Keep the Kids Inside?

Juvenile Curfews and Urban Gun Violence

Jillian B. Carr∗and Jennifer L. Doleac†

Date of current draft: December 2015

We thank Mark Anderson, Greg DeAngelo, David Eil, Bill Gale, Sara Heller, Judy Hellerstein, Mark Hoekstra, JonathanMeer, Emily Owens, John Pepper, Ariell Reshef, Bernardo Silveira, Jeff Smith, Josh Teitelbaum, and Carly Urban for helpfulcomments. We also thank seminar participants at UVA Batten, UVA Law, Georgetown Law, Montana State University,and Purdue University; and conference participants at the Midwest Economics Association annual meeting, the IRP SummerResearch Workshop, the Conference on Empirical Legal Studies, and the Southern Economics Association annual meeting.∗Department of Economics, Krannert School of Management, Purdue University, carr56@purdue.edu†Batten School of Leadership and Public Policy, University of Virginia, jdoleac@virginia.edu

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Abstract

Gun violence is an important problem across the United States. However, the impact of government

policies on the frequency and location of gunfire has been difficult to test due to limited data. The

data that do exist suffer from broad and non-random underreporting. This paper uses a new, more

accurate source of data on gunfire incidents to measure the effects of juvenile curfews in Washington,

DC. Juvenile curfews are a common, but extremely controversial, policy used in cities across the United

States. Their goal is to reduce violent crime by keeping would-be offenders and victims indoors, but

removing bystanders and witnesses from the streets could reduce their deterrent effect on street crime.

The net effect on public safety is therefore ambiguous. We use exogenous variation in the hours of the

DC curfew to identify the policy’s causal effect on gun violence. We find that, contrary to its goal of

improving public safety, DC’s juvenile curfew increases the number of gunfire incidents by 150% during

marginal hours.

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1 Introduction

Gun violence is a chronic problem in the United States. Nationally in 2012, 11,622 people were killed by

assault with a firearm.1 Many more people are injured by guns each year: in 2011, 693,000 individuals were

treated in emergency rooms for injuries due to assaults by firearms and similar mechanisms.2 Gun violence

takes a particularly large toll on young people: according to the CDC, homicide accounted for 18% of deaths

for males ages 15-19 and 20-24, more than for any other age group. For black males, homicide is the leading

cause of death for those age groups, explaining 48% and 50% of deaths, respectively (CDC, 2013).

Cohen and Ludwig (2003) wrote that "policymakers who are concerned about America’s problem with

lethal violence must ask: how can we prevent young men from shooting one another?" This has been

a difficult question to answer, and continues to attract a great deal of academic and policy attention.3

In general, violence-prevention policies can work one of two ways: (1) by deterring violence,4 or (2) by

incapacitating would-be offenders.5 If offenders have high discount rates and are unlikely to be deterred by

future punishments — a la Becker (1968) — then limiting their opportunities to commit crime could be the

most effective crime-prevention policy. With this in mind, cities across the United States have enacted and

actively enforce juvenile curfews.

Juvenile curfews require young people to be home during the nighttime hours when crime is most preva-

lent. Their goal is to reduce criminal activity via an incapacitation effect, but these curfews might unin-

tentionally reduce a deterrent effect that comes from having lots of people around. By incentivizing young

people (and by extension their caregivers) to be at home, juvenile curfews remove many would-be bystanders

and witnesses from public areas. Removing those people decreases the probability that any remaining of-

fenders will get caught (because there are fewer witnesses who would call or assist the police), as well as

the potential punishment (which would be higher if bystanders were injured). This idea is not new: Jane

Jacobs (1961) wrote that "A well-used street is apt to be a safe street. A deserted street is apt to be unsafe."

However, the net effect of juvenile curfews on public safety is unknown, and so the passage and enforcement

of such policies continues unabated.1These numbers do not include suicides. CDC report, “Deaths: Final Data for 2012,” table 10.2CDC: National Hospital Ambulatory Medical Care Survey: 2011 Emergency Department Summary Tables.3Much of the literature on gun violence has focused on the effects of laws that restrict gun ownership or use (e.g., Cook,

1983; Lott and Mustard, 1997; Black and Nagin, 1998; Ludwig, 1998; Duggan, 2001; Marvell, 2001; Moody, 2001; Ayres andDonohue, 2003; Donohue, 2004; Mocan and Tekin, 2006; Duggan, Hjalmarsson, and Jacob, 2011; Cheng and Hoekstra, 2013;Manski and Pepper, 2015). Overall, there is mixed evidence that these laws improve public safety; results depend heavily onidentification strategy and data quality.

4Deterring crime requires changing the relative costs and benefits of committing a crime in such a way that would-be offendersrationally choose not to offend. Deterrence-based policies typically involve increasing the punishment or the probability of gettingcaught.

5Incapacitation is often thought of as synonymous with incarceration. In this paper, we follow the literature and referto policies that operate by changing the relative costs and benefits of being in a particular location at a particular time as"incapacitation polices." The idea is that these policies reduce the opportunity to commit a crime, rather than the relativecosts and benefits of committing a crime, per se. Mandatory schooling and summer jobs for teens are examples of policies thatoperate in this manner.

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In this paper, we test the net effect of juvenile curfews on the number of gunfire incidents using exogenous

changes in curfew hours in Washington, DC. By law, the weekday curfew time changes from midnight to

11pm on September 1st, and back to midnight on July 1st, roughly following the school year. (We focus

here on the September change because the July change is difficult to isolate from the July 4th holiday.) If

curfews reduce crime, then when the curfew shifts to 11pm rather than midnight, crime between 11pm and

midnight should go down. To isolate the effect of the juvenile curfew from seasonal changes in gun violence,

we compare the effect in the 11pm hour on weekdays to effects during two sets of control hours: the 11pm

hour on weekends (which is always before curfew), and the midnight hour (which is always after curfew).

With a nod to the concept of a witching hour,6 we will henceforth refer to the treated hour – 11-11:59pm

on weekdays – as the "switching hour."

We use the full universe of gunfire incidents detected by an audio sensor technology called ShotSpotter

(described in more detail below) as our outcome measure. There are several advantages to using ShotSpotter

data in this context: (1) Gunfire incidents capture many more of the threatening uses of guns than do

homicides. This results in more variation in the outcome measure, which makes it easier to pick up policy

effects. (2) ShotSpotter data are more highly correlated with actual gunfire than 911 call and other reported

crime data, reducing measurement error. (3) The accuracy of gunfire detection is unaffected by the change

in curfew time, so using these data removes the potential confounding effect of a simultaneous change in

reporting.

Using ShotSpotter data, we estimate that the juvenile curfew in Washington, DC, increases the number

of gunfire incidents. Figure 1 plots the residualized number of gunfire incidents7 during the switching hour.

It shows an increase in gunfire after the curfew switches to 11pm on September 1st. A more rigorous

examination of the data confirms this effect. On average, there are 0.015 more gunfire incidents during the

switching hour after September 1st than during that hour before the curfew changed; this is a 50% increase

relative to the late-curfew baseline. However, this effect does not fully isolate the effect of the curfew

from seasonal changes in gun violence. Controlling for changes in gun violence during similar, non-treated

hours (11pm on weekends and midnight) provides a cleaner estimate: the curfew increases gun violence by

0.045 incidents per hour (approximately 150% of the baseline). This aggregates to seven additional gunfire

incidents per week, city-wide, during the switching hour alone.

We can rule out a number of alternative competing hypotheses. For instance, the increase in observed

gun violence is not simply due to an increase in reporting, since our measure of gun violence does not6"The witching hour... was a special moment in the middle of the night when every child and every grown-up was in a deep

deep sleep, and all the dark things came out from hiding and had the world all to themselves." – Dahl (1982)7The residuals represent the remaining variation in gunfire incidents, after controls for the fixed effects and controls in our

regression discontinuity specification.

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rely on reporting. We rule out seasonal effects using a difference-in-difference-in-regression-discontinuity

approach, and by testing for effects during other hours of the day. The absence of any effect during other

(non-switching) hours also helps rule out the possibility that gun violence is simply shifted to other times.8

Finally, our estimates are not driven by our model choice or other functional form assumptions. These results

suggest that on balance, the deterrent-reducing effect of juvenile curfews outweighs the incapacitation effect.

Using traditional crime data — such as 911 calls or reported crimes — for this analysis would not allow us

to study this effect. Like some other types of crime, gun violence is likely underreported in a highly-selected

manner. Particularly in inner-city communities that distrust the police, gunshots may not be reported

unless the bullet hits someone and medical assistance is required (and even then some individuals might

avoid hospitals to avoid arrest). The result is that traditional data on reported gunfire (via 911 calls) or

violent crime (via reported crime data) are extremely noisy and potentially unrepresentative measures of the

timing and frequency of gunfire incidents. In addition, most policy interventions that aim to reduce gunfire

probably also affect reporting rates. Any empirical analysis of a policy intervention’s impact on gunfire will

therefore be biased, and often the direction of the bias will be unknown (Pepper, Petrie, and Sullivan, 2010).

In the past, these concerns have limited researchers to using homicide (which is reported with near-perfect

accuracy) as an outcome measure. There are two problems with this: first, homicide is a relatively rare event,

and limited variation in the outcome makes it difficult to detect policy effects. Second, homicide is not the

only outcome of interest. Ideally, we would observe all instances where a gun threatened someone’s safety.

If we define gun violence in this way, a very small share of gun violence events result in homicides.

For comparison, we also consider the effects of the curfew on reported crime and 911 calls, using geo-coded

data from the Metropolitan Police Department (MPD). If we wanted to study the impacts of this policy on

gun violence without ShotSpotter data, these are the data we would have to use. The results are imprecise

but generally suggest that the early curfew decreases gun violence. This different (and we argue incorrect)

conclusion is likely due to the simultaneous effect of the curfew on reporting behavior, and emphasizes the

problem with using traditional crime data for the study of gun violence.

1.1 Background on juvenile curfews

Juvenile curfews are common in cities across the country, but they are extremely controversial for several

reasons: (1) They give police officers discretion to stop any young-looking person who is out in public at

night. Some worry this results in disproportionate targeting of racial minorities and contributes to tense

relationships with law enforcement.9 (2) They override the decisions of parents who would allow their kids8This is consistent with the finding in Doleac and Sanders (2015) that violent crime is not easily shifted across the day.9A recent interview with several DC teenagers provides anecdotal evidence that this is a legitimate concern in the city. An

excerpt: “Benn: And do you feel you’re being protected and served by the police? Doné: No way. I feel more threatened by

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to stay out late. (3) They divert police resources from other, potentially more productive, activities.

There is little previous work on the causal impacts of juvenile curfew policies. Kline (2012) studied the

impact of juvenile curfews on juvenile and non-juvenile arrest rates in cities across the country. He finds that

juvenile arrests go down following the enactment of new curfew laws. He also finds evidence that arrest rates

for older individuals decline, suggesting that juvenile curfews have spillover effects. However, arrest rates

are a function of not only criminal behavior, but police behavior and witnesses’ behavior. Curfew laws likely

affect all of these. Of particular concern, arrest rates might fall if witnesses and victims are less willing to

cooperate with police as a result of heavy-handed curfew enforcement. Similarly, enforcing the curfew could

distract police from solving criminal cases. Both effects could contribute to the reduction in arrests found in

the study. The advantage of looking at arrest rates is that the age of the offender is known; the advantage

of using ShotSpotter data is that we are able to measure effects on actual criminal activity.

Another key difference between our paper and Kline (2012) is that our empirical strategies address slightly

different, but highly complementary, questions: Kline considers the net effects of implementing new curfew

policies, including any distrust they might generate. In contrast, we consider the effect of incentivizing local

residents to go home during a marginal hour in a city with an existing curfew. This allows us to focus on

the countervailing incapacitation and deterrent effects of curfews. However, our estimates do not capture

these policies’ effects on residents’ trust of the police; such effects could worsen public safety further.

There is a slightly larger literature on other types of non-incarceration incapacitation policies. For

instance, mandatory schooling keeps juveniles occupied when they might otherwise be unsupervised and

likely to get into trouble. Anderson (2014) uses minimum dropout ages to measure the effect of mandatory

school attendance on crime. He finds that minimum dropout age requirements decreased arrest rates for

individuals aged 16 to 18 by 17%. Jacob and Lefgren (2003) also study the impact of school attendance on

crime, using exogenous variation in teacher in-service days to estimate the causal impact of being in school

on juvenile delinquency. They find that juvenile arrests for property crimes go down by 14% when school is

in session, while juvenile arrests for violent crimes go up by 28%. This suggests that gathering juveniles in

one place unintentionally increases interpersonal conflict that spills over into non-school hours.

We view the present study as contributing to the academic literature in several ways: (1) It measures the

public safety impacts of juvenile curfews, which are a controversial but widely-used crime-reduction policy

about which there is little empirical evidence. (2) To our knowledge, this is the first study to use ShotSpotter

data, or any data generated by high-tech surveillance tools, to evaluate policy effects. (3) It considers the

net effects of incapacitation policies on criminal behavior, thereby adding to a growing literature on this

them than by anybody else. Benn: Would you all ever help a police officer to apprehend a criminal? Doné: No. Martina: Hellno.” (Politico, 2015)

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topic. (4) It addresses gun violence, which is of particular interest in the United States but is generally very

difficult to study due to the lack of reliable data.

The paper proceeds as follows: Section 2 presents a simple model of how juvenile curfews affect gun

violence; Section 3 describes the data; Section 4 describes our empirical strategies; Section 5 describes our

results; Section 6 compares the gunfire effects with effects on reported crime and 911 calls; and Section 7

discusses the results and concludes.

2 A simple model

To frame our analysis, we present a model of how gun violence is affected by incapacitation policies like

juvenile curfews:

The number of gunshot incidents in an area is a function of several factors, including the number of

would-be offenders on the streets (o) and the probability of getting caught (p). The number of would-be

offenders is a function of whether a curfew (c) is in effect. The probability of getting caught is a function of

the number (or activity level) of law enforcement officers (l) and witnesses (w) in the area; both of these are

themselves functions of c. The curfew (c) decreases o, has an ambiguous effect on l, and decreases w.

Gunshots = g[o(c), p(l(c), w(c))]

We hypothesize that dg/do > 0 and do/dc < 0, so we expect the curfew to decrease the number of

gunshots through this channel. We also hypothesize that dg/dp < 0, dp/dl > 0, and dp/dw > 0. However,

dl/dc could be positive or negative, depending on how police use their time while enforcing the curfew, and

dw/dc < 0; this makes the impact of the curfew on the probability of getting caught (dp/dc) ambiguous.

The net effect of the curfew on gunfire (dg/dc) is therefore ambiguous.

3 ShotSpotter Data

ShotSpotter data have two key advantages over traditional reported crime data: (1) they have accurate

and precise time and location stamps, and (2) they are not subject to selective underreporting that could

bias empirical estimates. By using better data, we: reduce the attenuation bias due to measurement error;

remove the selection bias resulting from variation in reporting rates over time, populations, and geographic

areas; and eliminate the confounding effects of policies’ simultaneous influences on reporting and crime.

We use ShotSpotter data from Washington, DC, from January 2006 through June 2013, aggregated to the

level of Police Service Areas (PSAs).10 The technology was first implemented in Police District 7 (Anacostia)10Each Police District is composed of seven or eight PSAs; there are 31 PSAs in our sample.

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in January 2006, then expanded to Police Districts 5 and 6 in March 2008, and to Police District 3 in July

2008. These are the areas of DC that have the highest crime rates, and so were expected to have the highest

rates of gunfire. Figure 2 shows heatmaps of the raw gunshot data for each year.11

ShotSpotter technology consists of audio sensors installed around the city; these sensors detect gunshots,

then triangulate the precise location of the sound. A computer algorithm distinguishes the sound of gunfire

from other loud noises, and human technicians verify those classifications.12 Once verified, this information

is relayed to law enforcement so that police officers can quickly respond to the scene.

There are some false positives or negatives in the data — that is, noises that aren’t gunshots that are

recorded as gunshots, or gunshots that are missed — but these mistakes will be randomly distributed, and

unaffected by the policy intervention we’re studying. (The best evidence suggests the false negative rate is

very low — less than 1%. The false positive rate is much more difficult to estimate, since the purpose of

the technology is to detect gunfire that is not reported by others. See Carr and Doleac, 2015, for a review

of current evidence on ShotSpotter’s accuracy.) ShotSpotter is currently active in over eighty cities in the

United States; while considered proprietary in most locations, the data used in this paper are available from

the MPD via public records request.

The data include the date and time that the gunfire incident was detected, the latitude and longitude of

the incident, and whether the incident consisted of a single gunshot or multiple gunshots. During the period

of interest (July 30th through October 4th, for the years 2006-2012), there were 7.8 gunfire incidents per day

across the Police Districts where ShotSpotter is currently implemented. On average, 0.9 per day occurred

during the 11pm hour. Table 1 presents summary statistics.

4 Empirical Strategy

DC’s curfew time for anyone under age 17 is 11pm on weeknights and midnight on weekends from September

through June, and midnight on all nights during July and August.13 We exploit the September 1st change11We represent the geographic dispersion of gunshots using heat maps because the large quantity of gunshots makes detecting

the most densely concentrated areas difficult if we simply plot points. We construct the maps using a “point density” operationthat creates a grid over the map and then counts the number of gunshots within each grid cell. The darker colors represent thehighest concentration of gunshots.

12The sounds are classified as gunshots, construction, fireworks, car backfire, and so on. Only those classified as gunshotincidents are included in our data.

13The Juvenile Curfew Act of 1995 states that individuals under age 17 cannot be “in a public place or on the premises of anyestablishment within the District of Columbia during curfew hours.” Exceptions are made for several reasons, including if thejuvenile is accompanied by a parent or guardian, is working, or is involved in an emergency. During most of the year, curfewhours are 11:00pm on Sunday, Monday, Tuesday, Wednesday and Thursday nights, until 6:00am the following morning. Theyare 12:01am until 6:00am on Saturday and Sunday (that is, Friday and Saturday nights). During July and August, curfewhours are 12:01am to 6:00am every night. Juveniles who are caught violating curfew are taken to the nearest police station andreleased to the custody of their parents. They can also be sentenced to perform community service. Parents who violate thecurfew law by allowing their child to be in public during curfew hours can be fined up to $500 per day. The curfew policy inWashington, DC, is very similar to policies in cities across the country.

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from midnight to 11pm as a natural experiment. (Due to the confounding effect of the July 4th holiday, we

do not use the July 1st curfew time change.) The change in the curfew time roughly follows the academic

year; school starts in late August in DC.14 For this reason, we will need to be careful to isolate the effects of

the curfew time from that of underlying seasonal trends.

We first employ a regression discontinuity (RD) analysis to measure the causal impact of the curfew on

gun violence during the switching hour. The intuition is that on September 1st each year, the incentive

for local residents to be home during the switching hour increases discontinuously; the question is whether

that discontinuity in the incentive results in a discontinuity in gunfire incidents. Data are from 34 days on

either side of the curfew change; this is the Imbens-Kalyanaraman (IK) optimal bandwidth. For this first

specification, we use data from weekdays only (the days affected by the curfew change), and we focus on

gunfire occurring during the switching hour (11-11:59pm) each day:

Gunshotsd,p = α+ β1EarlyCurfewd + β2f(dayd) + β3f(day) ∗ EarlyCurfewd+

δ1School + ωd + λdayofweek + γyear + ρPSA + ed,p, (1)

where d is the day of observation and p is the Police Service Area (PSA). Early Curfew is an indicator for

whether the weekday curfew time is 11pm, instead of midnight (that is, whether the date is September 1st or

later). ωd is a vector of weather variables, including temperature and precipitation. School indicates whether

the school year is in session, and controls for any independent effect of school attendance on behavior. This

baseline specification includes fixed effects for year, day of the week, and PSA. It includes day of the year

as the running variable, and allows the slope to vary before and after the curfew change. In our preferred

specification, the running variable function is linear, though the the estimates are similar if we use quadratic

or cubic functions (as discussed in Section 5.1). Standard errors are clustered by day of the year. The

primary coefficient of interest is β1; this tells us if the early curfew time has an effect on the level of gunfire

during the switching hour.

The outcome measure is the number of gunfire incidents detected by ShotSpotter. For ease of interpre-

tation, our preferred specifications use an OLS model. For robustness, we run similar analyses using (1) a

Poisson regression, because the outcome measure is a count variable, and (2) a Logit regression, using a 0/1

indicator of any gunshot incidents as the outcome measure. The latter should be less sensitive to outlier

hours.

It is possible that the transition from summer to fall (or a similar time trend) is driving the RD results.14School start dates vary from year to year, and do not perfectly coincide with the September 1st curfew change: August 28,

2006; August 27, 2007; August 25, 2008; August 24, 2009; August 23, 2010; August 22, 2011; and August 27, 2012.

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To test this, we use a difference-in-RD (D-i-RD) framework to compare the 11pm hour on weekdays (the

switching hour) with the 11pm hour on weekends (which is not affected, so serves as a control). If the

juvenile curfew is driving the observed change in gunfire, it should affect only the switching hour, not the

weekend equivalent. We estimate:

Gunshotsd,p = α+ β1EarlyCurfew ∗Weekdayd + β2f(dayd)+

β3f(day) ∗ EarlyCurfew ∗Weekdayd+

δ1School + ωd + λdayofweek + γyear + ρPSA + ed,p, (2)

where β1 is the coefficient of interest. The sample for this model is 11-11:59pm on weekdays and weekends.

We include all pairwise combinations of the terms in the D-i-RD estimator. As above, we allow the various

levels and slopes to vary before and after the curfew change.

It is possible that the transition from summer to fall, independent of the curfew change, changes the

relationship between weekday and weekend activities. In that case, comparing trends in two sets of hours

(one set treated and one not treated), across weekdays and weekends, would better identify the effect of the

curfew. To test this, we employ a difference-in-difference-in-RD (D-i-D-i-RD) specification, using midnight

hours as a second set of controls (the midnight hour is always post-curfew). We compare the difference in

gunfire during the 11pm hour (which is treated) to gunfire during the midnight hour (which is a control),

across weekdays (treated) and weekends (control), testing for a discontinuity at September 1st. If the juvenile

curfew is driving any observed change in gunfire, the curfew time change should affect only the 11pm hour

on weekdays (the switching hour), not the midnight hour. (We will confirm below that crime is not shifted

to other hours.) We estimate:

Gunshotsh,d,p = α+ β1EarlyCurfew ∗Weekday ∗ 11pmHourh + β2f(dayd)+

β3f(day) ∗ EarlyCurfew ∗Weekday ∗ 11pmHourh+

δ1School + ωd + λdayofweek + γyear + ρPSA + ed,p, (3)

where the coefficient of interest is again β1. The sample is now 11pm–12:59am, on weekdays and weekends.

As in the above specifications, we include all combinations of the terms in the D-i-D-i-RD estimator, and

allow the levels and slopes to vary before and after the curfew change.

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5 Results

Table 2 presents the results of the juvenile curfew analysis using ShotSpotter data.

Column 1 shows the results of the basic RD specification, where we are interested in the coefficient on

Early Curfew. This estimates that the switch from a midnight to 11pm curfew on weekdays increases gun

violence during the switching hour. After the curfew time changes, the number of gunfire incidents increases

by 0.015 during the switching hour, or 50% of the late-curfew (pre-September 1) baseline. This estimate is

marginally significant, p < 0.10.

Column 2 shows the results of the D-i-RD specification, using the 11pm hour on weekends as a control.

Here we are interested in the coefficient on Early Curfew * Weekday, which is positive and statistically

significant. It estimates that the early curfew on weekdays increases gunfire during the switching hour by a

statistically-significant 0.044 incidents, which is 147% of the baseline.

Column 3 shows the results of the D-i-D-i-RD specification, using weekends and the midnight hour as

controls. This time were are interested in the coefficient on Early Curfew * Weekday * 11pm Hour. This

specification implies that the earlier curfew increases the number of gunfire incidents by 0.045 during the

switching hour, or 150% of the baseline. Note that while this estimate is statistically significant (p < 0.05)

it is imprecise; the 95% confidence interval suggests gunfire incidents increase by 19–280% of the baseline.

Regardless, it is reassuring that the D-i-RD and D-i-D-i-RD estimates are nearly identical. Recall that

observations are at the PSA-level, and our data cover 31 PSAs across the city. This effect size implies seven

additional gunfire incidents per week, during the switching hour alone.

Due to limited space, the coefficients for the running variable (and interactions thereof) are omitted; all

are statistically insignificant.

5.1 Robustness checks

We conduct a variety of robustness checks:

First, we consider the effect of using different bandwidths for the RD. (Our preferred bandwidth is the

IK optimal bandwidth, 34 days.) Appendix Figure A.1 plots estimates for the D-i-D-i-RD specification when

bandwidths of 5 to 50 days are used; the vertical red line is the IK optimal bandwidth used in the above

regressions. The estimate at 5 days is a bit larger than the others. Estimates at other bandwidths are very

close to our preferred estimate.

Next, we test the effect of the curfew change on gunfire during the other hours of the day. If our effects

are being driven by the changing number and composition of people out on the streets, we should only see a

statistically significant effect during the switching hour. That is what we find. Appendix Figure A.2 graphs

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the estimates by hour. Using the D-i-RD specification (because the concern is that all hours are treated,

we don’t want to select another hour as a control), we see that estimates are generally small and all are

statistically insignificant, except for the positive estimate for the 11pm (switching) hour.

Some readers might worry that we run an OLS regression even though our endogenous variable is a count

variable. This can lead to problems, since the assumption of normally distributed errors cannot be valid. To

address this concern, we run two alternative models designed for this setting. Appendix Table A.1 shows

Poisson and Logit results. The Poisson model uses the count of gunfire incidents as the outcome measure

(as in our OLS regressions); the Logit model uses a 0/1 indicator of any gunfire incidents as the outcome.

The Poisson estimates are a bit larger in magnitude and more significant, which provides assurance that

our basic OLS estimates are not driven by model choice. The Logit model gives point estimates that are

similar to those obtained from the Poisson and OLS regressions, but less precisely estimated. As a result,

the effect estimated in the Logit model is not statistically significant. Perhaps this isn’t surprising, since

we have decreased variation in the outcome variable, and the curfew was explaining some of that variance

too. Since it’s clearly worse to have two gunfire incidents rather than one, we think that total number of

incidents, rather than whether any incidents occurred or not, is the more relevant outcome variable.

Finally, we run the D-i-D-i-RD results using different functional forms of the running variable. Recall that

our preferred function is linear; we consider quadratic and cubic functions as well. Estimates, presented in

Appendix Table A.2, are nearly identical across these three specifications, though their statistical significance

decreases as including more terms reduces statistical power.

6 Comparing results using reported crime and 911 call data

For comparison, we repeat the main analysis using data on reported crime and 911 calls from the MPD. Our

goal is to see how our conclusions about curfews’ effects would differ if we used traditional crime measures.

We therefore construct outcome measures that, without ShotSpotter data, would be the best available to

study gun violence.

6.1 Reported crime and 911 call data

We use geo-coded data on reported crime and 911 calls from 2011 and 2012, aggregated to the PSA-level.

(Due to a technical problem at the MPD, geo-coded data on reported crime are not available for dates prior

to January 2011. The MPD does not maintain 911 call data for more than three years, so these are also

unavailable before January 2011.)

The reported crime data include reports of: homicide, sexual abuse, assault with a dangerous weapon,

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robbery, burglary, arson, motor vehicle theft, theft from an automobile, and other theft. We code the first

four crime types as “violent crimes," and also consider homicide separately. The data also include information

on the weapon used, if any; we code any crime in which a gun is listed as the weapon as a “gun-involved

crime.” The time and location stamps will generally be less precise than in the ShotSpotter data. The

geo-codes are reported at the block level, rather then the exact latitude and longitude. The times are often

estimates based on victims’ and witnesses’ recollections, and/or the time the incident was reported.

The 911 call data include all calls for service, not necessarily for the police. The outcome measures

of interest in this dataset are: all calls, calls for police, and calls to report gunshots. As for the reported

crime data, the geo-codes and time stamps will be less precise than in the ShotSpotter data. The geo-codes

will often be the address where the caller is calling from, rather than the location of the crime (this will

be particularly problematic for reported gunshots, where the shots could have been fired blocks away from

where they were heard). The time stamp is when the call was received.

As above, we restrict our analysis to the areas covered by ShotSpotter (Police Districts 3, 5, 6, and 7).

Summary statistics are in Table 1.

6.2 Relationship with ShotSpotter data

Carr and Doleac (2015) describe the relationship between the ShotSpotter data and traditional crime data

during this period. A primary advantage of using ShotSpotter data instead of the number of homicides as

a measure of gun violence is that there are far more of the former than the latter. (During 2012, excluding

outlier days, there were 81 reported homicides and 2234 ShotSpotter-detected gunfire incidents.) More

variation in the outcome measure improves our ability to detect policy effects. After controlling for a variety

of factors that might explain variation in crime reports and 911 calls, Carr and Doleac (2015) considers

gunfire incidents as exogenous shocks during particular hours, then estimates the effects on the number of

reports. The effects are highly statistically significant (implying that the noise in ShotSpotter data is not a

major problem), but suggest that reporting rates are extremely low: only 12.4% of gunfire incidents result in

a 911 call to report gunfire, and only 2.3% of gunfire incidents result in a reported assault with a dangerous

weapon (AWDW, the relevant crime if someone fires a gun at you). This is consistent with a model of street

crime (e.g. gang violence) where neither party is interested in involving the police.

6.3 Results using reported crime and 911 call data

Because the much shorter time period substantially decreases statistical power, we focus on the RD spec-

ification in Equation 1. The results are presented in Appendix Table A.3. While the ShotSpotter data

13

estimate that the earlier curfew increases gunfire incidents by 41% during the switching hour (close to the

50% estimate using the longer time period), the reported crime and 911 call data suggest that the earlier

curfew decreases gun violence.

The results are less precise than before, and should be considered merely suggestive. However, it is striking

that all of the coefficients using reported crime and 911 call data are negative. Using those traditional data

sources would therefore lead to the opposite conclusion about the effectiveness of this policy. Recall that

reporting behavior might change in response to the curfew, so both sets of comparison results could be biased

upward or downward. The typical solution to this problem, using homicide as an outcome measure, does

not help here: there are too few homicides during the switching hour to produce a meaningful estimate.

7 Discussion

In this paper, we use new gunshot incident data from ShotSpotter to measure the effects of a city-wide juvenile

curfew on gun violence. These data are not affected by the inaccuracies and selective underreporting that

plague traditional reported crime data. The resulting empirical estimates do not suffer from the biases that

make empirical results throughout the literature difficult to interpret. This is crucial for determining the

true impact of any policy on public safety.

The curfew policy in Washington, DC, was enacted in 1995 as an effort to improve public safety. Similar

curfew laws are in effect across the United States, but are controversial, and in some cases have been ruled

unconstitutional. While their goal is to improve public safety through an incapacitation effect, incentivizing

local residents to go home could reduce a deterrent effect on street crime. The net effect of the policy is

ambiguous. We show that in this city, at least, the juvenile curfew law increases the number of gunfire

incidents, by 0.045 additional incidents per PSA, during the switching hour. With 31 PSAs in our dataset,

this aggregates up to 1.40 extra gunfire incidents per weekday, or 6.98 extra gunfire incidents per week,

across Police Districts 3, 5, 6, and 7.

Our results suggest that curfew laws are not a cost-effective way to reduce gun violence in U.S. cities.

This does not necessarily mean that juvenile curfews are not cost-effective more broadly. We cannot measure

impacts on other types of crime, particularly minor offenses. It could be that curfews reduce those offenses

enough to offset the increase in gun violence and the infringement on juveniles’ rights and parents’ choices. It

is also possible that even if curfews do not reduce the number of gunshots, they might reduce the number of

victims when there are fewer innocent bystanders in the area. However, we doubt that most residents would

consider such an impact evidence of a real improvement in public safety — gunfire would still be audible,

and stray bullets would still be a threat. Finally, juvenile curfews might increase the amount of domestic

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violence by incentivizing kids (and their caregivers) to be home at night. This is an important potential cost

that should be considered.

Empirical evidence on this topic is particularly necessary in light of broader concerns about how to

improve trust between law enforcement and city residents. Juvenile curfews are the type of policy that many

worry worsens tensions between inner-city communities and the police. Ours is only the second rigorous

examination of the effects of juvenile curfews on public safety. This is probably due in part to the difficulty

of convincingly identifying impacts of a policy that could affect both criminal activity and reporting rates.

If we were using traditional crime data, it would be easy to explain our results as the effect of more police

scrutiny (that is, increased reporting rates) when the curfew is in effect. ShotSpotter data on gunfire incidents

provide a unique opportunity isolate the effect on crime from the effect on reporting.

One advantage of using ShotSpotter data instead of homicide data is that the larger amount of variation

in the number of gunfire incidents makes it easier to detect policy effects. However, homicides are clearly

more severe. How should we think of the cost of a gunshot that does not result in a death? One option

is to use gunfire incidents’ correlation with homicide and calculate an expected social cost of gunfire based

on the social cost of homicide. Carr and Doleac (2015) estimate that one gunfire incident results in 0.0048

additional homicides in DC. Using the social cost of homicide calculated in McCollister, French, and Fang

(2010) — $8,982,907 — we can estimate the expected social cost of gunfire incidents as 0.0048 x $8,982,907

= $43,118. This admittedly rough calculation gives researchers and policy-makers a way to compare the

social costs and benefits of policies that aim to reduce gun violence.

In this paper, we estimate that changing the curfew time from midnight to 11pm on weekdays increases

the number of gunfire incidents by 0.045 per PSA during that hour, or 6.98 gunfire incidents city-wide, per

week. Assuming that this effect is constant year-round, keeping the curfew at 11pm instead of midnight for

ten months of the year (45 weeks) implies 314.1 additional gunfire incidents annually. Using the social cost

of gunfire that we just estimated, this suggests that the early juvenile curfew in DC has an annual social

cost of over $13.5 million.15 This accounts only for the probable increase in homicides. Adding the expected

social costs of injuries, or extending these estimates to other hours, would bring the total higher.

15The other way to think about this number is that the 11pm curfew leads to 1.5 additional murders each year, on average.(0.0048 murders per gunfire incident x 314.1 additional gunfire incidents = 1.5 murders.) The social cost of those additional1.5 murders is $13.5 million.

15

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Jacob, B. A., and L. Lefgren (2003): “Are Idle Hands The Devil’s Workshop? Incapacitation, Concentration,And Juvenile Crime,” American Economic Review, 93(5), 1560–1577.

Jacobs, J. (1961): The Death and Life of Great American Cities. Random House.

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McCollister, K. E., M. T. French, and H. Fang (2010): “The cost of crime to society: New crime-specificestimates for policy and program evaluation,” Drug and Alcohol Dependence, 108, 98–109.

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8 Main tables and figures

Figure 1: Residualized Gunshot Incidents during 11pm Hour on Weekdays

Notes: Graph shows residuals of 11pm weekday gunfire (at the PSA-level) minus predicted gunfire, along with linear fits.The vertical line denotes the date of the change in weekday curfew hours from starting at midnight to 11pm. Data source:ShotSpotter data from MPD.

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Figure 2: Heatmaps of ShotSpotter-Detected Gunshot Incidents

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Gunshot Incidents in DC by Police District in 2006

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Gunshot Incidents in DC by Police District in 2007

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Gunshot Incidents in DC by Police District in 2008

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Gunshot Incidents in DC by Police District in 2009

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Gunshot Incidents in DC by Police District in 2010

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Gunshot Incidents in DC by Police District in 2011

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Gunshot Incidents in DC by Police District in 2012

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Gunshot Incidents in DC by Police District in 2013

Notes: Shaded regions show the location of detected gunfire in Washington, DC, in each year (January 2006 through June2013), along with labeled outlines of the seven Police Districts. Darker regions signify more gunfire. Note that ShotSpottersensors cover primarily Districts, 3, 5, 6, and 7; we restrict our analyses to these regions. Data source: MPD.

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Table 1: Summary Statistics

N Mean SD Min MaxGunshots in Washington, DCDaily DC SST-detected incidents 469 7.757 5.640 0 38DC SST-detected incidents, 11pm-midnight 469 0.938 1.377 0 9DC SST-detected incidents, midnight-1am 469 0.885 1.289 0 9Gunshots at the PSA-level (geographic unit of analysis)Daily PSA SST-detected incidents 11457 0.318 0.807 0 11PSA SST-detected incidents, 11pm-midnight 11457 0.038 0.250 0 6PSA SST-detected incidents, midnight-1am 11457 0.036 0.230 0 5Crime at the PSA-level (geographic unit of analysis)Daily PSA MPD reported crimes 4154 1.790 1.552 0 15PSA MPD reported crimes, 11pm-midnight 4154 0.097 0.323 0 3Daily PSA MPD reported gun-involved crimes 4154 0.143 0.392 0 3PSA MPD reported gun-involved crimes, 11pm-midnight 4154 0.011 0.110 0 2Daily PSA MPD reported violent crimes 4154 0.449 0.698 0 4PSA MPD reported violent crimes, 11pm-midnight 4154 0.034 0.188 0 2Daily PSA 911 calls 4154 17.958 7.644 1 52PSA 911 calls, 11pm-midnight 4154 0.930 1.100 0 8Daily PSA 911 calls for police 4154 13.873 6.191 0 40PSA 911 calls for police, 11pm-midnight 4154 0.759 0.970 0 7Daily PSA 911 calls reporting gunshot 4154 0.143 0.424 0 4PSA 911 calls reporting gunshot, 11pm-midnight 4154 0.012 0.115 0 2

Geographic areas covered: Police Districts 3, 5, 6, 7. Dates covered: July 30 through October 4. Data on gunshot incidentsinclude the years 2006-2012. MPD and 911 Call data cover 2011-2012.

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Table 2: Effect of Curfews on Gun Violence

RD D-i-RD D-i-D-i-RD(1) (2) (3)

SST-Detected Gunshot Incidents

early curfew 0.015* -0.027 0.015(0.008) (0.019) (0.018)

weekday -0.051*** -0.024*(0.017) (0.014)

early curfew * weekday 0.044** 0.000(0.021) (0.020)

11pm hour 0.021(0.016)

early curfew * 11pm hour -0.045**(0.021)

weekday * 11pm hour -0.027*(0.016)

early curfew * weekday * 11pm hour 0.045**(0.020)

late curfew mean .030 .030 .030

Observations 8162 11457 22914Sample is 11-11:59pm only X XSample is 11-12:59am XSample is weekdays only X

* p < .10, ** p < .05, *** p < .01.

Notes: Standard errors are clustered on the running variable (day of year) and are shown in parentheses. Results are from OLSregressions; outcome measure is the number of gunshot incidents. Analysis uses data from Police Districts 3, 5, 6, and 7. Datesincluded: 34 days (the IK optimal bandwidth) on either side of September 1st. All specifications include: whether school isin session; year, day of week and PSA fixed effects; precipitation; and temperature. ShotSpotter data source: MPD. Weatherdata source: NOAA.

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A Appendix: Additional tables and figures

Figure A.1: Effect of 11pm Curfew on Gunfire Incidents

Notes: The figure plots coefficients on an early curfew indicator and their 95% confidence intervals from D-i-D-i-RD regressions(Table 2, column 3 specification) on SST incidents in the 11pm hour using various bandwidths. Bandwidths range from 5 - 50at increments of 5. The vertical line denotes the IK optimal bandwidth, 34.

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Figure A.2: Effect of 11pm Curfew on Gunfire Incidents by Hour of Day

Notes: The figure plots coefficients on an early curfew indicator and their 95% confidence intervals from D-in-RD regressions(Table 2, column 2 specification) on SST incidents in each hour of the day. The 11pm estimate is the result of interest.

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A.1 Alternative specifications

Table A.1: Poisson and Logit Results: Effect of Curfews on Gun Violence

Poisson Logit(1) (2) (3) (4) (5) (6)

SST-Detected Gunshot Incidents

early curfew 1.698** 0.619 1.418 1.485 0.817 1.552(0.456) (0.221) (0.513) (0.416) (0.272) (0.658)

weekday 0.260*** 0.507* 0.324*** 0.504*(0.100) (0.204) (0.125) (0.184)

early curfew * weekday 2.812** 1.090 1.852 0.927(1.323) (0.534) (0.867) (0.450)

11pm hour 1.574 1.406(0.490) (0.488)

early curfew * 11pm hour 0.413** 0.521(0.159) (0.256)

weekday * 11pm hour 0.492** 0.695(0.168) (0.270)

early curfew * weekday * 11pm hour 2.634** 1.937(1.129) (1.042)

late curfew mean .03 .036 .033 .024 .027 .027

Observations 8162 11457 22914 6734 10787 22914Sample is 11-11:59pm only X X X XSample is 11-12:59am X XSample is weekdays only X X

* p < .10, ** p < .05, *** p < .01.

Notes: Standard errors are clustered on the running variable (day of year) and are shown in parentheses. Poisson specification:Poisson regression with number of gunshot incidents as the outcome measure. Coefficients are presented as incident-rate ratios;1 = no effect. Logit Specification: outcome measure is a 0/1 indicator of any gunshot incidents. Coefficients reported asodds ratios; 1 = no effect. Dates included: 34 days before and after September 1; years 2006-2012. Analysis uses data fromPolice Districts 3, 5, 6, and 7. All specifications include: whether school is in session; year, day of week and PSA fixed effects;precipitation; and temperature. ShotSpotter crime data source: MPD. Weather data source: NOAA.

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Table A.2: Effect of Curfews on Gun Violence

linear quadratic cubic(1) (2) (3)

SST-Detected Gunshot Incidents

early curfew * weekday * 11pm hour 0.045** 0.035 0.047(0.020) (0.021) (0.031)

late curfew mean .030 .030 .030

Observations 22914 22914 22914Sample is 11-11:59pm onlySample is 11-12:59am X X XSample is weekdays only

* p < .10, ** p < .05, *** p < .01.

Notes: Standard errors are clustered on the running variable (day of year) and are shown in parentheses. Results are fromD-i-D-i-RD OLS regressions; outcome measure is the number of gunshot incidents. Analysis uses data from Police Districts 3,5, 6, and 7. Dates included: 34 days (the IK optimal bandwidth) on either side of September 1st. All specifications include:whether school is in session; year, day of week and PSA fixed effects; precipitation; and temperature. ShotSpotter data source:MPD. Weather data source: NOAA.

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A.2 Reported crime and 911 call data

Table A.3: Effect of Curfews on Gun Violence

ShotSpotter Incidents MPD Reported Crime 911 Calls for ServiceGun- For To Report

All All Homicides Involved Violent All Police Gunshots(1) (2) (3) (4) (5) (6) (7) (8)

early curfew 0.007 -0.023 -0.001 -0.010 -0.009 -0.065 -0.083 -0.016(0.010) (0.018) (0.001) (0.007) (0.011) (0.090) (0.078) (0.011)

late curfew mean .017 .100 .000 .012 .04 .885 .721 .013

Observations 3007 3007 3007 3007 3007 3007 3007 3007Sample is 11-11:59pm only X X X X X X X XSample is weekdays only X X X X X X X XSample is 2011-2012 X X X X X X X X

* p < .10, ** p < .05, *** p < .01.

Notes: Standard errors, clustered by day of year, are shown in parentheses. Results are from OLS regressions. Analysis usesdata from Police Districts 3, 5, 6, and 7. Dates included: 34 days (the IK optimal bandwidth) on either side of September 1st.All specifications include: whether school is in session; year, day of week and PSA fixed effects; precipitation; and temperature.ShotSpotter, MPD and 911 call data source: MPD. Weather data source: NOAA.

26