes.

21

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in Table 1 are robust to the inclusion of state-specific linear trends, one may argue that

this does not accurately capture non-linear pre-trends. We investigate this possibility

using an event-study design based on column 2 in Table 1, in which we allow for quarterly

treatment effects. The results are depicted in Panel A of Figure 4 and show no indication

of non-linear pre-trends.22

In the two years before November 2012, we do not observe

a clear pattern of up- or downward trends in our estimation. In the quarter following

Die 2012 Presidential election, Jedoch, the effect of Delay states on handgun sales turns

significantly negative. After that, the coefficients gradually move back to the pre-period

level and remain insignificant for the entire Post2 period. This also provides additional

evidence against the possibility that firearm purchases were merely postponed.

FIGURE 4 ABOUT HERE

In Appendix Section B.1, we demonstrate that no other factors related to the exis-

tence of delay laws systematically affected handgun sales during the demand shock and

provide a host of additional robustness and sensitivity checks. These additional analyses

suggest that the omission of Texas reduces the effect, as the state’s regression weights

are redistributed to a large number of states.

If each state suffers from measurement

error with some probability, spreading the weights will increase the overall impact of

mismeasurement. Außerdem, population weighting is necessary to correctly capture

countrywide effects as the effect arises predominantly in urban areas. Placebo regressions,

22Für diese Analyse, we aggregate the data into 3-month bins starting in November

since “classic” quarters would result in one fully and two partially treated time periods.

Appendix Figure 31 shows the same graph using monthly data. Appendix Figure 27

reports a similar event study graph without seasonal differencing extending over a longer

Zeitraum.

22

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different sample definitions, removing single states from the sample, results in levels

and/or without seasonal differencing, weighting by the adult population, controlling

for the economic environment, and using alternative clustering techniques confirm the

robustness of our findings.

5.3 Mechanismen

Having established different reactions in handgun sales between Delay and NoDelay states,

we proceed by evaluating whether our findings could be driven by impulsive consumers.

The first appraoch to characterize impulsive agents is the potential divergence between

plans and actions.

Mit anderen Worten, impulsive consumers may decide to buy a firearm

under the influence of transient emotions but eventually do not buy since these emotions

have already passed. This should not be observed for regular, non-impulsive consumers if

they make a perfectly rational purchase decision. Jedoch, a delay in receiving the gun

makes the purchase also less attractive for non-impulsive consumers since it reduces the

item’s net present value. Wenn, Jedoch, the decision not to buy is driven predominantly by

standard exponential discounting, we should observe that longer delays reduce purchases

substantially more than shorter delays. Impulsive agents, Jedoch, would be deterred by

any delay since they cannot get hold of the firearm while being in a particular emotional

state. The second key characteristic of impulsiveness would thus be that even very short

delays should have a notable impact on the likelihood to buy.23

TABLE 2 ABOUT HERE

23These predictions can also be formally derived in a theoretical framework which is

available on request but omitted here for the sake of space.

23

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We start by investigating the congruence between plans to buy firearms and actual

sales. This analysis uses Google searches for the term “gun store,” which serves as a proxy

for public interest in buying a gun and has been identified as a strong predictor for firearm

purchasing intentions in previous research by Scott and Varian (2014). Columns 1 Und 2

in Table 2 repeat our preferred regression specifications using Google searches for “gun

store” as the dependent variable. We do not detect large or significantly different changes

in search results, which provides evidence that the different evolution of gun sales in the

wake of the demand shock was not driven by different preferences for and intentions to

buy firearms.24 This is also additional evidence that our results are unlikely to be driven

by unobserved state heterogeneity. Wichtiger, these findings indicate a mismatch

between firearm purchase intentions and actual sales in Delay states. Jedoch, diese

results could also reflect that potential buyers do not know their state’s firearm laws

while searching for a gun store but only learn about delays at a later point and then

deliberately decide not to buy. For such non-impulsive consumers, we should observe

that decreasing delay lengths smoothly reduce the effect, which we test for next.

In columns 3 Zu 10 of Table 2, we use our two main specifications from Table 1 Und

gradually exclude states with delay lengths exceeding 30, 14, Und 3 Tage. The table also

features tests for coefficient equality of β1 in the short-delay and the baseline sample.

Gesamt, we do not detect strong variations in the estimated coefficients for β1. Im

most restrictive specifications 9 Und 10, with only four treatment states and at most

three days of delay, the estimates are still very close to the baseline in columns 3 Und

4. The Wald tests can never confidently reject the null hypothesis of coefficient equality

24Figur 28 in the Appendix shows the development of Google searches between

November 2009 und Oktober 2013 graphically. A regression using levels and producing

similar results can be found in Appendix Table 28.

24

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for β1. The absence of a systematic decrease in the effect size suggests that gun buyers

may, in fact, respond more to the presence of a delay per se rather than its length.25

This evidence lends further support to the above conjecture that the difference in sales

between the two groups of states is predominantly driven by impulsive consumers.

Ein anderer, competing explanation for the relative drop in handgun sales would be fear of

tighter gun legislation. Such legislation would be particularly binding in NoDelay states

which generally exhibit weaker gun legislation. The results in this and the previous section

offer some insights into why this may not be the case. Erste, the Google search results

in Table 2 favor impulsiveness as an explanation over rational, forward-looking behavior.

Zweite, since firearm ownership is a constitutional right and handgun ownership, In

besondere, cannot easily be prohibited by the states, any belief in substantially more

binding handgun ownership restrictions may be classified as distorted.26 Holding such

distorted beliefs makes further non-rational behavior conceivable. Dritte, the robustness

checks in Table 7 and Appendix Sections B.1 and B.2 show that gun law strictness (oder

its absence) by and large does not explain away the effect of delay laws.

6 The Effect of Delay Laws on Homicides

6.1 Ergebnisse

Having found that handgun sales increased significantly less in Delay states during the

2012 firearm demand shock, we investigate whether there was also a corresponding effect

25These findings are corroborated by a triple difference analysis presented in Appendix

Tisch 35. In Appendix Table 29, we also show that including transaction costs from, z.B.,

gun licensing fees in our regressions does not qualitatively change our findings regarding

the effect of purchase delay laws.

26This follows from the landmark ruling of D.C. v Heller, 554 UNS. 570 (2008).

25

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on homicide rates. Tisch 3 shows the results from Equation 2. Observations are now

at the county-month level, and the sample includes all states previously omitted due to

measurement error in the NICS data. Column 1 shows that Delay states saw a significant

relative drop in gun homicide rates by 2.4% after the start of the firearm demand shock

and an insignificant 1.4% relative decrease during Post2. Controlling for observables in

column 2 yields a significant 2.2% relative drop in Delay states’ handgun homicide rates

during the treatment period Post1 and an insignificant relative decline of 1.8% in Post2.

The inclusion of county trends in column 3 mainly leads to a loss in precision but only

slightly diminishes β1 to −0.019, which is still significant at 5%.27

FIGURE 3 ABOUT HERE

Columns 4 Und 5 show that the P ost1 effect for handgun homicides is also reflected in

decreased aggregate homicide rates of similar magnitude. This effect is significant at the

5% level without trends but loses significance when these are included. Vor allem, there is

virtually no impact of delay laws on overall homicides in the P ost2 period. The reason for

this becomes apparent when looking at specifications 6 Und 7, which show a significant

increase during P ost2 for non-handgun homicides. A straightforward explanation could

be that the reaction of NoDelay states reflects two different channels through which

increased handgun ownership can affect homicides. One would be a lethality effect by

which random acts of aggression or anger turn into the shooting and killing of another

person. The second effect would be a substitution effect whereby homicides are simply

carried out using handguns instead of other weapons with no aggregate effect. While the

27Our results thus imply an elasticity of homicide with respect to gun sales of between

0.23 Und 0.3. This compares to an elasticity of 0.2 reported in Duggan (2001) oder 0.1-0.3

in Cook and Ludwig (2006).

26

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former suggests an immediate, impulsive killing that would not have arisen without a gun,

the latter constitutes a less specific crime that would have taken place in any case. Unser

results are indicative of both effects, with lethality being more prevalent during Post1

and substitution dominating the Post2 period (possibly because homicides are generally

more prevalent in the months of the year also included in Post2 ). Since our main interest

is delay laws’ aggregate effects, the remainder of the paper focuses on the lethality effect

and the impact of delay laws on handgun-related homicides during the Post1 period.

Columns 8 Und 9 use the violent crime rate (following the FBI’s definition) as the

dependent variable to investigate whether the decrease in homicides may have been

counteracted by an increase in other types of violent crime and thus provide a test of the

“more guns, less crime” hypothesis. The estimated coefficients, Jedoch, are insignificant,

small in magnitude for the Post1 period and point in the same direction as the coefficient

for homicides. If anything, more handguns thus increased violent crime in our setting.28

6.2 Robustness Checks

We run similar checks as in Section 5.2 to establish the validity of our identification

strategy. Erste, we investigate the possibility of non-linear pre-trends using the same

event-study design as for the NICS data. Panel B of Figure 4 indeed does not show

any systematic effect for handgun-induced homicides before the onset of the treatment.29

28Appendix Section B.3 decomposes the overall violent crime rate and shows that

aggregation does not hide substantial effects on individual categories of violent crime.

Appendix Section B.4 shows the effect on suicides and accidents.

29Appendix Figure 32 reports a similar event study graph using monthly data.

Appendix Figure 29 reports a similar event study graph without seasonal differencing

extending over a more extended period.

27

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During our treatment period Post1, Jedoch, there is a clear negative impact for the first

quarter following the demand shock and a slightly smaller one for the second treatment

quarter, which lines up with the patterns observed for handgun sales rates in Panel

A of Figure 4.30

In Appendix Section B.2, we show that our findings on handgun

homicide rates are also not a by-product of underlying differences in political leanings,

law stringency, and preferences for and supply of firearms, and we discuss and report

placebo checks, state-level results, and sensitivity to alternative sample definitions, Daten

transformation, and weighting choices. As with the BGC results, population weighting

is necessary to correctly capture countrywide effects as the effect arises predominantly in

urban areas. Placebo regressions, different sample definitions, removing individual states

from the sample, results in levels and/or without seasonal differencing, weighting by the

adult population, controlling for the economic environment, applying other clustering

Techniken, and using state-level aggregates confirm the robustness of our findings.

6.3 Mechanismen

Abschnitt 5.3 provided tentative evidence that impulsive consumers are likely to drive the

differences in handgun sale BGCs between Delay and NoDelay states. In diesem Abschnitt,

we provide evidence that our results on homicides can also be traced back to impulsive

behavior. We do so by taking a closer look at the type of additional handgun homicides

in NoDelay states (or equivalently, which were “prevented” in Delay states).

30Appendix Figure 30 shows no systematic effect on non-handgun homicides before or

during our treatment. The positive effect during Post2 in the baseline regressions applies

to all three-month periods but is only statistically significant for May to July 2013.

28

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Panel A of Table 4 presents the results split up by victim sex with a particular focus

on the 20 Zu 29 age group, into which the majority of first-time buyers should fall.31 The

results show that men make up about 2/3 of the victims while women account for 1/3.

The coefficients for female victims, Jedoch, are more precisely estimated. Both male

and female victims are predominantly aged 20 Zu 29. These findings suggest that female

victims are overrepresented, as less than 10% of overall homicide victims are women in our

data.32 Given this and our evidence on impulsive consumers, we investigate the role of

domestic violence. To do so, we split the handgun homicide victims into those who were

shot in their homes and those who were assaulted elsewhere. Panel B of Table 4 Berichte

the corresponding results. For the male victims, we find that the entire effect is driven

by attacks outside their homes. Female victims, andererseits, are predominantly

assaulted in their place of living, consistent with instances of domestic violence.

To further investigate the role of domestic violence and impulsive killings more gener-

ally, we present results using the UCR SHR data on homicide circumstances in Panel C of

Tisch 4.33 Columns 1 Zu 2 show the baseline specification for handgun homicides reported

31Appendix Table 32 shows corresponding results for all other age groups. We also

report victim splits by race in Appendix Table 33 and show that, in line with the overall

demographics of homicide victims in the United States, victims tend to be almost evenly

categorized as ’White’ and ’Black.’

32To judge how common homicides of each category are, Panels A, B, and C of Table 4,

as well as Appendix Tables 32 Und 33, include an additional row reporting the mean of

the non-differenced dependent variable in levels.

33As outlined in Section 3.2, this data exhibits a more restricted coverage. Appendix

Tisch 34 shows that the UCR SHR data yield qualitatively similar estimates compared

to the NVSS data in our Post1 period of interest. A map illustrating the exact coverage

for the UCR data is shown in Appendix Figure 12.

29

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in the UCR SHR and then split these into specific murder circumstances. The results for

aggregate handgun homicides have the same sign as those using the NVSS data but are

only about 2/3 in size and insignificant, likely due to the more limited coverage and data

Qualität. The results in columns 3 Und 4, Jedoch, indicate that deadly assaults related

to arguments account for the main part of the additional handgun homicides in NoDelay

Staaten. Unlike the aggregate handgun murder rate, this effect is also highly significant.

All other types of homicide circumstances such as brawls, (organized) crime, and defense,

as well as other/undetermined, do not seem to be systematically affected during the Post1

Zeitraum. These findings lend further support to the hypothesis that impulsive consumers

are driving the differences in handgun homicides during the demand shock.

TABLE 4 ABOUT HERE

Summarizing these findings, we observe that the additional homicides of females in

NoDelay states primarily happened inside their home, predominantly to women between

20 Und 29, and often as a result of arguments. Homicides of men, stattdessen, passiert

primarily outside their home, but also primarily because of arguments. Similar to women,

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.

male victims are typically 20-29 Jahre alt. In terms of mechanisms, our findings suggest

domestic violence and other heat of the moment murders as a possible explanation

for the observed differences in homicides between Delay and NoDelay states. Diese

interpretations are in line with insights by Tangney, Baumeister, and Boone (2004) Das

F

B
j
G
u
e
S
T

T

Ö
N
0
8
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0
2
3

impulsiveness is correlated across domains.

7 Abschluss

In light of the persistently high rate of firearm homicides in the United States, verstehen-

ing the consequences of legislation limiting access to guns is imperative. One of the main

30

0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz.

arguments used by proponents of gun rights is that gun laws do not substantially affect

violent crime but impose excessive burdens on law-abiding gun owners. In this study, Wir

focus on the effects of a specific type of policy measure, handgun purchase delay laws,

and provide evidence that, while not infringing with Second Amendment rights, diese

laws can substantially reduce homicides by preventing impulsive purchases.

We present empirical evidence that states with delay laws in place saw comparatively

lower handgun sales during a demand shock after the re-election of President Obama

In 2012 and the shooting at Sandy Hook Elementary School. Further results show that

purchase delays have strong effects even when they are very short and did not affect

intentions to buy a firearm but only the likelihood of consumers making an actual handgun

purchase. In the second part of our analysis, we investigate delay laws’ effect on homicide

Tarife. Using detailed micro-data on mortality, we find a significant effect of delay laws

on handgun-related homicides during the period of the demand shock. The effect size is

um 2%, which in turn implies that about 200 homicides could have been “prevented”

during the six-month Post1 period if all U.S. states had had some sort of purchase delay

law in place. These additional homicides encompass both genders and indicate that

arguments, as well as domestic violence, constitute some of the main channels through

which handgun ownership by impulsive individuals may affect homicide rates.

We see our study as a good starting point for more nuanced investigations into the

relationship between gun ownership and crime. Erste, additional direct evidence on the

circumstances linking gun sales to violent crime is needed. While our results were able to

point in the direction of arguments and domestic violence, the results are far from clear-

cut. With increasing coverage of the FBI’s National Incident-Based Reporting System

(NIBRS ), more detailed information on particular crime incidents could be utilized to

study similar future firearm demand shocks. Zweite, given the absence of accurate data

31

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0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz.

on how county-level gun ownership evolves over time, our study cannot pin down an exact

gun-homicide elasticity. The NICS data is very noisy and makes cross-state comparison

impossible at times. We thus stress the need for a more transparent, county-level version

of handgun sales than what is currently available. Endlich, we believe that more research

is needed to evaluate the costs and benefits of specific gun laws. As shown in this study,

the positive effects of purchase delays may be understated. Rigorous analyses of gun laws

may therefore help foster a more informed debate on gun policy.

Verweise

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Total
Handgun sale
Non-handgun sale

S
k
C
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H
C
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N
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G
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A
B

F
Ö
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2,000,000

1,500,000

1,000,000

500,000

0

Jan 2007
Jan 2007
Jan 2007

Jul
Jul
Jul

Jan 2008
Jan 2008
Jan 2008

Jul
Jul
Jul

Jan 2009
Jan 2009
Jan 2009

Jul
Jul
Jul

Jan 2010
Jan 2010
Jan 2010

Jul
Jul
Jul

Jan 2011
Jan 2011
Jan 2011

Jul
Jul
Jul

Jan 2012
Jan 2012
Jan 2012

Jul
Jul
Jul

Jan 2013
Jan 2013
Jan 2013

Jul
Jul
Jul

Jan 2014
Jan 2014
Jan 2014

Jul
Jul
Jul

Jan 2015
Jan 2015
Jan 2015

Jul
Jul
Jul

Figur 1: NICS BGCs

l

D
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w
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.

Notes: Monthly federal NICS BGCs between November 2007 und Oktober 2015 In
absolute numbers. The sample encompasses data for all states consistently included
in our main specification as per Section 3.1. The light gray area is our sample window;
the dark grey area depicts the six months after the 2012 election and the shooting at
Sandy Hook. The gray line shows BGCs for handguns, the dashed black line all other
firearm-related BGCs, and the solid black line displays the sum of the two.

F

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38

0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz.

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.

Delay states
NoDelay states
Not in NICS sample (BL1)
Not in NVSS sample (BL2)

Figur 2: States and counties represented in the NICS and NVSS samples

Notes: Map of the United States showing the states contained in the NICS BGC data and
counties contained in the NVSS homicide data. Dark gray counties are located in NoDelay
Staaten. Light gray counties are located in Delay states. Shaded states are dropped from
the NICS sample. Near-black counties are not included in the NVSS sample.

F

B
j
G
u
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S
T

T

Ö
N
0
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S
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2
3

39

0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz.

Delay states

NoDelay states

D ec 2009
D ec 2009

Feb 2010
Feb 2010

A pr 2010
A pr 2010

Jun 2010
Jun 2010

A ug 2010
A ug 2010

Oct 2010
Oct 2010

D ec 2010
D ec 2010

Feb 2011
Feb 2011

A pr 2011
A pr 2011

Jun 2011
Jun 2011

A ug 2011
A ug 2011

Oct 2011
Oct 2011

D ec 2011
D ec 2011

Feb 2012
Feb 2012

A pr 2012
A pr 2012

Jun 2012
Jun 2012

A ug 2012
A ug 2012

Oct 2012
Oct 2012

D ec 2012
D ec 2012

Feb 2013
Feb 2013

A pr 2013
A pr 2013

Jun 2013
Jun 2013

A ug 2013
A ug 2013

Oct 2013
Oct 2013

(A) Log BGC rate for handguns

Delay states

NoDelay states

l

D
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w
N
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A
D
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D

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:
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(B) Log homicide rate

Figur 3: Evolution of outcome variables in Delay vs NoDelay states

Notes: Log of monthly NICS handgun BGCs per 100,000 inhabitants (panel A), Log
of monthly homicides per 100,000 inhabitants (panel B) in Delay states and NoDelay
states between November 2009 und Oktober 2013. The sample encompasses data from
all counties consistently included in our main specification. The dark grey-shaded area
includes the first six months after the 2012 election, d.h., November 2012 to April 2013.
Light grey-shaded areas are marking the same period for preceding years. For better
visibility, each series has been re-scaled to 0 on the last observation before the treatment.

40

0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) Lizenz.

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< :(: (cid:30)(cid:30) (cid:30)(cid:30)(cid:30) (cid:4)(cid:5)(cid:6) (cid:4)(cid:5) (cid:7) (cid:4)(cid:5)(cid:4) -(cid:4)(cid:5) (cid:7) -(cid:4)(cid:5)(cid:6) 0.050 (cid:30)(cid:31)(cid:30) ! " 0.000 (cid:29)(cid:30)(cid:31)(cid:30) ! " (cid:29)(cid:30)(cid:31)(cid:30)!(cid:30) (cid:29)(cid:30)(cid:31)(cid:30) ! (b) Handgun homicide rate Figure 4: Event study graphs Notes: Coefficients and 95% confidence intervals for the effect of being in a Delay state on ∆12 Log of NICS handgun BGCs per 100,000 inhabitants (panel A) or ∆12 Log handgun homicide per 100,000 inhabitants (panel B) for each three-month period between November 2010 and October 2013. The dark grey-shaded area includes the first six months after the 2012 election, i.e., November 2012 to April 2013. Light grey-shaded areas are marking the same period for preceding years. 41 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / d o i / . / 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f b y g u e s t t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) license. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / d o i / / . 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f b y g u e s t t o n 0 8 S e p e m b e r 2 0 2 3 Table 1: Handgun sale BGCs ∆12 Log of BGCs per 100,000 inhabitants Handgun Sale Total Other Delay×Post1 Delay×Post2 (3) (1) (2) (4) −0.112∗∗∗ −0.081∗ −0.073∗∗ −0.036 (0.028) (0.041) 0.048 0.057 (0.054) (0.062) (0.033) 0.005 (0.086) (0.045) 0.008 (0.066) (5) −0.028 (0.024) 0.053 (0.062) (6) 0.016 (0.053) 0.113 (0.097) (7) 0.026 (0.049) 0.127 (0.095) Year-Month FE Controls State Trends Y N N Y Y N Y Y Y Y Y N Y Y Y Y Y N Y Y Y States Observations R2 43 1,516 0.446 43 1,516 0.538 43 1,516 0.591 43 1,516 0.685 43 1,516 0.721 43 1,516 0.676 43 1,516 0.756 Notes: Observations are at the state-month level. The sample period is November 2010 until October 2013, i.e., an asymmetric 36-month window 2 years before and 1 year after the 2012 election. Standard errors clustered at the state level are in parentheses: ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01. Included control variables are log(population), % rural, % below poverty line, % Black and % Hispanic. All variables are as of 2010 and interacted with Month FE. Regressions are weighted by the state population. 42 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) license. Table 2: Online searches & Handgun BGCs (delay length) ∆12 Log of handgun BGCs per 100,000 inhabitants ∆12 Log std’zed share of Google searches for “gun store” Maximum delay length D Delay×Post1 4 3 Delay×Post2 Year-Month FE Controls State Trends States Observations R2 p(β1 = −0.073) Baseline (=12 delay states) D ≤ 30 Drop NY (=11) D ≤ 14 Drop MD, NC, NJ (=8) D ≤ 3 Drop CA, DC MN, RI (=4) (1) 0.043 (0.072) −0.029 (0.104) (2) −0.045 (0.080) −0.116 (0.138) (3) −0.081∗ (0.045) 0.008 (0.066) (4) −0.073∗∗ (0.033) 0.005 (0.086) (5) −0.074 (0.049) 0.012 (0.072) (6) −0.072∗∗ (0.035) 0.001 (0.094) (7) −0.105∗∗ (0.052) −0.001 (0.080) (8) −0.088∗∗ (0.041) −0.004 (0.116) (9) −0.071∗∗ (0.035) −0.131∗∗ (0.058) (10) −0.074∗ (0.038) −0.173 (0.119) Y Y N 49 1,764 0.276 Y Y Y 49 1,764 0.310 Y Y N 43 1,516 0.538 Y Y Y 43 1,516 0.591 Y Y N 42 1,480 0.547 Y Y Y 42 1,480 0.599 Y Y N 39 1,374 0.558 Y Y Y 39 1,374 0.603 Y Y N 35 1,230 0.612 Y Y Y 35 1,230 0.661 0.98 0.99 0.54 0.7 0.97 0.98 Notes: Specifications as per Table 1. Google search results include % with internet access as additional controls. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / d o i / . / 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f b y g u e s t t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) license. Table 3: Baseline: homicide rates ∆12 Log of ... per 100,000 inhabitants Homicides All violent crimes Any Other Delay×Post1 Delay×Post2 (1) −0.024∗∗∗ (0.009) −0.014 (0.012) Handgun (2) −0.022∗∗∗ (0.008) −0.018 (0.015) (3) −0.019∗∗ (0.010) −0.016 (0.018) (4) −0.024∗∗ (0.012) 0.003 (0.017) (5) −0.021 (0.015) 0.005 (0.022) (6) −0.001 (0.010) 0.023∗∗∗ (0.008) (7) −0.000 (0.013) 0.024∗∗ (0.011) (8) 0.004 (0.019) −0.018 (0.028) 4 4 Year-Month FE Controls County Trends Y N N Y Y N Y Y Y Y Y N Y Y Y Y Y N Y Y Y Y Y N (9) 0.002 (0.023) −0.019 (0.033) Y Y Y Counties Observations R2 3,047 109,692 0.002 3,047 109,692 0.008 3,047 109,692 0.019 3,047 109,692 0.006 3,047 109,692 0.016 3,047 109,692 0.005 3,047 109,692 0.014 2,091 75,276 0.007 2,091 75,276 0.034 Notes: Observations are at the county-month level. The sample period is November 2010 until October 2013, i.e., an asymmetric 36-month window 2 years before and 1 year after the 2012 election. Standard errors clustered at the state level are in parentheses: ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01. Included control variables are log(population), % rural, % below poverty line, % Black and % Hispanic. All variables are as of 2010 and interacted with Month FE. Regressions are weighted by the county population. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / d o i / / . 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f b y g u e s t t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) license. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / d o i / . / 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f b y g u e s t t o n 0 8 S e p e m b e r 2 0 2 3 45 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) license. Panel A: Victim sex Victim age Delay×Post1 Delay×Post2 Table 4: Effect on homicide rates: mechanisms Victim age ∆12 Log of handgun homicides per 100,000 inhabitants Any Any Male Female Any 20-29 Any 20-29 (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) −0.022∗∗∗−0.019∗∗−0.013 −0.011 −0.011∗−0.008 −0.008∗∗−0.008∗ −0.006∗∗∗−0.006∗∗ (0.008) (0.010) (0.008) (0.009) (0.006) (0.006) (0.003) (0.005) (0.002) (0.002) 0.002 −0.002 −0.002 −0.018 −0.016 −0.018 −0.016 (0.015) (0.018) (0.013) (0.015) (0.007) (0.008) (0.005) (0.007) (0.002) (0.003) 0.005 0.002 0.002 County Trends Mean DV levels R2 N 0.287 0.008 Y 0.287 0.019 N 0.243 0.008 Y 0.243 0.020 N 0.099 0.012 Y 0.099 0.023 N 0.045 0.005 Y 0.045 0.014 N 0.012 0.007 Y 0.012 0.016 Panel B: Victim sex Place of assault Any Any Place of Assault Male Female Home Not Home Home Not Home Delay×Post1 Delay×Post2 (5) (1) (4) (9) 0.004 −0.018∗−0.014 −0.007∗∗−0.008∗∗−0.001 (10) (3) (2) −0.022∗∗∗−0.019∗∗ 0.006 0.000 (0.008) (0.010) (0.008) (0.008) (0.009) (0.011) (0.003) (0.004) (0.002) (0.003) −0.018 −0.016 −0.012∗−0.014∗−0.008 −0.004 0.002 (0.015) (0.018) (0.006) (0.008) (0.011) (0.012) (0.005) (0.006) (0.002) (0.003) 0.001 0.000 0.001 (7) (6) (8) County Trends Mean DV levels R2 N 0.287 0.008 Y 0.287 0.019 N 0.083 0.006 Y 0.083 0.017 N 0.159 0.011 Y 0.159 0.022 N 0.027 0.004 Y 0.027 0.014 N 0.018 0.006 Y 0.018 0.016 Panel C: Circumstances ∆12 Log of handgun murders per 100,000 inhabitants Circumstances Any Arguments Brawls Gang, Felony, or Defense All Other Delay×Post1 Delay×Post2 (4) (2) (1) (10) (5) (3) −0.015 −0.018 −0.011∗∗∗−0.018∗∗∗0.002 0.003 (0.011) (0.013) (0.004) (0.006) (0.001) (0.001) (0.009) (0.010) (0.012) (0.010) −0.008 −0.011 −0.009∗−0.015∗−0.000 −0.000 −0.011 −0.019 0.023 (0.017) (0.022) (0.005) (0.008) (0.001) (0.001) (0.008) (0.014) (0.012) (0.016) (6) (9) 0.002 −0.001 −0.010 −0.007 0.013 (7) (8) County Trends Mean DV levels R2 N 0.253 0.011 Y 0.253 0.022 N 0.049 0.009 Y 0.049 0.021 N 0.003 0.013 Y 0.003 0.024 N 0.080 0.022 Y 0.080 0.043 N 0.121 0.010 Y 0.121 0.026 Notes: Panels A and B: All regressions use 109,692 observations from 3,047 counties. Panel C: All regressions use 75,276 observations from 2,091 counties. Specifications as per Table 3. 46 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / d o i / / . 1 0 1 1 6 2 / r e s t _ a _ 0 1 1 0 6 1 9 6 6 3 2 4 / r e s t _ a _ 0 1 1 0 6 p d . f b y g u e s t t o n 0 8 S e p e m b e r 2 0 2 3 0110621Review of Economics and Statistics Just Accepted MS.restby the President and Fellows of Harvard College and the Massachusetts Institute of Technology . Published under a Creative Commons Attribution 4.0 International (CC BY 4.0) license.

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