Essays In Health Economics & Economics of Crime

by

Kyutaro Matsuzawa

A dissertation accepted and approved in partial fulfillment of the

requirements for the degree of

Doctor of Philosophy

in Economics

Dissertation Committee:

Benjamin Hansen, Chair

Edward Rubin, Core Member

Kathleen Mullen, Core Member

Kristen Bell, Institutional Representative

University of Oregon

Spring 2025



DISSERTATION ABSTRACT

Kyutaro Matsuzawa

Doctor of Philosophy in Economics

Title: Essays in Health Economics & Economics of Crime

In Chapter 1, which is forthcoming at the Journal of Law & Economics, I exploit an ex-

ogenous ban of drunk driving (DUI) checkpoints, which were generally mandated via lengthy

Supreme Court cases, to explore whether DUI checkpoints, a salient and targeted enforce-

ment strategy, are effective in reducing drunk driving incidents. Using conventional and new

two-way fixed effects models, I find robust evidence that DUI checkpoint bans lead to an

approximately 12.4 percent increase in traffic fatalities involving drunk drivers. In addition, I

find that DUI checkpoint bans lead to both an increase in DUI arrests as well as self-reported

drunk driving behavior. These findings suggest that DUI checkpoints can create a general

deterrent effect in curbing drunk driving behavior.

In Chapter 2, I study a reform in the Los Angeles Police Department (LAPD) that aims

to reduce pretextual stops, which are types of traffic stops where the officer cites minor traffic

violations as a reason to stop and search a driver for contraband. Using regression disconti-

nuity design, I find that immediately following the adoption of this new policy, the number

of stops for minor traffic violations – defined as stops for equipment or non-moving violations

– reduced. Moreover, I find evidence that this policy may have helped reduce the number of

Black drivers getting stopped. On the other hand, I find little evidence of long-term adverse

effects in terms of public safety, as defined by traffic accidents and reported crime.

In Chapter 3, my coauthors (David Hall and Ben Hansen) and I replicate, reconcile, and

extend two early studies investigating the effect of Oregon and Washington’s drug decrim-

inalization law on drug overdoses but reach different conclusions. We document that the

conclusions of the two papers differ primarily due to the differences in the outcome investi-

gated and the pre-treatment window utilized. However, these differences do not matter in

the long run, as these results converge as we include further post-treatment data. Focusing

on the 3-year post-treatment window, we find robust and compelling evidence that drug

mortality increased following drug decriminalization.

This dissertation includes published material as well as unpublished coauthored material.

2



© 2025 Kyutaro Matsuzawa

All rights reserved.

3



CURRICULUM VITAE

NAME OF AUTHOR: Kyutaro Matsuzawa

GRADUATE AND UNDERGRADUATE SCHOOLS ATTENDED:

University of Oregon, Eugene

San Diego State University, San Diego

DEGREES AWARDED:

Doctor of Philosophy, Economics, 2025, University of Oregon

Master of Science, Economics, 2023, University of Oregon

Master of Art, Economics, 2019, San Diego State University

Bachelors of Art, Economics, 2017, San Diego State University

Bachelors of Science, Statistics, 2017, San Diego State University

AREAS OF SPECIAL INTEREST:

Applied Microeconomics, Public Policy, Labor Economics, Health Economics,
Economics of Crime

PROFESSIONAL EXPERIENCE:

Graduate Employee, University of Oregon, 2020-Present

Graduate Affiliate, Center for Health Economics & Policy Studies, 2019 - Present

Graduate Teaching Associate, San Diego State University, 2018-2019

Research Assistant, Institute for Behavioral And Community Health, 2017-2019

GRANTS, AWARDS, AND HONORS:

NAASE Graduate Student Paper Award - 2024

Russell Sage Foundation Dissertation Fellowship - 2024

Kleinsorge Summer Fellowship - 2022, 2024

University oforegon Department of Economics Best Field Paper Award - 2023

San Diego State University Terhune Economics Scholarship - 2017, 2018, 2019

San Diego State University Academic Excellence in Statistics - 2017

4



PUBLICATIONS:

Matsuzawa, Kyutaro. 2025. “The Deterrent Effect of Salient and Targeted Police
Enforcement: Evidence from DUI Checkpoint Bans”. Forthcoming. Journal of Law
& Economics

Matsuzawa, Kyutaro, Daniel I. Rees, Joseph Sabia, and Rebecca Margolit. 2025.
“Minimum Wages and Teenage Childbearing in the United States”. Journal of
Applied Econometrics

Dave, Dhaval, Andrew I. Friedson, Kyutaro Matsuzawa, Samuel Safford, and
Joseph J. Sabia. 2023. “Black Lives Matter Protests and Risk Avoidance The Case of
Civil Unrest During a Pandemic”. Journal of Human Resources

Dave, Dhaval, Andrew I. Friedson, Kyutaro Matsuzawa, Drew McNichols, Connor
Redpath, and Joseph J. Sabia. 2023. “Sudden Lockdown Repeals, Social Mobility,
and COVID-19: Evidence From a Judicial Natural Experiment”. Journal of
Empirical Legal Studies

Anderson, D. Mark, Kyutaro Matsuzawa, & Joseph Sabia. 2022. “Marriage
Equality Laws and Youth Mental Health”. Journal of Law & Economics 64(1), 29-51

Dave, Dhaval, Andrew I. Friedson, Kyutaro Matsuzawa, Samuel Safford, and
Joseph J. Sabia. 2022. “JUE Insight: Were Urban Cowboys Enough to Control
COVID-19? Local Shelter-in-Place Orders and Coronavirus Case Growth”. Journal
of Urban Economics 59(1), 29-52

Dave, Dhaval, Andrew I. Friedson, Kyutaro Matsuzawa, Drew McNichols, Connor
Redpath, and Joseph J. Sabia. 2021. “Risk Avoidance, Offsetting Community
Effects, and COVID-19: Evidence From an Indoor Political Rally.” Journal of Risk
and Uncertainty 63:133-167

Dave, Dhaval, Andrew I. Friedson, Kyutaro Matsuzawa, and Joseph J. Sabia.
2021. “When Do Shelter-in-Place Orders Fight COVID-19 Best? Policy
Heterogeneity Across States and Adoption Time”. Economic Inquiry 59(1), 29-52

Anderson, D. Mark, Kyutaro Matsuzawa, & Joseph Sabia. 2020. “Cigarette Taxes
and Teen Marijuana Use”. National Tax Journal 73(2), 475-510

5



ACKNOWLEDGEMENTS

I thank Professors Ben Hansen, Ed Rubin, Kathleen Mullen, and Kristen Bell for their

advice, mentorship, and unwavering support. I am incredibly grateful to Professor Hansen

for his encouragement, kindness, guidance, and support throughout my time as a graduate

student. Special thanks are also due to Professors Rubin, Mullen, and Bell, who provided

valuable inputs that helped improve my dissertation.

I owe many thanks to all my co-authors for providing helpful inspiration and motivation

for my research over the years. I am also thankful to my family, friends, and especially my

partner, who believed in me and supported me throughout my journey. Finally, I would like

to thank Jono, Paavo, and Tony for providing me with group therapy during times of stress.

This work has been partly supported by the Russell Sage Dissertation Fellowship.

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Table of Contents

1 The Deterrent Effect of Salient & Target Police Enforcement: Evidence
from DUI Checkpoint Bans 11
1.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11
1.2 Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 15

1.2.1 History of DUI Checkpoints in the United States . . . . . . . . . . . 15
1.2.2 Theoretical Effect of DUI Checkpoints and Ban . . . . . . . . . . . . 17

1.3 Methods . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 20
1.3.1 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 20
1.3.2 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . 23

1.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28
1.4.1 Traffic Fatalities . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28
1.4.2 DUI Arrests . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33
1.4.3 Self-Reported DUIs . . . . . . . . . . . . . . . . . . . . . . . . . . . . 36
1.4.4 Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 37

1.5 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 38
1.6 Table & Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40

1.6.1 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40
1.6.2 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 45

2 Pretextual Stop Restriction and Policing: Evidence from Los Angeles 50
2.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 50
2.2 Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 55

2.2.1 Background on Policies Surrounding Pretextual Stops . . . . . . . . . 55
2.2.2 Economic Framework . . . . . . . . . . . . . . . . . . . . . . . . . . . 57

2.3 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 62
2.3.1 Traffic Stop Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 62
2.3.2 Other Datasets . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 65

2.4 Methods . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 66
2.4.1 Short-run Estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . 66
2.4.2 Long-run Estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . 69

2.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 71
2.5.1 Immediate Impact of Pretextual Stop Restriction on Number of Stops 71
2.5.2 Immediate Impact of Pretextual Stop Restriction on Stop Outcomes . 76
2.5.3 Impact of Pretextual Stop Restriction on Reported Arrests & Traffic

Accidents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 79
2.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 82
2.7 Tables & Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 85

2.7.1 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 85
2.7.2 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 92

7



3 The Impact of Drug Decriminalization on Overdoses: Evidence from
Measure 110 98
3.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 98
3.2 Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 103

3.2.1 Oregon’s Measure 110 . . . . . . . . . . . . . . . . . . . . . . . . . . 103
3.2.2 Washington’s “Blake Fix” . . . . . . . . . . . . . . . . . . . . . . . . 106

3.3 Literature Review . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 107
3.3.1 Two Contradicting Early Evidence of Drug Decriminalization on Drug

Overdose . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 107
3.3.2 Longer-run Effect of Drug Decriminalization . . . . . . . . . . . . . . 111

3.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 113
3.4.1 Replication & Extension of Spencer (2023) and Joshi et al. (2023) . . 113
3.4.2 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117
3.4.3 Replication of Zoorob et al. (2024) . . . . . . . . . . . . . . . . . . . 119

3.5 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 122
3.6 Tables & Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 126

3.6.1 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 126
3.6.2 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 129

4 Appendices 134
4.1 Appendix for Chapter 1 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134

4.1.1 Chapter 1. Appendix Figures . . . . . . . . . . . . . . . . . . . . . . 134
4.1.2 Chapter 1. Appendix Tables . . . . . . . . . . . . . . . . . . . . . . . 145

4.2 Appendix for Chapter 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 151
4.2.1 Chapter 2. Appendix A. Proof . . . . . . . . . . . . . . . . . . . . . . 151
4.2.2 Chapter 2. Appendix B. Descriptive Figures & Tables . . . . . . . . . 155
4.2.3 Chapter 2. Appendix C. Supplemental Analysis . . . . . . . . . . . . 163

4.3 Appendix for Chapter 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 179
4.3.1 Chapter 3. Appendix Figures . . . . . . . . . . . . . . . . . . . . . . 179
4.3.2 Chapter 3. Appendix Tables . . . . . . . . . . . . . . . . . . . . . . . 185

References 189

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List of Figures

1.1 Trend in DUI Fatalities & Arrests . . . . . . . . . . . . . . . . . . . . . . . . 40
1.2 “First Stage” Effect of Changes in State Court Cases Arguing About DUI

Checkpoints . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 41
1.3 TWFE Event Study Analysis on Drunk Driving Fatalities; FARS 1980-2018 . 42
1.4 Robustness to the Use of New Difference-in-Differences Strategy; FARS 1980-

2018 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 43
1.5 Event Study Analysis on DUI Arrests, UCR 1980-2018 . . . . . . . . . . . . 44

2.1 RDiT Estimate: Police-Initiated Stops . . . . . . . . . . . . . . . . . . . . . 85
2.2 RDiT Estimate by Race . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 86
2.3 RDiT Estimate by Gender . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87
2.4 RDiT Estimate Stop Outcomes: All Stops . . . . . . . . . . . . . . . . . . . 88
2.5 RDiT Estimate: Arrests, Crime, & Traffic Accidents . . . . . . . . . . . . . . 89
2.6 SDiD Estimate: Crime Comparing Los Angeles to the Rest of U.S. . . . . . . 90
2.7 SDiD Estimate: Accidents . . . . . . . . . . . . . . . . . . . . . . . . . . . . 91

3.1 Differences in Overdose Definition Levels . . . . . . . . . . . . . . . . . . . . 126
3.2 Oregon vs. Synthetic Oregon in Drug Overdose Rate, Longer Time Window 127
3.3 Washington vs. Synthetic Washington in Drug Overdose Rate, Longer Time

Window . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128

9



List of Tables

1.1 Year of DUI Checkpoint Bans by State . . . . . . . . . . . . . . . . . . . . . 45
1.2 Estimated Effect of DUI Checkpoint Bans on Drunk Driving Fatalities, FARS

1980-2018 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 45
1.3 Estimated Effect of DUI Checkpoint Bans on DUI Fatalities: Using Subset of

Counties, FARS 1980-2018 . . . . . . . . . . . . . . . . . . . . . . . . . . . . 46
1.4 Estimated Effect of DUI Checkpoint Ban on Other Traffic Fatalities . . . . . 46
1.5 Estimated Effect of DUI Checkpoint Bans on DUI Arrests: UCR 1980-2018 . 47
1.6 Estimated Effect of DUI Checkpoint Bans on Self-Reported Drunk Driving,

BRFSS 1984-2018 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 48
1.7 Heterogeneous Treatment Effects by Whites vs. Blacks . . . . . . . . . . . . 49

2.1 RDiT: Number of Stops . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 92
2.2 RDiT: Number of People Stopped by Race . . . . . . . . . . . . . . . . . . . 92
2.3 RDiT: Number of People Stopped by Gender . . . . . . . . . . . . . . . . . . 93
2.4 RDiT: Traffic Stop Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . 94
2.5 RDiT: Arrest, Crime, & Accidents . . . . . . . . . . . . . . . . . . . . . . . . 95
2.6 SDiD: Reported Crime . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 96
2.7 SDiD: Reported Traffic Accidents . . . . . . . . . . . . . . . . . . . . . . . . 97

3.1 Measure 110 Law Adjustment 1 . . . . . . . . . . . . . . . . . . . . . . . . . 129
3.2 Difference in Replicated Weights . . . . . . . . . . . . . . . . . . . . . . . . . 130
3.3 Summary of Differences in Replicated Works . . . . . . . . . . . . . . . . . . 131
3.4 Replication: Synthetic Control Estimate for Oregon . . . . . . . . . . . . . . 131
3.5 Replication: Synthetic Control Estimate for Washington . . . . . . . . . . . 131
3.6 Extension: Synthetic Control Estimate for Oregon, Include Longer Post-

treatment Period . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132
3.7 Extension: Synthetic Control Estimate for Washington, Include Longer Post-

treatment Period . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132
3.8 Zoorob (2024) Replication & Extension . . . . . . . . . . . . . . . . . . . . . 133

10



The Deterrent Effect of Salient & Target Police

Enforcement: Evidence from DUI Checkpoint Bans

This chapter is based on a manuscript accepted for publication in the Journal of Law &
Economics in August 2024.

Abstract: I estimate the causal effect of drunk driving (DUI) checkpoints on traffic fatalities,
DUI arrests, and self-reported DUIs. Exploiting quasi-random variation in state-level laws
that ban DUI checkpoints, I find a 12.4% increase in DUI-related traffic fatalities within
the first five years following a DUI checkpoint ban. I also find a persistent increase in DUI
arrests and a short-run increase in self-reported DUI behavior. Together, these findings
suggest that targeted, salient police enforcement has a general deterrent effect on dangerous
driving. Furthermore, back-of-the-envelope calculations suggest that a federal ban on DUI
checkpoints would lead to an annual cost of approximately $6.4 billion in terms of lives lost
from DUIs.

1.1 Introduction

Driving under the influence of drugs and/or alcohol (DUI) is a major global public health

problem. In the United States, DUIs are responsible for an average of 32 deaths daily

and cost society approximately $44 billion annually (The Centers for Disease Control &

Prevention 2020), representing about a third of all traffic-related fatalities. DUIs serve as a

negative externality, affecting not only the offenders but also other drivers on the road and

their families. According to the National Highway Traffic Safety Administration’s Fatality

Analysis Reporting System (FARS), in 2019, 40% of DUI-related crashes involved multiple

vehicles, 32% of DUI-related fatalities were non-drunk drivers (for example, other drivers or

passengers), and 27.2% of DUI accidents led to the death of only the external party. Levitt

& Porter (2001) calculate that the externality costs associated with each DUI incident,

regardless of whether it results in an accident, can be as high as $14,000.1 Strikingly, while

111 million DUI incidents occur annually, less than 1% result in an arrest (The Centers for

Disease Control & Prevention 2020).

1Levitt & Porter (2001) initially report $8,000, which translates to $14,000 after being adjusted for
inflation.

11



Enforcement and sanctions are common approaches to deter criminal behaviors. Specific

approaches shown to be effective at reducing DUIs include a lower per se legal threshold for

DUIs (Dee 2001, Eisenberg 2003, Hansen 2015), administrative license revocation laws (Fell

& Scherer 2017, Freeman 2007), minimum legal drinking age laws (Carpenter & Dobkin 2009;

2011, Hansen & Waddell 2018, Voas et al. 2003), 24/7 complete sobriety laws (Midgette et

al. 2021), and zero-tolerance DUI laws (Carpenter 2004, Voas et al. 2003). Another common

targeted enforcement strategy is DUI checkpoints, where police officers screen drivers on

certain roads.2 These checkpoints not only apprehend violators but also visibly remind

drivers about DUI repercussions. While many states conduct DUI checkpoints on a weekly

basis, their impact and the consequence of prohibiting their use remain unclear.

In this paper, I measure the deterrent effect of DUI checkpoints. I employ a two-way

fixed effects (TWFE) difference-in-differences estimator by leveraging plausibly exogenous

spatial and temporal variation in state laws that banned the use of DUI checkpoints, which

were largely created by state supreme court decisions. I use three comprehensive national

datasets—FARS, Uniform Crime Report (UCR), and Behavioral Risk Factor Surveillance

System (BRFSS)—and examine three different DUI-related outcomes: fatalities, arrests,

and self-reported behavior. The use of these outcomes helps validate my results more clearly

and to examine the mechanisms through which checkpoints might influence DUI behaviors.

Using data from the 1980–2018 FARS, I find a robust 12.4% increase in fatalities involving

drunk drivers during the first several years after the ban was imposed. In the longer run,

I continue to find an increase of 10%–12%, but the estimates are sometimes imprecisely

estimated. Heterogeneity analyses reveal that these effects may be driven by larger states,

where the number of DUI checkpoints and police enforcement may be more common and

where the policy is expected to have a greater impact. A supplemental analysis examining

the impact on non-DUIs suggests that the increase in fatal DUI accidents may be offset

by a reduction in fatal speeding accidents. However, these estimates are very imprecisely

2DUI checkpoints are also known as DUI checkpoints, DWI (driving while intoxicated) checkpoints, or
sobriety checkpoints. In this paper, I refer to them as DUI checkpoints.

12



estimated.

I also find a persistent 12%–17% increase in DUI arrests using the UCR data. Addi-

tionally, using self-reported survey data from the BRFSS, I find evidence of an increase in

self-reported DUI behavior in the extensive margin and some evidence of an increase in the

intensive margin, an important channel that explains these net increases. Furthermore, back-

of-the-envelope calculations suggest that a federal ban on DUI checkpoints would generate

$6.4 billion annual costs from the lives lost from DUIs.3

This paper makes several contributions to the literature on DUI checkpoints. First, I

estimate their causal effect at the national level. While the existing literature documents an

association between the use of DUI checkpoints and reductions in DUI traffic accidents and

fatalities in the United States (Bergen et al. 2014, Elder et al. 2002, Evans et al. 1991, Fell

et al. 2004; 2005, Kenkel 1993, Lacey et al. 1999, Miller et al. 1998, Peek-Asa 1999, Sanem

et al. 2015), their estimates may be biased due to the potential endogenous placement of

individual programs in locations with higher DUI rates. Moreover, many of these studies

only focus on smaller areas, such as individual states or cities, which raises concerns about

external validity.4

Banerjee et al. (2019) use a randomized field experiment in Rajasthan, India and find

that locations with rotating DUI checkpoints (randomly assigned checkpoints) reduce traffic

accidents by 17% and deaths by 25%, relative to locations with no checkpoints. While they

find compelling evidence supporting DUI checkpoints, several questions remain unanswered,

which I address. First, what is the dynamic effects of conducting DUI checkpoints? Second, is

the reduction in traffic accidents occurring through increased deterrence or increased arrests?

Understanding the exact mechanism is important when policymakers are deciding on how to

efficiently allocate police resources. Third, Banerjee et al. (2019) investigate efficient ways to

use checkpoints but do not consider whether removing them and substituting away to other

3Further back-of-the-envelope calculations suggest that in states where DUI checkpoints are banned, an
estimated $1.8 billion is lost annually due to lives lost from DUIs.

4The magnitude of these studies range from 8% (Bergen et al. 2014) to 70% (Peek-Asa 1999) based on
the geography examined, suggesting heterogeneous local treatment effects.

13



patrol methods are also effective in deterring drunk driving or have spillover effects on other

non-drunk drivers.5

A working paper by Jones & Morin (2022) investigates the impact of state laws prohibit-

ing the use of DUI checkpoints on traffic fatalities. Using traffic fatality data from 1980

to 2000, they find that laws banning checkpoints lead to a 17% increase in total fatalities.

My research complements this paper while providing more robust findings. First, I use an

empirical specification that allows me to mitigate biases that may arise from heterogeneous

treatment effects due to bigger states experiencing a larger treatment effect than smaller

states (Chaisemartin & d’Haultfoeuille 2020, Goodman-Bacon 2021, Sun & Abraham 2021).

A concern with the methodology employed by Jones & Morin (2022) pertains to their use

of the overall level of traffic fatalities. Relying on raw counts rather than rates or logs will

result in larger heterogeneous treatment effects due to wide variations in population and

driving, potentially introducing bias into their estimates.6 Second, I use a more saturated

model that incorporates various controls for police enforcement, which may be theoretically

correlated with DUI behavior and changes in the use of DUI checkpoints.7 Third, I examine

various outcomes to further examine the mechanism in which DUI checkpoints affect DUIs.

Fourth, I extend the sample time window and analyze the short-, medium-, and long-run

effects of banning DUI checkpoints.8 Finally, I conduct various sensitivity tests to determine

if my estimates are artifacts of researcher choices in specification.

The rest of the paper proceeds as follows. Section 1.2 provides background on DUI

checkpoints and the theoretical mechanism. Section 1.3 discusses the data and econometric

methods. Section 1.4 presents the main estimates, and Section 1.5 concludes.

5A question that remains unanswered is whether the salience of DUI checkpoints or the presence of police
is the key to deterring drunk driving.

6Assuming that their effect entirely originates from DUI fatalities, their estimates would imply a sub-
stantial increase of approximately 50% increase in DUI fatalities, which would be extremely large if true.

7Jones & Morin (2022)’s control variables include unemployment rates, per capita income, and the pop-
ulation over 65.

8For instance, the effect of DUI checkpoints may be different from two decades ago due to the evolution
of technology, which makes communication about DUI checkpoints easier and more salient.

14



1.2 Background

1.2.1 History of DUI Checkpoints in the United States

DUI checkpoints, first introduced in the 1970s and growing in prevalence during the early

1980s (The Centers for Disease Control & Prevention 2015b), are a form of roadblock that

police officers use to detect and deter drunk drivers.9 At these checkpoints, officers block

a street and stop most, if not all, drivers to determine if they are sober. The procedure

generally involves the officer speaking with the driver, administering sobriety tests, and

conducting additional screening (such as a breath test) if they suspect the driver is under

the influence. The screening process at DUI checkpoints is relatively quick and lasts about

as long as a red light at an intersection (Mothers Against Drunk Driving 2022).

The main goal of DUI checkpoints is to deter people from driving under the influence

rather than to catch drunk drivers. Many checkpoints are salient, publicized, and highly

visible to increase a potential drunk driver’s perceived risk of getting caught. In many cases,

news outlets or police announcements will publicly report the number of arrests made at a

DUI checkpoint to remind the public about the consequences of driving under the influence.

Additionally, many police departments announce when and where they will conduct the

checkpoints (The Centers for Disease Control & Prevention 2015b, Mothers Against Drunk

Driving 2022).

The use of DUI checkpoints has sparked controversy, with opponents arguing that they

violate the Fourth Amendment because police officers search without probable cause.10 Ad-

ditionally, critics claim that the checkpoints can increase police discrimination, for several

reasons. First, police departments often disproportionately place the checkpoints in neigh-

borhoods with predominantly more racial minorities (Caputo 2015, Lacombe 2016, Romero

9Other types of roadblocks include traffic stops to check for a valid driver’s licenses and vehicle registration,
as well as to find undocumented immigrants.

10The Fourth Amendment states that “the right of the people to be secure in their persons, houses, papers,
and effects, against unreasonable searches and seizures, shall not be violated, and no Warrants shall issue,
but upon probable cause, supported by Oath or affirmation, and particularly describing the place to be
searched, and the persons or things to be seized.”

15



2016).11 Second, at a DUI checkpoint, police officers can easily observe the driver’s race.

This visibility raises concerns that implicit biases of the officers may the influence the de-

cision to conduct further screening of the driver (Goncalves & Mello 2021, Pierson et al.

2020).

In the 1990 U.S. Supreme Court case of Michigan Department of State Police v. Sitz, a

group of Michigan residents sued the state for conducting DUI checkpoints and violating their

individual rights. The Supreme Court concluded, with a ruling of 6-3, that DUI checkpoints

are constitutional and meet the standard of “reasonable search and seizure.” However, the

court also left it to each state to decide whether to allow them.

Between 1980 and 2018, 10 states prohibited the use of DUI checkpoints as illustrated by

Table 1.1, which shows these states and the year in when the bans were enacted.,12,13 States

have two methods to banning DUI checkpoints: legislative actions and court decisions. In

the legislative approach, a state legislature can ban checkpoints by passing new legislation

that is related to traffic stops or vehicle inspections but does not explicitly mention or target

DUI checkpoints.14 In these states, the ban on DUI checkpoints results from legislation

unrelated to DUI rates. Consequently, these policies create plausibly exogenous variation,

which I use to estimate the causal effect of DUI checkpoints and their prohibition on DUI

behavior.

In the second method, defendants arrested for a DUI argue that the evidence obtained at

the DUI checkpoint should not be used for legal prosecution. One of their legal defenses is

that the evidence was unlawfully obtained due to a search conducted without probable cause.

11For example, in Chicago, only 4% of checkpoints between 2010 and 2014 were placed in the city’s
majority-white police districts despite these neighborhoods accounting for around a quarter of the city’s
alcohol-related traffic accidents (Caputo 2015).

12Montana, although not included in the list, similarly bans DUI checkpoints. Unlike the other states,
Montana does not explicitly allow the use of DUI checkpoints but does allow “safety” spot checks instead.
These spot checks allow police officers to form roadblocks to check for a valid driver’s license or vehicle
registration and to screen for drunk drivers. For this paper, I treat Montana as a control state. However,
the estimates are robust to whether I treat it as a treatment state or exclude it.

13In 2000, Louisiana, which banned DUI checkpoints in 1989, permitted the use of DUI checkpoints. Thus,
there are currently 11 states that ban the use of DUI checkpoints.

14For example, in 1986, Iowa passed §321K.1, which provides information on when police officers can
conduct vehicle roadblocks. An interpretation of §321K.1 led the state to ban DUI checkpoints.

16



Another argument is that DUI checkpoints are illegal because the state never established an

administrative scheme for conducting them.15 Typically, in these cases the defendant loses

or the case gets dropped. However, in some rare instances, the defendant may decide to

appeal and bring the case to the Supreme Court or the Court of Appeals. This decision to

further argue against the constitutionality made by the defendant or their lawyer may create

a plausibly exogenous variation in the timing of when DUI checkpoints might be banned.

After long sequences of lower court trials, negotiations, and appeals, a state supreme court

judge may rule that the state has no right to conduct DUI checkpoints.16

The basis of these decisions come down to whether (i) DUI checkpoints lack statutory

constraints on the discretion of the police, (ii) they are intrusive based on the average length

of the interaction between the driver and the police officer, and (iii) the invasion of privacy

outweighs their social benefit. The third provision allows judge discretion based on their

assessment of the trade-offs between public safety and individual privacy. For my analysis,

this implies that my estimated effects may be a lower bound of the overall average treatment

effect. This inference is drawn from the premise that bans on DUI checkpoints are more

likely to occur in jurisdictions where judges feel that the safety impacts are smaller relative

to the privacy lost.

1.2.2 Theoretical Effect of DUI Checkpoints and Ban

In Becker (1968)’s model of criminal deterrence, fewer crimes will occur when the ex-

pected costs of committing a crime increase—through a higher probability of detection or

penalty from detection. The criminology literature classifies deterrent effects as either gen-

eral deterrence (committing fewer crimes due to future punishments) or specific deterrence

(committing fewer crimes due to previous punishments). Theoretically, DUI checkpoints can

create either form of deterrence. They can increase a drunk driver’s perceived risk of getting

15For example, in State of Oregon v. Boyanovsky in 1987, the defendant argued that the “roadblock was
unlawful because it took place without statutory authority or agency rules allowing and controlling such a
procedure.”

16On average, these court cases take approximately three to four years from the arrest to reach a conclusion.

17



caught, thereby reducing the likelihood of driving while drunk (general deterrence). They

may also dissuade drivers through peer effects when they see their peers getting arrested

for DUIs (Billings & Schnepel 2022, Chalfin & McCrary 2017, Leadbeater et al. 2008); dis-

suade drivers who were previously screened at a DUI checkpoint (Beck & Moser 2004; 2006);

and reinforce good behavior by reminding drivers about the potential consequences of DUIs

(specific deterrence).

The effect of a DUI checkpoint ban can be asymmetric depending on whether the check-

point acts as a general or specific deterrence. If checkpoints create a general deterrent effect,

then banning them will have similar effects (but opposite in sign) as conducting one. Drivers,

without the deterrence method, may perceive a lower risk of getting caught and begin driv-

ing drunk more frequently. In this scenario, DUI fatalities and arrests may increase when

DUI checkpoints are banned. Conversely, if DUI checkpoints create a specific deterrent ef-

fect, then conducting them can have a more persistent effect rather than a temporary one.

Therefore, even if DUI checkpoints are banned, the effect of the initial DUI checkpoints may

continue, and people may react less to the ban. Under this scenario, the short-run effect of

bans may be smaller and asymmetric to conducting one. Instead, the effect of bans on DUI

fatalities or arrests may be more dynamic and increase over time.

A change in police behavior and arrests due to DUI checkpoints is also an important

channel through which DUI fatalities can change. If DUI checkpoints are effective in arresting

drunk drivers, then banning them could lead to fewer DUI arrests, potentially resulting in

an increase in traffic fatalities. However, checkpoints may be an inefficient way of catching

drunk drivers and might not lead to increased DUI arrests (Greene 2003, Kenney 2018).

Their limited geographical coverage and the possibility of drivers avoiding them can reduce

effectiveness. Moreover, the testing methods used at DUI checkpoints may be inaccurate or

inefficient. Consequently, if DUI checkpoints do not significantly contribute to DUI arrests,

their absence might actually reduce fatalities if more effective enforcement strategies are

implemented instead.

18



Another consideration is the displacement effect. If checkpoints primarily result in the

arrest of low-risk drivers rather than high-risk ones, they might inadvertently increase traffic

fatalities. Under this scenario, banning DUI checkpoints could lead police to substitute away

to a more efficient method of arresting drunk drivers.17,18,19 An increase in the arrest of more

and higher-risk drunk drivers following a ban could then lead to a decrease in DUI fatalities.

Finally, changes in traffic and speeding as a result of DUI checkpoints can also affect

the rate of DUI fatalities. If checkpoints increase traffic and slow down driving speeds, this

change may not necessarily lead to fewer crashes involving drunk drivers. However, it may

reduce the severity of such incidents. For example, an accident may be more likely to result

in minor collisions, like fender-benders, than serious car accidents. If this mechanism is true,

banning DUI checkpoints could have an immediate effect on the day when they would have

typically been conducted.

In summary, theoretically, the effect of a DUI checkpoint on traffic fatalities involving

drunk drivers and DUI arrests is ambiguous. Similarly, the effect of banning DUI checkpoints

is also ambiguous and not necessarily symmetric to conducting or allowing one. Moreover,

the effects of these strategies and policies can be dynamic but in an unknown direction.

Therefore, this ambiguity motivates both my empirical approach and the variety of measures

related to DUIs that I outline in the next section.

17Another example of a targeted enforcement strategy is saturation patrol, where a large number of police
officers patrol a specific area for a set time to find impaired driving behaviors, such as swerving and speeding.
The main difference between a DUI checkpoint and a saturation patrol is that during a saturation patrol,
police officers will need probable cause and reasonable suspicion to pull over a driver to screen. Compared to
a DUI checkpoint, a saturation patrol may be more effective in arresting drunk drivers because it can cover
larger areas and catch riskier drunk drivers (Greene 2003). However, it is less salient than a DUI checkpoint.

18For example, Minnesota began Operation NightCAP (Concentrated Alcohol Patrol), a high-profile sat-
uration patrol program, four years after the state’s supreme court ruled that DUI checkpoints are unconsti-
tutional.

19Other enforcement strategies, such as saturation patrol, can also have spillover effects on non-drunk
drivers by detecting other violations like speeding.

19



1.3 Methods

1.3.1 Data

Data on yearly traffic fatalities come from FARS, which is a national census that provides

information on traffic accidents that result in at least one death. FARS, which became

operational in 1975, provides a wide variety of information, including the time of day when

the accident occurred, the driver’s blood alcohol content (BAC), whether the driver was

speeding, and demographic information of the people involved in the accident. Using these

data, I create a state-by-year panel of total fatalities for all 50 states plus Washington, D.C.

between 1980 and 2018. Since Louisiana reversed its ban in 2000, I exclude it from the panel

after 2000.20

My main outcome of interest is the rate of total fatalities involving at least one driver

with a reported positive BAC, a measure used in the previous literature examining DUI

fatalities (Adams et al. 2012, D. M. Anderson et al. 2013, M. L. Anderson & Davis 2023,

Eisenberg 2003, Sabia et al. 2019).21 I determine a positive BAC if the result of the BAC test

was at least zero or if the reporting officer suspected that alcohol was involved.22 In addition,

I collect information on total non-DUI traffic fatalities and non-DUI speeding fatalities.23

Panel (a) of Figure 1.1 plots the total number of DUI fatalities per 100,000 people, strat-

ified by whether a state ever banned DUI checkpoints. In the early 1980s, the DUI fatality

rate peaks and has a similar pattern of trends across both the treatment and control groups.

Around the late 1980s and 1990s, when most states began to prohibit DUI checkpoints, the

fatality rates for both groups begin drastically declining but also begin diverging, with states

that banned DUI checkpoints having higher DUI fatality rates. These results suggest that

20The estimates are robust to whether I exclude Louisiana entirely from the panel or keep it post-2000
and use it as a control group.

21When I experiment with the total number of fatal accidents, rather than the number of fatalities, I
continue to find similar patterns of results.

22The results are qualitatively similar when I use multiple imputed BAC to determine DUI accidents
(Adams et al. 2012).

23Because information on speeding is not available until 1982, my analysis for the latter outcome focuses
on the time period from 1982 to 2018.

20



DUI checkpoint bans may have increased the fatality rate involving drunk drivers.

The use of the alcohol measure in FARS may introduce bias due to measurement errors,

as the reporting of a driver’s intoxication status relies on the discretion of the reporting

officer. To address whether measurement error is a concern, I conduct two data checks.

First, I decompose each state’s trend of DUI traffic fatalities into seasonality and time-series

trends and identify anomalies in the time series based on the proportion of time series that

are not explained by the two components (Hyndman 2021). This exercise aims to detect

inconsistencies in the reported DUI fatality rate. The results show that only 0.4% (9 of

1,989) of the observations have an anomaly, defined as at least three times the interquartile

range. The anomalies are spread over time and over the region rather than concentrated

during a certain time window or around a certain geography. Furthermore, when I regress

the anomaly indicator (equal to one if an observation was an anomaly and zero otherwise)

on the treatment variable and state and time fixed effects, I obtain an F-stat of 0.136. This

analysis confirms that there is very little or no correlation between potential measurement

error and treatment status. These findings suggest that the use of reported DUI fatalities

as the outcome is not a severe problem.24

Second, I examine the robustness of the estimates to using other traffic fatality outcomes,

which could serve as proxies for DUIs. Specifically, I study weekend deaths and weekend or

holiday nighttime deaths, a time of the week when DUIs are most likely to occur.

To measure the number of DUI arrests, I use crime data from the 1980–2018 UCR,

obtained from Jacob Kaplan’s Concatenated Files (Kaplan 2021b). Similar to the FARS

data, I create a state-by-year panel for the rate of reported DUI arrests per 100,000 people.

It is worth noting that the number of arrests undercounts the total number of offenses because

not every crime results in an arrest. However, the use of arrests is appropriate because there

is a high correlation between arrest reports from the UCR and actual crimes when data are

available for both (Lochner & Moretti 2004).

24I find similar patterns of findings when I exclude the anomalies from the main regression estimate.

21



Although the UCR reports the number of arrests for more than 18,000 police agencies

across the United States, reporting is voluntary, which raises concerns about data quality.

For example, an agency that reported a crime at time t may not report any crime at time

t − 1. I address this reporting error in the data using several procedures. First, I restrict

the sample to agencies that report crimes at least one month of the year, helping me loosen

my assumption about missing versus zero crime.25 Second, when calculating the rate of DUI

arrests, I use the sum of the population covered by each agency rather than the state-level

population. Using an agency population will guard against any biases that may arise due

to agencies dropping out and changing the sample’s composition.26 However, one potential

concern when using an agency-level population is that multiple agencies can cover the same

geographic region, resulting in some agencies having zero populations (National Archive of

Criminal Justice Data). To address this issue, I create a share of the total number of agencies

with zero population and include it as a control variable in the regression analysis. Finally,

I test if the estimates are sensitive to outliers.

Panel (b) of Figure 1.1 plots the trend in the average DUI arrests per 100,000 people by

whether a state ever prohibited the use of DUI checkpoints. The trend of DUI arrests is nois-

ier relative to the trends in DUI fatalities, but it generally mirrors the trend of DUI fatalities.

DUI arrest rates drastically decline over time for both the treatment and control groups, but

the trend starts diverging around the 1990s. In panel (a), I continue to find slightly higher

DUI arrests for the treated group relative to the control group after many states banned

the DUI checkpoints. This difference in trends also provides descriptive evidence that DUI

arrests increase after the bans.

I also use data from the 1984–2018 BRFSS, a nationally representative health survey con-

ducted by the Centers for Disease Control and Prevention (CDC), to measure self-reported

DUI outcomes. This allows me to assess whether DUI checkpoints increase DUI behaviors,

25By excluding agencies that do not consistently report arrests, I can safely assume that “zero” reported
crime means that no arrests were made rather than missing reports.

26I find qualitatively similar results when running the estimates at the agency level, which further guards
against any changes in the sample’s composition.

22



an important channel through which DUI checkpoint bans can affect DUI fatalities and ar-

rests. However, the CDC did not extend the BRFSS coverage to all states until the 1990s,

which limits the number of policy changes in my sample window to eight, with only four

states having at least four years of pre-treatment data. Moreover, some survey years do not

provide DUI information, limiting my ability to identify each lead-and-lag coefficient using

the same set of treatment states in an event study analysis framework. For these reasons,

while the BRFSS estimates are an important part of my analysis, the results should be

interpreted with caution.

In the BRFSS, survey respondents are asked if they have consumed any alcoholic bev-

erages during the last 30 days. Those who reported drinking are also asked if they have

driven after they “perhaps had too much to drink.” Using the answers to these questions,

I construct a dummy variable equal to one if an individual reported driving while drunk at

least once in the past month and zero otherwise. I also create a similar dummy variable but

only focus on the sample of drinkers. Finally, I create a measure based on the log of the

number of times an individual drove drunk.

1.3.2 Empirical Strategy

I begin by estimating the following TWFE difference-in-differences model:

log(Yst) = β0 + β1Ban
0−5
st + β2Ban

6−10
st + β3Ban

11+
st + γXst + δs + τt + αs · t+ εst, (1.1)

where Yst represents the outcome variable, which is the rate of DUI fatalities or DUI arrests

per 100,000 people in a given state s at time (year) t. To address the skewness of the data

and remain consistent with previous literature, I log transform the outcome. Ban0−5
st is a

treatment indicator denoting 0 to 5 years after the DUI checkpoint was banned, Ban6−10
st is a

treatment indicator denoting 6 to 10 years, and Ban11+
st is a treatment indicator denoting 11

or more years. β1, β2, and β3 are the causal parameters of interest, where β1 represents the

23



short-run effect, β2 represents the medium-run effect, and β3 represents the long-run effect of

a DUI checkpoint ban. The vector Xst contains time-varying state-level controls, which are

indicators for whether a state had a BAC 0.08 law, administrative license suspension law,

zero-tolerance DUI law, minimum legal drinking age law, seat belt law, 65 mph and 70 mph

speed limit law, and graduated license requirement law; beer tax rate; vehicle miles traveled;

police employment; police expenditure; unemployment rate; and GDP per capita.27 These

control variables capture economic condition and policies that are shown to be associated

with DUI or traffic fatalities, and they are commonly used in the literature examining the

effect of public policy on traffic fatalities (D. M. Anderson & Rees 2015, D. M. Anderson et

al. 2024, Carpenter 2004, Carpenter & Dobkin 2009; 2011, Cohen & Einav 2003, DeAngelo

& Hansen 2014, Dee 1999; 2001, Eisenberg 2003, Fell & Scherer 2017, Freeman 2007, Hansen

2015, Hansen & Waddell 2018, Lovenheim & Steefel 2011, Voas et al. 2003). δs and τt are

state and time fixed effects, respectively.

I also include a state-specific linear time trend (αs · t) that is, again, used commonly in

the literature examining the effect of public policy on traffic fatalities. Including this control

aids in reducing omitted variable bias by controlling for unobserved state trends that unfold

linearly and are incidentally correlated with both the treatment and outcome. The estimates

are weighted by the state population, and standard errors are clustered at the state level

(Bertrand et al. 2004).28,29

For the BRFSS estimate, I estimate the following model, similar to Equation (1.1):

Yist = β0 + β1Ban
0−5
st + β2Ban

6−10
st + β3Ban

11+
st + γXst + ϕZist + δs + τt + α · t+ εist, (1.2)

where Yist represents the outcome variable on DUI behavior in the last 30 days. The difference

between Equation (1.1) and Equation (1.2) is that since the BRFSS provides individual-level

27Appendix Table 1.1 provides summary statistics and sources for each control variable.
28Population data come from the Surveillance, Epidemiology, and End Results Program (2022).
29When I experiment with inference based on wild-cluster bootstrapping (Cameron et al. 2008, Cameron

& Miller 2015), I continue to find similar significance levels as the inference based on clustered standard
errors.

24



survey data, my analysis is performed at the individual level (denoted by i) rather than

at the aggregated state level. Because the survey date is available, I include month-by-

year fixed effects rather than year fixed effects. Following Carpenter (2004), I also include

individual-level controls denoted by Zist: three indicators of education (high school degree,

some college, college or higher), an indicator for white non-Hispanic, an indicator for male,

and age. To obtain nationally representative health statistics, I weight the regression using

BRFSS-provided survey weights. For ease of interpretation and to remain consistent with

Carpenter (2004), Equation (1.2) is estimated using OLS and a linear probability model.

Additionally, because I only have eight treatment states that have data on both the pre-

and post-treatment period, I report standard errors that are clustered at the state level and

wild-cluster bootstrapped.

For Equation (1.1) and Equation (1.2) to be causal, I assume that the parallel trends

assumption holds. I observe that the majority of the checkpoint bans (8 out of 12) oc-

curred through states’ supreme court rulings, which concluded lengthy (and arbitrarily long)

sequences of lower court trials, negotiations, appeals, and decisions. Consequently, these

case-driven court rulings plausibly introduce a policy variation independent of trends in

DUIs and DUI checkpoints.30,31 To assess the validity of the parallel trends assumption, I

conduct an event study analysis in which I replace the treatment indicators in Equation (1.1)

with ζτst lead-and-lag treatment indicators:

log(Yst) = β0 +
−2∑

τ=−6

βPre
τ ζτst +

12∑
τ=0

βPost
τ ζτst + γXst + δs + τt + α · t+ εst, (1.3)

where ζτst is equal to one if a state had a DUI checkpoint ban τ years before or after. I use

βPre
τ to test whether the policy is endogenous to the outcomes under study or is correlated

30For example, in Oregon, the court case that led to the 1987 ban on DUI checkpoints originally began
in 1984 but did not reach the state supreme court until January 1987. The court made its final decision in
September 1987.

31Alaska, Iowa, Wisconsin, and Wyoming are the four states where DUI checkpoints are banned through
legislative order. When I exclude them and focus only on treatment that occurred via a judicial order, I still
observe similar patterns of results.

25



with differential trends in outcomes across the treated and non-treated states. I examine

βPost
τ to assess for any post-treatment changes.

A recent development in the literature on difference-in-differences emphasizes the bias

that could arise from staggered treatment and dynamic and heterogeneous treatment effects

(Goodman-Bacon 2021). I argue that because my panel consists of significantly more never-

adopters (39 states), the weights of the β estimates are likely to be significantly influenced

more by the clean comparison groups, which use never-adopters as a control group, rather

than by the bad comparison group that uses already or early adopters as controls. An

exercise showing Goodman-Bacon (2021) weights confirms this claim. I find that 91.7% of

the weights come from the comparison group of treated versus never treated. Furthermore,

I find that the weights assigned to the bad comparison group (late versus early adopters)

are relatively low, at only 7.7%. In addition to Goodman-Bacon (2021)’s decomposition, I

also test for the presence of negative weights, which could bias the β estimates, using the

methods introduced by Chaisemartin & d’Haultfoeuille (2020). The results show that only

14.1% (50 out of 353) of my ATTs receive a negative weight, summing to only a total of

5.9% negative weight.

Together, these exercises suggest that the staggered treatment and heterogeneous and

dynamic treatment effects are unlikely to substantially bias the estimates. Nonetheless, as

a robustness check, I also re-estimate the main TWFE estimate using the Callaway and

Sant’Anna estimator (Callaway & Sant’Anna 2021), the Sun and Abraham estimator (Sun

& Abraham 2021), and a stacked difference-in-differences (stacked DD) estimator (Cengiz et

al. 2019), which allow me to mitigate such biases. For the Callaway and Sant’Anna estimator,

I use not-yet-adopting states as the counterfactual, and for the other two estimators, I use

never-adopting states as the counterfactual.32

Another key assumption I make is that there is a first-stage effect on the number of DUI

checkpoints decreasing after the DUI checkpoint ban. This assumption may be violated,

32Because there are some treatment states that are next to each other (for example, Washington and
Oregon), not-yet-adopting states may be a better counterfactual than never-adopting states.

26



for example, if there are some areas that never conducted a DUI checkpoint, resulting in

no change in the number of DUI checkpoints. While this assumption cannot directly be

tested due to the unavailability of historical data on when and where DUI checkpoints were

conducted, I defend it in two ways.

First, I gather information on state supreme court cases using data from casetext.com, a

cloud-based legal research platform that provides organized case information about state and

federal supreme court cases. Using this source, I identify historic dates when DUI checkpoints

were conducted, following two steps. I first search for state supreme court cases involving the

keywords “DUI checkpoint,” “sobriety checkpoint,” or “DWI checkpoint.” Next, I conduct

a text analysis to determine if the court cases mention when the checkpoints in question

were conducted.33 This process results in 365 unique court cases where the exact date of

DUI checkpoints are known.

While these court cases do not encompass the entirety of checkpoints conducted, Ap-

pendix Figure 1.1 shows a strong correlation between the number of state supreme court

cases and the number of DUI checkpoints conducted between 2008 and 2018.34 This corre-

lation supports the assertion that this measure can serve as a proxy for the overall amount

of DUI checkpoints conducted. Using these court cases, I calculate the yearly number of

reported DUI checkpoints for each state. The descriptive trends shown in panel (a) of Fig-

ure 1.2 and the event study analysis shown in panel (b) provide descriptive evidence that

the number of DUI checkpoints was quite similar between the treatment and control states

in the pre-treatment period (for example, the 1980s) but indeed significantly decreased after

the ban.35,36

33In many cases, the court document will include a phrasing along the lines of “on this date, the defendant
was arrested at a DUI checkpoint.”

34The data on the number of reported DUI checkpoints come from DUIBlock.com. DUIBlock.com provide
information on when and where a DUI checkpoint was held between 2008 and 2018, encompassing over
33,000 DUI checkpoints. However, these data are only available starting in 2008, meaning I do not have any
states contributing to my identification.

35I also note that DUI checkpoints started being used in Louisiana after the ban’s reversal in 2000.
36In Appendix Figure 1.2, I show event study analysis where I examine the number of court cases involving

the keyword “Driving Under the Influence.” I find no evidence that the number of state supreme court cases
arguing about DUIs decreased after the prohibition of DUI checkpoints. This finding suggests that only DUI

27

https://casetext.com
http://www.duiblock.com/
http://www.duiblock.com/


Next, to further validate the first-stage assumption, I construct a pseudo-state-by-year

panel using only the counties where DUI checkpoints will most likely occur and another

pseudo-state-by-year panel using counties where they are unlikely to have a DUI check-

point.37 To identify counties likely to conduct a DUI checkpoint, I use the county’s popula-

tion characteristics. In Appendix Figure 1.3, I use data on local DUI checkpoints compiled

by DUIBlock.com and find a strong positive association between different population mea-

sures and the number of reported DUI checkpoints. I define a county as likely to conduct

a DUI checkpoint if (1) its population is greater than 45,000, (2) its weighted population

density is greater than 1,000, or (3) its urbanicity is greater than 60%.38 If my sub-state

analysis suggests that the treatment effect is driven by counties where it is ex ante expected

that the policy will more likely be binding due to a higher frequency of DUI checkpoints,

then this exercise will strengthen my confidence in the first-stage assumption.

1.4 Results

1.4.1 Traffic Fatalities

Table 1.2 shows the TWFE estimates of the effect of DUI checkpoint bans on traffic

fatalities involving drivers with a positive BAC level. The point estimate from column

(1) implies an 18.5% increase in deaths from DUIs within five years after DUI checkpoints

were banned.39 In the fully saturated model in column (2), where I include various control

variables, I continue to find similar patterns of results, though the estimated effect is slightly

smaller. The point estimate from column (2) suggests a significant short-run effect of a

12.4% increase in traffic fatalities involving drunk drivers due to a DUI checkpoint ban

court cases involving DUI checkpoints were affected by the policy.
37The estimates are qualitatively similar when I conduct the analysis at the county-by-year level instead.
38I choose these cutoffs because they are greater than the 90th percentile among counties without DUI

checkpoints and around the 50th percentile among counties with DUI checkpoints (Appendix Table 1.2).
However, the estimates are robust to using different cutoffs.

39exp(0.170)− 1 = 0.185.

28

http://www.duiblock.com/


and a medium-run (6 to 10 years after the policy ban) effect of a 12.2% increase in such

fatalities. However, the latter estimate is only significant at the weakest conventional level.

The estimates show that the positive effect continues in the long run (11 or more years after),

but the effect size decreases and the estimates become imprecise, making it difficult to draw

any definitive conclusions.

Using the estimates from DeAngelo & Hansen (2014), my estimated increase in traffic

fatalities is comparable to what would be expected from a 31%–36% decrease in the size of

the highway police force, suggesting that the magnitude of this estimated effect is plausible

and reasonable. Moreover, this 12.4% increase translates to approximately 474 additional

DUI fatalities among the treatment state.40 This count of 474 additional deaths is reason-

able given the sheer number of cars that drive through DUI checkpoints.41 Because the

estimated effects closely match those found in the previous literature examining the original

implementation of DUI checkpoints (Banerjee et al. 2019), I can conclude that the start and

end of these policies have symmetric effects.

In Appendix Figure 1.4, I further examine which control variables are causing the point

estimates to be smaller. First, I find that including the unemployment rate reduces the

estimated coefficients by about 16% (0.156 to 0.131). This reduction is not surprising given

that previous studies have shown that both police enforcement and mortality may change

during the recessionary period (Ruhm 1996, Makowsky & Stratmann 2014). I also find that

including other DUI enforcement strategies may be responsible for the change in the esti-

mated effect. States that are likely to ban DUI checkpoints may also be more likely to adopt

other DUI policies in lieu of not having checkpoints, which can reduce DUIs. For instance,

a state may be more likely to enforce stronger sanctions (for example, administrative license

40To calculate this number, I use the total number of DUI fatalities in the period immediately before the
ban (3,823), multiplied by 12.4%.

41While the exact number of cars that pass through a DUI checkpoint is not available, the numbers are
expected to exceed a million cars. For example, just in San Diego, California, over half a million cars were
screened between 2012 and 2018 (Payton et al. 2018). Moreover, assuming that approximately 500 cars
are screened per night, this translates to over 1.5 million cars being screened annually if we assume that
approximately 33,000 DUI checkpoints were conducted between 2008 and 2018 (DUIBlock.com).

29

http://www.duiblock.com/


suspension law) when it cannot deter DUIs using one of the common enforcement strategies.

In Appendix Figure 1.5, I experiment with using different spatial controls, models, and

other functional forms of the outcome variable, and document several findings. First, omit-

ting the state-specific linear time trend does not alter the results. Second, the estimates are

robust to including other spatial controls. Third, the results are robust to using (i) inverse

hyperbolic sine transformation, (ii) the rate of DUI fatalities per 100,000 people, (iii) the

share of total fatalities involving drunk drivers, (iv) the monthly rather than the yearly level,

and (v) estimating fatality counts using a Poisson model. However, the estimated effects

are slightly sensitive to using fatality levels, an outcome used by Jones & Morin (2022). My

findings suggest a slightly larger and more persistent effect size that evolves over time. I

argue that the functional form of the outcome used and the possible omitted variable biases,

as shown in Appendix Figure 1.4, are likely contributing to the smaller estimated effect

observed in comparison to Jones & Morin (2022).

Finally, in the last (very right) estimate in Appendix Figure 1.5, I find that the estimated

effects are smaller in magnitude, suggesting relatively large effects for states with larger

populations. To address this potential heterogeneity, in Appendix Table 1.3 I show estimated

effects categorized by “low-population states” and “high-population states,” as suggested by

Solon et al. (2015) and following Kelly et al. (2020).42,43 I find that the estimated effects

are larger and driven by high-population states. In Appendix Table 1.4, I note that police

enforcement—measured by police employment, police expenditures, and the number of DUI

checkpoints conducted—is higher in larger states. These differences are consistent with the

hypothesis that higher levels of enforcement can lead to reduced criminality and dangerous

driving (Chalfin et al. 2022, DeAngelo & Hansen 2014, Evans & Owens 2007, Mello 2019).

Figure 1.3 presents the results from the event study analysis, in which the treatment

indicators are replaced with lead-and-lag treatment indicators. In the pre-treatment period, I

42Low-population states are defined as states with a below-median 2018 population, and high-population
states are defined as states with an above-median 2018 population.

43Due to having only five treatment states in each group, I report standard errors calculated using wild-
cluster bootstrapping.

30



find an insignificant pre-trend centered around zero, suggesting that DUI fatality rates do not

differ across the treatment and control states before the implementation of a DUI checkpoint

ban.44 This result instills a degree of confidence that the timing of DUI checkpoints is

exogenous to the trends in DUI traffic fatalities. In the post-treatment period, consistent

with Table 1.2, I find a positive effect of 10%–12%, which persists for about eight years

and then becomes smaller. Additionally, the results are once again robust to excluding

(panel (a)) and including (panel (b)) state-specific linear time trends, indicating that the

preferred specification is not biased from the potential negative weights that can result from

state-specific linear time trends.

Figure 1.4 presents the event study figures from the stacked DD, the Sun and Abraham

estimators, and the Callaway and Sant’Anna estimators. Because control variables are criti-

cal in my model, I use the residuals obtained after regressing the outcome on all my preferred

set of controls as the left-hand side variable for the Callaway and Sant’Anna estimator. This

approach allows for the flexible inclusion of various sets of control variables.45 Across all

new difference-in-differences strategies, I find an insignificant pre-treatment trend, followed

by a short- to medium-run jump of around 10%–12%. Columns (3) and (4) of Table 1.2

present the overall estimated treatment effects from the Sun and Abraham and stacked DD

estimators, respectively. These results continue to show a significant, positive short- and

medium-run effect and an imprecisely estimated long-run effect. The exception is the Sun

and Abraham estimate, which shows a more precisely estimated effect of similar magnitude.

These results suggest that the results are robust to using new difference-in-differences estima-

tors, which guard against biases that could arise due to staggered rollout and heterogeneous

44When I test whether the lead coefficients sum to zero, I find a χ2 of 0.3054 and 0.4825 for panels (a)
and (b), respectively.

45In Appendix Figure 1.6, I simulate a data-generating process (1,000 times) to show that under omitted
variable bias, the Callaway and Sant’Anna estimate, when using residuals as the outcome, produces less
biased estimates compared to those obtained by simply using the raw outcome variable. In panel (a) of
Appendix Figure 1.7, I present the Callaway and Sant’Anna estimates that use the raw outcome instead of
residuals. Consistent with Appendix Figure 1.6, Table 1.2, and the event study figure using TWFE without
any controls (panel (b) of Appendix Figure 1.7), the estimated effect is greater, indicating the presence of
omitted variable biases. However, my preferred Callaway and Sant’Anna estimates alleviate some of the
omitted variable biases.

31



and dynamic treatment effects.

In Appendix Figure 1.8, I explore the sensitivity of the estimates to using alternative

definitions of traffic fatalities, which can be used as a proxy for DUIs or as a falsification

test for data quality. Specifically, I present Callaway and Sant’Anna estimates for weekend,

weekend nighttime, weekday, and work hour traffic fatalities.46 The first two categories

represent times when DUI fatalities are most likely to occur, while the latter two represent

times when they are less likely to occur. Panels (a) and (b) show an insignificant pre-

trend, followed by a persistent post-treatment increase in crashes during both weekends

and weekend or holiday nights. However, the post-treatment coefficients are sometimes

imprecisely estimated. The effect size suggests a 5%–11% increase in these fatalities, which

is reasonable considering that the estimated effect on traffic fatalities involving impaired

drivers is around 10%–12%. Panels (c) and (d) show no increase in traffic fatalities during

the time at which DUIs are less likely to occur, suggesting that the increase in DUI fatalities

is not attributed to an increase in traffic fatalities during non-peak DUI hours. Together,

the results of this exercise confirm that the results are not driven by potential estimation

error.

Table 1.3 explores the effect of a DUI checkpoint ban after excluding subsets of counties

based on the perceived treatment intensity. In columns (1) and (2), I construct a pseudo-

state-by-year panel using large and small population counties. I find that the estimated effect

is driven by counties with a larger population (14.7% increase in the short and medium run),

aligning with the observation that larger population counties have a higher rate of DUI

checkpoints. The findings from columns (3)–(6) are also consistent with the notion that

more urban and denser counties experience larger treatment effects. Together, these results

lend support to my assumption that the change in the use of DUI checkpoints is driving the

46The weekend is defined as any time from Friday evening at 6:00 pm to Monday morning at 5:59 am.
Weekend or holiday nights are defined as the hours from 6:00 pm to 5:59 am the following morning, applicable
to weekends, federal holidays, and the evenings before federal holidays. Weekdays are defined as the period
starting from 6:00 am on Monday to 5:59 pm on Friday, and work hours are defined as the period from 8:00
am and 5:59 pm from Monday to Friday, excluding any times that fall on federal holidays.

32



results.

To investigate whether DUI checkpoint bans have an offsetting effect on non-DUI fatalities

due to changes in police enforcement or traffic congestion, I estimate their effect on these

fatalities. Column (1) of Table 1.4 shows little evidence of total fatalities increasing following

the ban on DUI checkpoints. Column (3) indicates that this null effect on total fatalities may

be offset by a reduction in speeding-related fatalities; however, the estimates are too imprecise

to draw firm conclusions.47 This reduction in speeding-related fatalities aligns with the

hypothesis that police officers, substituting away from DUI checkpoints to other enforcement

strategies such as saturation patrols, which can deter speeding, may have spillover effects on

other drunk drivers (DeAngelo & Hansen 2014).48 Finally, column (4) shows no evidence

of non-DUI fatalities increasing during the nighttime on weekends, when DUI checkpoints

are most likely conducted. This suggests that the change in the flow of traffic or congestion

created by checkpoints may not be a predominant channel.

1.4.2 DUI Arrests

The FARS estimates provide robust evidence of a short-run impact and some evidence

of a medium-run effect of a DUI checkpoint ban on traffic fatalities involving drunk drivers.

Two possible channels exist through which this positive effect can occur. First, if DUI

checkpoints are an effective deterrent method, banning them can lead to increased DUIs.

Second, if they are effective in catching drunk drivers, banning them can also lead to fewer

DUI arrests, which can cause more drunk drivers being involved in a car accident rather than

getting caught. To explore these mechanisms, I next explore the impact of a DUI checkpoint

ban on DUI arrests.

47In Panel I of Appendix Table 1.5, I examine heterogeneous treatment effects by counties for non-DUI
speeding-related fatalities. The findings suggest a similar pattern of results: larger short-run treatment effects
for larger, more urban, and more densely populated counties. However, the estimates are still imprecisely
estimated.

48In a supplemental analysis where I regress log police employment capita as the outcome variable, I find
no evidence of a reduction in police employment following a DUI checkpoint ban, suggesting that the bans
may lead to different types of enforcement rather than to a reduction in police force sizes.

33



In Table 1.5, I observe a similar pattern to those found for traffic fatalities. Column (1)

shows the TWFE estimate without including any of the preferred controls, which suggests

a statistically and economically significant increase in reported DUI arrests in the short and

medium run after a DUI checkpoint ban. Column (2) shows that the estimated effect is robust

to including various control variables, with the preferred specification implying a 12%–17%

increase in the reported DUI arrests 10 years after a ban. Columns (3) and (4) report similar

results using the new difference-in-differences techniques, suggesting a 12%–20% persistent

increase in DUI arrests. The UCR estimates, coupled with the FARS estimates, imply that

DUI checkpoints can create a general deterrent effect and the prohibition of DUI checkpoints

induces more people to drive drunk.

In Figure 1.5, I present the event study analyses to assess the validity of the parallel

trends assumption. Panel (a) uses a standard TWFE estimate, and panels (b)–(d) use

alternative difference-in-differences estimators. Across the four panels, I consistently find no

evidence of a pre-treatment trend in DUI arrests and an increase of around 10%–20% in the

post-treatment period. The results suggest that the estimates can be interpreted as causal.

Appendix Figure 1.9 shows the robustness of the UCR estimates to various data-cleaning

strategies. In the first (very left) estimate, I replicate my main preferred estimates found in

column (2) of Table 1.5. In the next estimate, I calculate the crime rate using the state-level

population as the denominator. The point estimates remain largely unchanged, suggesting

that the main results are not driven by the use of agency population as the denominator. In

the next four estimates, I account for any state-agency-time-specific unobservables, such as

underreporting by agencies, that could bias the estimates.

To identify anomalies in the observations, I experiment with two methods. First, I fit

a time-series model for each jurisdiction and exclude any state-by-year observations with

significant spikes and drops.49 I decompose each jurisdiction’s trend into seasonality, trend,

and unobservable components and classify any observation as an outlier if its unobservable

49Due to larger noise at a finer level such as agency level, conducting this exercise at a finer level yields
fewer detection. However, the results are qualitatively similar.

34



exceeds three times the interquartile range. For the second experiment, I use a simple two

standard deviation rule to detect for outliers in the data. Any state-by-month-year observa-

tions that are classified as an outlier are either excluded from the analysis, replaced with just

the trend and seasonality components, or replaced with the mean. The findings from this

exercise reveal somewhat larger effect sizes, suggesting that agencies that underreport crimes

may be biasing the estimates downward. Nevertheless, these results provide confidence that

the positive effect I am finding is not an artifact of poor data quality and that the main

UCR effect is the lower bound.

Finally, in the last two estimates in Appendix Figure 1.9, I experiment with stricter

sample restrictions. First, I create the state-by-year panel using agencies that report crimes in

all 12 months to address any issues that may arise from inconsistent reporting. I then use only

primary agencies, defined as agencies with a population greater than zero.50 I continue to find

a positive and persistent effect of 12%–14%, though the estimates are imprecisely estimated

for the longer-run coefficients. In summary, these estimates strengthen my confidence that

measurement errors that may arise in the UCR are not positively biasing the positive effect

found in Table 1.5.

In the remaining UCR regressions, I continue to check for the robustness of the UCR

estimates using different specifications. In panel II of Appendix Table 1.5, I explore the effect

of a DUI checkpoint ban by removing a subset of counties based on the perceived intensity of

treatment. The findings in this table continue to show that the counties that are more likely

to conduct a DUI checkpoint observe a larger treatment effect. Appendix Figure 1.10 shows

the Callaway and Sant’Anna estimates on arrests from other crimes, serving as a falsification

test for the quality of the UCR data. The rationale is that if some unobservable changes in

crime reporting are correlated with the treatment, then other crime outcomes should also

increase when DUI checkpoints are banned. Furthermore, I can also examine whether the

50An example of a zero population agency is a university police, which covers the same jurisdictions as a
city police department.

35



increase in DUI arrests is due to the UCR hierarchy rules.51

In panels (a) and (b) of Appendix Figure 1.10, I estimate the effect of a DUI checkpoint

ban on index crimes, which are less likely to be affected by a checkpoint and are also con-

sidered more severe offenses than DUIs. I do not find any evidence of changes in property

crime or violent crime. This null effect implies that the results are not driven by idiosyncratic

changes in how agencies report crime. In panel (c), I examine the effect on crimes that are

commonly committed along with DUIs to detect any changes in arrests involving multiple

offenses.52,53 I find no evidence of a decline in crimes involving drugs or weapons after the

ban on DUI checkpoints. This exercise confirms that the positive effect on DUI arrests is

not driven by the change in the composition of the type of offenses being reported to the

UCR.

1.4.3 Self-Reported DUIs

I next turn to the BRFSS data to estimate whether the ban on DUI checkpoints leads

to more DUI behavior. In columns (1) and (2) of Table 1.6, I find a statistically significant

short-run increase of 0.4 percentage points (8% increase relative to the baseline mean) in

self-reported DUIs during the last 30 days. These results are consistent with those of Kenkel

(1993), who finds that DUI checkpoints lead to a modest decrease in self-reported DUIs.

Focusing on people who reported drinking (columns (3) and (4)), I find a larger effect of

around 1 to 1.1 percentage points (11%–13%) increase. In the longer run, I continue to find

51The UCR uses a hierarchy rule where it reports only the most serious crime in an incident involving
multiple offenses. For example, if an offender is arrested for DUIs and murder, then they will be classified
under the charge of murder, as it is a more severe crime compared to a DUI. This rule creates a problem if the
total number of DUI arrests remains unchanged, whereas the total number of arrests for DUI in conjunction
with other crimes (for example, drug offenses) is changing. In this case, the total number of reported DUIs
will change despite the number of actual DUI arrests remaining the same.

52The offenses I examine are drug offenses, weapon violations, assaults, and vandalism.
53Offenders committing multiple crimes may be a concern because according to my calculations using

the National Incident-Based Reporting System, in 2018 roughly 30% of offenses resulting in a DUI arrest
involved other offenses including drug offenses, vandalism or destruction of property, assaults, and weapon
law violations.

36



a positive effect, but the estimates are smaller and imprecisely estimated.54 These results

suggest that in the extensive margin, DUI checkpoint bans are increasing DUI behavior,

consistent with the results that I uncover with the FARS and UCR data.

In columns (5) and (6), I examine the effect on the intensive margin, finding a persistent

increase in the frequency of driving under the influence among individuals who reported

driving drunk. However, inference using wild-cluster bootstrapping methods cannot conclude

any significant effect.55 During the first 5 years after the ban, the number of times an

individual reports driving while drunk increases by 8%–14%. Over time, the effect increases,

and the long-run coefficients suggest a 31% increase 11 or more years after the ban. These

results are consistent with the possibility that the ban gives an immediate shock to drivers

previously deterred by a checkpoint, while those who are driving drunk may progressively

increase their frequency of doing so over time. These findings are consistent with the theory

of general deterrence, where drivers respond more to current or future DUI checkpoints than

to previous checkpoints or arrests.

1.4.4 Heterogeneity

In Table 1.7, I estimate heterogeneous treatment effects by different race groups (white

versus black).56 In columns (1) and (2), I find that the effect on DUI arrests is consistently

greater for white individuals than for black individuals. The magnitude of these estimates

indicates a weakly significant and persistent 13%–19% increase in DUI arrests involving

white offenders but a smaller insignificant 8%–11% increase involving black offenders. How-

ever, I cannot rule out with 90% confidence if the effects are significantly greater for white

individuals than for black individuals.

Focusing on the estimates using BRFSS data (columns (3)–(6)), I find that, contrary

54When using the logit or probit model (columns (1)–(4) of Appendix Table 1.6), I continue to find similar
patterns of magnitudes but a statistically significant medium-run effect.

55Poisson estimates in column (5) of Appendix Table 1.6 also confirm this result.
56Because FARS did not start reporting drivers’ races until 1991, I did not conduct this exercise using the

FARS data.

37



to the results from the UCR data, banning DUI checkpoints may lead to an increase in

self-reported DUI behaviors among black individuals compared to white individuals. One

possible explanation for these heterogeneous treatment effects is the location where police

officers decide to conduct a DUI checkpoint. If checkpoints are placed disproportionately

and more frequently in neighborhoods with more racial minorities, then they can also have

a disproportionate deterrent effect. Together, these point estimates support the notion

that prohibiting DUI checkpoints may alleviate racial gaps in DUI arrests and that DUI

checkpoints could contribute to greater racial disparities. However, I cannot conclusively

reject the hypothesis that DUI checkpoints are equitable.

In Appendix Table 1.7, I consider heterogeneous treatment effects by different age groups.

Given the complexity in identifying dynamic effects by cohorts, I report the overall average

treatment effects.57 These findings are generally mixed. Panel I shows the largest effect

on DUI behavior for the older group (30–39 years old and 40 or older). For DUI arrests,

panel II shows that the effect may be larger for the younger group (29 or younger and 30–39

years old). However, it is uncertain whether these effects are significantly different between

different age groups or not. Turning to the BRFSS estimates from panels III and V, I find the

largest (and significant) effect among 30- to 39-year-olds. However, there is limited evidence

on whether these effects are significantly different between different age groups.

1.5 Conclusion

Since DUI checkpoints were introduced, lawmakers have debated about whether to al-

low states to continue conducting them. As of 2022, DUI checkpoints are not conducted

in 11 states, with some considering implementing bans (Chaduvula 2019, Gutierrez 2021).

Although these checkpoints have been in place for several decades, there is limited evidence

on their causal effect and the potential consequences of making them illegal. In this paper,

57For example, the estimated short-run effects for ages 16–29 will be identified off different samples than
the long-run effect for the same age group, since those who are between 16 and 29 within the first few years
following a DUI checkpoint ban will become part of the older cohort group after several years.

38



I fill this gap by exploiting the spatial and temporal variation in state policies banning DUI

checkpoints to estimate their impact on DUI fatalities, arrests, and behavior.

Using data from FARS, I find a short- and medium-run effect of DUI checkpoint bans,

though the medium-run effects are sometimes imprecisely estimated. My preferred model’s

point estimate suggests a 12.4% increase in DUI fatalities within the first five years follow-

ing a ban, equating to an annual cost of approximately $6.4 billion in terms of lives lost

from DUIs.58 These findings are robust to various functional forms and the use of new

difference-in-differences approaches that account for treatment effect heterogeneity. Event

study analyses and falsification tests further support the causal interpretation of these esti-

mates.

An important channel for the increase in alcohol-related traffic fatalities appears to be an

increase in DUI incidents. Analysis of data from the UCR reveals a persistent increase in DUI

arrests. Additionally, data from the BRFSS indicate a short-run increase in self-reported

DUI behavior on the extensive margin after DUI checkpoints are banned. Together, these

findings highlight the effectiveness of salient and targeted enforcement strategies, such as

DUI checkpoints, in curbing dangerous driving behaviors across a broad spectrum of drivers,

regardless of their sobriety status.

58To estimate this number, I take the estimated percentage change from the preferred estimate to calculate
the total increase in DUI fatalities among states that allow the use of DUI checkpoints. I then convert the
total additional fatalities to total annual costs, assuming that the value of statistical life is approximately $7
million (Banzhaf 2021).

39



1.6 Table & Figures

1.6.1 Figures

Figure 1.1: Trend in DUI Fatalities & Arrests
(a) DUI Fatalities by Treatment Status

(b) DUI Arrests by Treatment Status

Notes: Panel a uses data from the FARS. Panel b uses data from the UCR. The rate is calculated as the total count of traffic

fatalities or DUI arrests divided by the total population for each group.

40



Figure 1.2: “First Stage” Effect of Changes in State Court Cases Arguing About DUI
Checkpoints

(a) Descriptive Trends

(b) TWFE Estimates

Notes: The data on the number of court cases that mention that a defendant was arrested at a DUI checkpoint are manually

collected from casetext.com. Panel a plots the total counts of these court cases. Panel b presents population-weighted TWFE

OLS event study estimates. The estimate in panel b includes state and time fixed effects. The bar lines in panel b represent

95% confidence intervals generated using standard errors clustered at the state level.

41

casetext.com


Figure 1.3: TWFE Event Study Analysis on Drunk Driving Fatalities; FARS 1980-2018
(a) Excluding State-Specific Linear Time Trends

(b) Including State-Specific Linear Time Trends

Notes: Population-weighted estimates are generated using data from the 1980-2018 FARS. All estimates include state and year

fixed effects and my preferred set of control variables. Panel a excludes state-specific linear time trend and panel b includes

state-specific linear time trend. The bar lines represent 95% confidence intervals generated using standard errors clustered at

the state level.

42



Figure 1.4: Robustness to the Use of New Difference-in-Differences Strategy; FARS
1980-2018

(a) Sun & Abraham

(b) Stacked DD

(c) Callaway & Sant’Anna

Notes: Population-weighted estimates are generated using data from the 1980-2018 FARS. All estimates include state and

year fixed effects and my preferred set of control variables. For panel c, the outcome variable is the residuals after I regress my

outcome on my preferred set of controls. The counterfactuals for panel c are restricted to not-yet-adopting states. The bar lines

represent 95% confidence intervals generated using standard errors clustered at the state level (panels a and b) or bootstrapped

standard errors (panel c).

43



Figure 1.5: Event Study Analysis on DUI Arrests, UCR 1980-2018
(a) TWFE (b) Sun & Abraham

(c) Stacked DD (d) Callaway & Sant’Anna

Notes: Population-weighted estimates are generated using data from the 1980-2018 UCR. All estimates include state and time fixed effects and my preferred set of control

variables. For panel d, the outcome variable is the residuals after I regress my outcome on my preferred set of controls. The counterfactuals for panel d are restricted to not-yet

adopting states. The bar lines represent 95% confidence intervals generated using standard errors clustered at the state level (panels a to c) or bootstrapped standard errors

(panel d).

44



1.6.2 Tables

Table 1.1: Year of DUI Checkpoint Bans by State

State Treament Year
Alaska Pre-1980
Idaho 1988
Iowa 1986
Louisiana 1989
Michigan 1993
Minnesota 1994
Oregon 1987
Rhode Island 1989
Texas 1991
Washington 1988
Wisconsin 1991
Wyoming Pre-1980

Table 1.2: Estimated Effect of DUI Checkpoint Bans on Drunk Driving Fatalities, FARS
1980-2018

(1) (2) (3) (4)
0 to 5 Year After 0.170* 0.117* 0.123** 0.129+

(0.067) (0.049) (0.034) (0.069)

6 to 10 Years After 0.142+ 0.115+ 0.125** 0.119+

(0.084) (0.058) (0.039) (0.062)

11+ Years After 0.046 0.097 0.105+ 0.093
(0.098) (0.069) (0.058) (0.066)

N 1,970 1,970 1,970 14,138
Controls? No Yes Yes Yes

Model TWFE TWFE
Sun &

Abraham
Stacked
DD

+ P < .10; * P < .05; ** P < .01

Notes: Population-weighted estimates are generated using data from the 1980-2018 FARS. All estimates include state and year

fixed effects and all of my preferred set of control variables. Standard errors clustered at the state-level are reported inside the

parenthesis.

45



Table 1.3: Estimated Effect of DUI Checkpoint Bans on DUI Fatalities: Using Subset of
Counties, FARS 1980-2018

Population Urbanicity Density

(1) (2) (3) (4) (5) (6)
0 to 5 Year After 0.137* 0.028 0.131** 0.069 0.121* 0.090

(0.052) (0.058) (0.046) (0.075) (0.046) (0.072)

6 to 10 Years After 0.137* -0.023 0.135* 0.041 0.124* 0.056
(0.059) (0.074) (0.054) (0.096) (0.056) (0.092)

11+ Years After 0.125+ -0.095 0.131* -0.015 0.109 0.019
(0.071) (0.113) (0.061) (0.113) (0.067) (0.110)

N 1,970 1,719 1,967 1,809 1,970 1,773
≥45000 <45000 ≥60 <60 ≥1000 <1000

+ P < .10; * P < .05; ** P < .01

Notes: Population-weighted estimates are generated using data from the 1980-2018 FARS. All estimates include state and

year fixed effects and all of my preferred set of control variables. Standard errors clustered at the state-level are reported inside

the parenthesis. Data are aggregated to a state-by-year panel using specific sets of counties. Column 1 uses counties with at

least 45,000 population. Column 2 uses counties with less than 45,000 population. Column 3 uses counties with at least 60%

of residents living in urban areas. Column 4 uses counties with less than 60% of residents living in urban areas. Column 5 uses

counties with a weighted population density of at least 1000. Column 6 uses counties with a weighted population density of

less than 1000.

Table 1.4: Estimated Effect of DUI Checkpoint Ban on Other Traffic Fatalities

(1) (2) (3) (4)

All Non-DUI
Non-DUI:
Speeding

Non-DUI:
Weekend
Night

0 to 5 Year After 0.005 -0.052 -0.111 -0.070
(0.023) (0.032) (0.074) (0.047)

6 to 10 Years After 0.021 -0.024 -0.006 0.001
(0.040) (0.040) (0.126) (0.058)

11+ Years After 0.008 -0.039 -0.044 -0.076
(0.049) (0.058) (0.142) (0.092)

N 1,970 1,970 1,867 1,970

+ P < .10; * P < .05; ** P < .01

Notes: Population-weighted estimates are generated using data from the 1980-2018 FARS (columns 1, 3, and 4) and 1982-2018

FARS (column 2). All estimates include state and year fixed effects and my preferred set of control variables. Standard errors,

clustered at the state level, are reported inside the parenthesis.

46



Table 1.5: Estimated Effect of DUI Checkpoint Bans on DUI Arrests: UCR 1980-2018

(1) (2) (3) (4)
0 to 5 Year After 0.134+ 0.118+ 0.109* 0.130+

(0.075) (0.065) (0.042) (0.076)

6 to 10 Years After 0.159+ 0.154* 0.158** 0.181*
(0.087) (0.071) (0.057) (0.078)

11+ Years After 0.121 0.143 0.195* 0.171
(0.122) (0.109) (0.084) (0.112)

N 1,896 1,896 1,896 13,504
Controls? No Yes Yes Yes

Model TWFE TWFE
Sun &

Abraham
Stacked
DD

+ P < .10; * P < .05; ** P < .01

Notes: Population-weighted estimates are generated using data from the 1980-2018 UCR. All estimates include state and year

fixed effects, and my preferred set of control variables. Data are aggregated to state-by-year panel using agencies that report

at least once a month. Standard errors, clustered at the state level, are reported inside the parenthesis.

47



Table 1.6: Estimated Effect of DUI Checkpoint Bans on Self-Reported Drunk Driving, BRFSS 1984-2018

Drink Drive Yes/No Drink Drive Frequency

(1) (2) (3) (4) (5) (6)
0 to 5 Years After 0.0039* 0.0041* 0.0113* 0.0096* 0.1276* 0.0814*

(0.0018) (0.0017) (0.0049) (0.0040) (0.0532) (0.0399)
{0.083}+ {0.08}+ {0.068}+ {0.073}+ {0.071}+ {0.125}

[4e-04,0.0076] [4e-04,0.0079] [0.0015,0.0217] [9e-04,0.0184] [0.0168,0.2418] [-0.0052,0.1687]

6 to 10 Years After 0.0009 0.0018 0.0060 0.0042 0.1696 0.1335
(0.0021) (0.0019) (0.0064) (0.0047) (0.1091) (0.0914)
{0.677} {0.37} {0.539} {0.539} {0.244} {0.326}

[-0.0029,0.005] [-0.0013,0.005] [-0.0046,0.0175] [-0.0053,0.0144] [-0.0372,0.3802] [-0.0718,0.3492]

11+ Years After 0.0025 0.0017 0.0099 0.0080 0.2690+ 0.2695+

(0.0042) (0.0037) (0.0103) (0.0076) (0.1551) (0.1467)
{0.599} {0.692} {0.445} {0.467} {0.157} {0.184}

[-0.0061,0.0119] [-0.0058,0.0097] [-0.0082,0.0295] [-0.0075,0.0256] [-0.0277,0.5725] [-0.0508,0.6103]
Mean of DV 0.051 0.051 0.086 0.086 0.466 0.466
N 4,221,619 4,221,619 2,157,199 2,157,199 78,412 78,412
Sample Everyone Everyone Drinker Drinker Drunk Driver Drunk Driver
Controls? No Yes No Yes No Yes

+ P < .10; * P < .05; ** P < .01

Notes: Survey-weighted estimate is generated using data from the 1984-2018 BRFSS. Every estimates include state and year-by-month fixed effects and all of my preferred set

of control variables and demographic controls (gender, race/ethnicity, age, and education). The sample for columns 3 and 4 is restricted to individuals who reported drinking

at least one alcoholic beverages in the past 30 days. The sample for columns 5 and 6 is restricted to individuals who reported drinking and driving at least once in the past 30

days. Standard errors clustered at the state-level are reported inside the parenthesis. The p-values obtained using wild-cluster bootstrapping are shown inside the curly bracket

and the 90% CIs generated using wild-cluster bootstrapping are shown inside the square bracket.

48



Table 1.7: Heterogeneous Treatment Effects by Whites vs. Blacks

Arrests Drink-Drive Everyone Drink-Drive Drinker Drink-Drive Frequency
(1) (2) (3) (4)

Whites Blacks Whites Blacks Whites Blacks Whites Blacks

0 to 5 Year After 0.119 0.099 0.004 0.009 0.009* 0.021 0.087+ 0.243+

(0.074) (0.117) (0.002) (0.008) (0.004) (0.017) (0.043) (0.142)
{0.175} {0.492} {0.1} {0.388} {0.099}+ {0.196}

[-0.001,0.008] [-0.013,0.031] [1e-04,0.018] [-0.024,0.069] [0.002,0.174] [-0.06,0.559]

6 to 10 Years After 0.178+ 0.104 0.002 -2e-04 0.005 -0.001 0.116 0.433*
(0.091) (0.159) (0.002) (0.008) (0.004) (0.019) (0.088) (0.202)

{0.369} {0.992} {0.418} {0.961} {0.35} {0.348}
[-0.001,0.006] [-0.038,0.038] [-0.004,0.014] [-0.082,0.081] [-0.069,0.309] [-0.241,1.146]

11+ Years After 0.174 0.076 0.002 -0.003 0.007 -0.001 0.241 0.612**
(0.135) (0.159) (0.004) (0.008) (0.006) (0.018) (0.147) (0.227)

{0.712} {0.838} {0.419} {0.977} {0.209} {0.083}+
[-0.006,0.01] [-0.023,0.017] [-0.005,0.02] [-0.048,0.049] [-0.069,0.567] [0.065,1.227]

N 1,914 1,903 3,629,480 348,140 1,917,265 133,358 68,868 4,511

+ P < .10; * P < .05; ** P < .01

Notes: Weighted estimates are generated using data from the 1980-2018 UCR (columns 1 and 2), and 1984-2018 BRFSS (columns 3 to 8). All estimates include state and

time fixed effects, and my preferred set of control variables. Standard errors, clustered at the state level, are reported inside the parenthesis.

49



Pretextual Stop Restriction and Policing: Evidence

from Los Angeles

Abstract: This paper explores the impact of the Los Angeles Police Department (LAPD)’s
restriction on pretextual stops on policing behavior and public safety. Using data on all Cal-
ifornia traffic stops, I find compelling evidence that the policy led to an immediate reduction
in stops for equipment or non-moving violations. However, I find little evidence that the
overall number of total stops decreased in the short run, potentially due to police substitution
behavior. This finding is consistent with my economic framework, which suggests that police
officers will respond to increased scrutiny placed on some tasks by shifting their behavior to
other tasks. At the same time, I find that this policy led to an approximately 15 percent
reduction in the number of racial minorities stopped by police officers. Focusing on traffic
stop outcomes, I document that the number of stops resulting in a warning decreased, and
conversely, the number of stops resulting in a citation may have increased. Moreover, the
policy led to fewer searches and contraband found, but little change in contraband seized.
Finally, I find little evidence that the number of reported crimes, arrests, and traffic fatalities
increased following the restriction of pretextual stops. Together, my findings imply that the
LAPD’s pretextual stop restriction achieved its intended goal of reducing racial disparities
without diminishing public safety.

2.1 Introduction

With recent social justice movements and incidents of police brutality, the public’s trust

in the police has fallen recently. For instance, in 2023, confidence in the police fell to an all-

time low of 43 percent, down 10 percentage points from 2019 and 21 percentage points from a

record high in 2004 (Gallup 2024). Furthermore, another Gallup poll shows that 89 percent of

Americans believe policing needs major or minor changes (McCarthy 2022). This decline in

trust in the police highlights the ongoing principal-agent problem between the public and the

police. In this context, the public (principal) aims to maximize social we