The geography, incidence, and underreporting of gun violence: new evidence using ShotSpotter data Jillian B. Carr∗ and Jennifer L. Doleac† December 2015

We thank three anonymous referees for valuable feedback. We also thank participants in the APPAM Big Data PreConference Workshop. ∗ Department of Economics, Purdue University, [email protected] † Batten School of Leadership and Public Policy, University of Virginia, [email protected]

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Abstract Criminal activity is often selectively underreported, which can make it difficult to understand public safety problems and devise effective policy strategies to address them. However, new surveillance technologies are facilitating the collection of more accurate data on crime. In this paper, we describe data on gunfire incidents, recorded using a tool called ShotSpotter. We also compare those data with previously-available data on reported crime and 911 calls to estimate baseline correlations between these measures as well as the causal effects of gunfire incidents on reporting. This provides evidence on the extent of underreporting of gun violence. Finally, we use these data to replicate and extend Levitt (1998), strengthening his evidence that police hiring increases the reporting of serious crimes. The characteristics and research potential of these data are relevant to surveillance data more broadly; while such data have not yet been exploited by social scientists, they could be extremely valuable for crime research.

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Introduction

The selective underreporting of criminal activity is a primary concern for researchers. No traditional source of crime data includes the full universe of criminal activity. This is concerning because the reporting of criminal activity probably varies across communities and crimes in a non-random manner. Of even greater concern, many policy interventions that researchers might like to evaluate (such as hiring additional police officers) likely affect both the amount of crime and the rate at which crime is reported. Any analyses using traditional crime data will therefore produce biased estimates, and often that bias will be unsigned (Pepper, Petrie, and Sullivan, 2010). High-tech surveillance data could be a game-changer. As a case study, this paper describes a new source of data on gun violence, from a widely-used surveillance tool called ShotSpotter. It compares the ShotSpotter (surveillance) data with the best available data on gun violence from traditional sources (data on reported crimes and 911 calls), and uses them to consider the degree of crime underreporting as well as the value of the ShotSpotter data for policy analyses. Using data from Washington, DC, and Oakland, CA, we find evidence of severe underreporting of gun violence. An individual gunfire incident provides an exogenous shock to the likelihood of a 911 call or crime report, so allows us to estimate the effect of gunfire on reporting. In DC, only one in eight gunfire incidents result in a 911 call to report shots fired. Any time a gun is fired with the intent to injure someone (or to threaten someone with injury), an assault with a dangerous weapon (AWDW) has been committed. However, only one in forty-three gunfire incidents in DC and one in fifteen gunfire incidents in Oakland result in a reported AWDW. Unless the remaining 93-98% of gunfire in these cities is not intended to be threatening (which seems highly unlikely), this type of crime is reported at extremely low rates. The effect of gunfire incidents on reporting varies by Police District, implying that underreporting is a larger problem in some places than others. Together, these estimates suggest that analyses based on traditional data could be biased, and that there is a lot of room for crime-fighting policies to increase reporting. With this in mind, we turn next to a policy lever that is commonly assumed to affect the reporting of criminal activity: police hiring. Depending on the context, and the relationship between law enforcement and the local community, putting more police on the streets could increase or decrease the reporting of crime. We use ShotSpotter data on gunfire to replicate and extend the analysis in Levitt (1998), which tested the effect of police hiring on the ratio of reported crime to the number of homicides. If we assume that the quantities of other crimes move in fixed proportions to the number of homicides (for example, if the number of homicides doubles, the numbers of rapes, robberies, and assaults also double), and that homicides are accurately reported (generally believed to be true), we can attribute any change in the ratio of reported

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crimes to a change in reporting of the numerator crime. For instance, if we observe ten reported robberies for every homicide in year one, and 15 reported robberies for every homicide in year two, we would say that the reporting of robberies increased by 50%. Homicides are sufficiently rare, particularly in recent years, that this method has a difficult time picking up significant effects of police hiring. (Levitt restricted his sample to large cities, presumably for this reason.) We substitute gunfire incidents (as detected by ShotSpotter) for homicide in the denominator of the crime ratios, and find positive and statistically significant effects of police hiring on the reporting of rape, assault, burglary, larceny, and vehicle theft. Using homicide in the denominator picks up only a marginally-significant effect for vehicle theft. While limited to a small sample of cities, we consider this evidence that police hiring continues to have a positive effect on crime reporting in recent years, and a demonstration of these data’s usefulness in analyses where reporting rates are a concern. This paper proceeds as follows: Section 2 discusses traditional data on criminal behavior. Section 3 describes ShotSpotter technology and data availability. Section 4 uses ShotSpotter data from DC and Oakland to estimate the effect of gunfire incidents on reporting. Section 5 uses ShotSpotter data from six cities to test the effects of police hiring on crime reporting. Section 6 discusses and concludes.

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Traditional data on criminal behavior and gun violence

For unbiased analyses of policy effects on crime, we need data that capture all criminal activity, or at least a random subset of all criminal incidents. This does not describe traditional sources of crime data. The best-known datasets on criminal behavior are the Uniform Crime Reports (UCR) and National Incident-Based Reporting System (NIBRS), both maintained by the FBI. The UCR and NIBRS provide information on the number of reported crimes at the reporting-agency level (typically a city or county); NIBRS also includes richer detail on these offenses for the subsample of jurisdictions that choose to participate in the program. These are, technically, administrative data, but they are collected from individual jurisdictions across the country, and those jurisdictions do not always respond accurately or completely. Additionally, and by nature, they miss any criminal activity that is not reported to law enforcement and recorded as a crime. Both the UCR and NIBRS arguably improve upon large-scale surveys such as the National Crime Victimization Survey (NCVS), which asks respondents to recall crimes from previous months that they may or may not have reported to the police. In reality, these data sources are complementary, due to concerns about the selective underreporting of crime. All are, ultimately, imperfect proxies for true criminal activity. An increasing number of academic papers rely instead on detailed administrative data from local agencies. Local administrative data on individuals arrested for or convicted of crimes provide more flexibility in terms

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of the issues researchers can address (for instance, tracking individuals over time to measure recidivism). However, arrests and convictions are, again, imperfect proxies for criminal behavior. For instance, racial disparities in how individuals are perceived and/or treated by law enforcement, victims, and witnesses, could affect the likelihood that they are included in these datasets, conditional on the same underlying behavior. Such sample selection could bias the apparent effects of crime-prevention policies. Data on gun violence are particularly problematic. The ideal data on gun violence would be something along the lines of every incident where a gun threatened someone else’s safety. As a proxy for this, researchers can use administrative data on reported crime that include weapons used (such as NIBRS), but — as noted above — not all gun violence is reported to police. Gun violence research typically focuses on gun homicides to minimize concerns about underreporting, but obviously not all shots fired (or guns wielded as a threat) result in death, and in fact as medical technology improves fewer gunshot injuries will result in fatalities. Many jurisdictions can provide data on 911 calls reporting shots fired. However, gunshots that do not hit anyone are often not reported to police, and this selective underreporting may be particularly problematic in the most violent neighborhoods if residents don’t trust the police to be helpful. The NCVS asks whether respondents were victims of a crime committed with a firearm, but these data are subject to the usual concerns about the validity of survey responses and self-selection of respondents; they also do not include precise times or locations of crime incidents. The Centers for Disease Control and Prevention (CDC) maintains city-level data on fatal injuries (from death certificates) and nonfatal injuries (from hospital emergency rooms), but these will obviously not include information about gun violence that does not result in injury, or individuals who avoid hospitals for fear of being arrested. Research based on any of these traditional data can provide suggestive evidence, at best. This situation is distressing, given the important, often life-and-death nature of questions related to criminal justice policy and violent crime. But there is good news: improvements in technology are changing this status quo. As law enforcement and governments increase their use of surveillance tools, they collect a great deal of objective data on criminal activity. These data have not yet been exploited by social science researchers, but have the potential to transform the field. In this paper, we consider a new source of data, generated by ShotSpotter technology, from several jurisdictions across the United States. These data measure the quantity, timing, and locations of gunfire incidents with greater accuracy than do reported crime or 911 call data. More importantly, the accuracy of the data is unlikely to be affected by most interventions that aim to reduce gun violence. For this reason, using ShotSpotter data as an outcome measure is more likely to produce meaningful, unbiased results in policy evaluations.

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Description of ShotSpotter and evidence on accuracy

ShotSpotter consists of audio sensors implemented throughout a targeted area (on top of buildings and in similar discrete locations), which detect the sound of gunfire and triangulate its location. An algorithm analyzes the recorded sound and determines whether it was gunfire or another loud noise such as construction or fireworks. If it is confirmed to be gunfire, the relevant information (including time, location, and a recording of the incident) is sent to local police so that they can quickly go to the scene. ShotSpotter has been adopted by over eighty jurisdictions across the United States. Not all of these jurisdictions are major cities, though they tend to have higher crime rates than average. The firm releases an annual "National Gunfire Index" summarizing the data its system generates in cities across the United States (ShotSpotter, 2013). However, they do not make the incident-level data publicly available. We have obtained incident-level data directly from several jurisdictions where the data are considered public record, for academic research on how policy interventions affect the incidence and reporting of gun violence. The appeal of ShotSpotter-generated data is that they likely provide a more accurate count of "true" gunfire incidents than data such as reported crime or 911 calls. In addition, they include timestamps and geocodes that are far more precise than those in reported crime and 911 call data. However, ShotSpotter data are not perfect. In all data on gunfire – indeed, in all data on any criminal activity – there are two potential problems: false positives (detected incidents that were not actually gunshots) and false negatives (actual gunshots that were not detected). The technology on which ShotSpotter data are based has improved over time, but there is limited independent, published evidence of its current accuracy. Redwood City conducted a field trial in 1997; it found that ShotSpotter detected "nearly 80 percent of the test shots" and "was able to triangulate (locate) 84 percent of the test shots (N = 26 of 31 shooting events) within a median margin of error of 25 feet" (Mazerolle, Frank, Rogan, and Watkins, 2000). In a 2006 study financed by the National Institute of Justice, ShotSpotter "detected 99.6 percent of 234 gunshots at 23 firing locations", and "located 90.9 percent of the shots within 40 feet" (Goode, 2012), though the report noted that quality of implementation will be key to the sensors’ success (Litch and Orrison, 2011). To address the number of false positives, ShotSpotter funded an independent study of the technology’s use and effectiveness. The researchers interviewed employees at seven police departments that use ShotSpotter. The interviewees were asked what share of ShotSpotter alerts were actual gunfire. Their responses ranged from 50% to 97% (averaging 67%). However, these estimates were based on individuals’ perceptions, not an analysis of actual data. Also, it is important to note that it is typically impossible to distinguish false positives from gunshots that cannot be corroborated by other evidence (e.g., a 911 call or evidence found at the scene). That said, large spikes in detected gunfire incidents on New Year’s Eve and July 4th suggest

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that the algorithm sometimes confuses fireworks and firecrackers with gunfire (though local residents would probably not be able to distinguish between these sounds either, out of context). At this point, there is no reliable evidence about the rate of false positives in actual ShotSpotter data, and this is an area where future research would be helpful. False negatives and false positives in any dataset are a concern for researchers if they are not random. If they are random noise, they introduce measurement error, which could increase the standard errors on empirical estimates (when the data are used as an outcome measure). However, if they are nonrandom – for example, if gunfire in particular areas or by particular people is systematically less likely to be detected – this will introduce selection bias. False negatives and false positives are a greater concern for research on gun violence if they are affected by the policy interventions being studied (Pepper, Petrie, and Sullivan, 2010). The typical concern is that many policies that could reduce gun violence – like increasing policing in dangerous neighborhoods – probably also affect the reporting of gunfire; this makes it difficult to determine the true effect on criminal activity when using reported crime as the outcome measure. The promise of ShotSpotter data is that (1) both measurement error and selection bias should be much lower than when using reported crime data or 911 call data, and (2) the detection of gunfire by ShotSpotter will be unaffected by policy interventions that aim to reduce gun violence.

3.1

Description and availability of ShotSpotter data

ShotSpotter data typically include the following information on each incident: date, time, location (latitude and longitude), and whether the incident consisted of a single gunshot or multiple gunshots. These data on gunfire incidents exist for many cities in the United States, but not all. The cost of the technology limits its coverage: not all cities choose to implement it, and those that do target the most violent neighborhoods. Data are freely-available to researchers for only a small subset of ShotSpotter cities. Most local contracts give ShotSpotter ownership of the data, so the data are not considered public record in most places. (Note that ShotSpotter is open to selling the data to researchers.) We submitted public records requests to all ShotSpotter cities, and obtained data on gunfire incidents from the following: Washington, DC; Oakland, CA; Beloit, WI; Redwood City, CA; Youngstown, OH; Canton, OH; Peoria, IL; and Nassau County, NY. Animated maps of the incidents over time in each jurisdiction are available at http://jenniferdoleac. com/maps/. Their limited availability makes ShotSpotter data most useful for city-specific research questions. They are currently less useful for projects where cross-city comparisons are necessary. However, as coverage

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expands, and as ShotSpotter becomes more open to collaborating with researchers, this could change.

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Estimating the underreporting of gun violence

We use the timing of gunfire incidents in Washington, DC, and Oakland, CA, to test the effect of gunfire on crime reports and 911 calls. This gives us a measure of the extent of underreporting.

4.1

Data

To compare ShotSpotter data with traditional sources of crime data, we focus on Washington, DC, and Oakland, CA – the two largest cities in our sample. We were able to obtain incident-level, timestamped, geo-coded data on ShotSpotter incidents and traditional crime measures (reported crime and/or 911 calls) for the following time periods: January 2011 through June 2013 in DC, and January 2008 through October 2013 (excluding January through July of 2011) for Oakland1 . Because we are interested in whether gunfire incidents are reported, we focus on the categories of reported crimes and 911 calls that are most likely to be associated with such an incident. The reported crimes of interest are homicide and AWDW. The 911 call categories of interest are all calls, calls for police assistance, and calls to report gunfire. We obtained incident-level data on reported crimes and 911 calls from Washington, DC. These data include the date, time, and location of each event, but these are generally less precise than in the ShotSpotter data. The time and date of the reported crime will often be an estimate based on when the crime was discovered and/or when it was reported to police. The time and date of the 911 call is when the call was received at dispatch. In all cases, the location is an address rather than a latitude and longitude. In the case of 911 calls, the address is typically that of the caller, not necessarily where the crime occurred; it is therefore a particularly noisy measure for calls reporting gunshots. Because ShotSpotter covers a relatively large area in Washington, DC, we aggregate to the police district (PD) level2 . Each observation is the number of incidents occurring during a particular hour in a particular PD. We obtained incident-level data on reported crimes (but not 911 calls) from Oakland, CA. The data characteristics are similar to those in DC. We aggregate incidents to the city level, so each observation is the number of incidents occurring during a particular hour, city-wide. As mentioned above, there are large spikes in ShotSpotter-detected incidents on New Year’s Eve and near the July 4th holiday. This is likely due to real increases in celebratory gunfire as well as large numbers of 1 In Oakland, ShotSpotter data are unavailable for January through July of 2011, apparently due to a technical problem with the sensors. We thus exclude those months from the analysis. 2 ShotSpotter has been implemented in PDs 3, 5, 6, and 7, so we restrict our attention to these areas.

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false positives due to fireworks or firecrackers that make it through the algorithm’s filter because they sound so similar to gunshots. To deal with this, we exclude January 1st, the week of July 4th, and December 31st. Summary statistics for DC are in Table 1. Summary statistics for Oakland are in Table 2.

4.2

Empirical Strategy

Our goal is to estimate how gunfire incidents affect the number of 911 calls (total calls, calls for police, and calls to report gunshots), and the number of reported violent crimes (homicides and AWDWs)3 . The intuition is that a gunshot incident is the initial event, and crimes are reported and/or 911 calls made as a result of that incident. Conditional on a variety of time and location fixed effects, the occurrence of a gunfire incident can be thought of as an exogenous shock to the likelihood of a 911 call or reported crime during that hour. The estimated effect of gunfire on reports tells us about the extent of underreporting of gun violence. Descriptively, we see suggestive evidence that underreporting is a problem: In DC, there are 4,483 hours during our sample period with at least one gunshot incident. Only 982 of those hours also had at least one 911 call to report shots fired, and only 453 of the 4,483 hours with gunfire saw at least one AWDW reported. Only 110 of the 4,483 hours with gunfire incidents included both a 911 call to report shots fired and a reported AWDW. To more rigorously test for the effects of gunfire incidents on reporting, we construct a balanced panel of data on the number of ShotSpotter incidents, reported crimes, and 911 calls, by hour, by location (PD or city). We consider the effect of the number of gunfire incidents using the following specification:

Outcomei,h,p = α + β1 Gunshotsh,p + β2 LaggedOutcomei,h,p +

(1)

λLocation + γHourOf Day + δM onthOf Y ear + θY ear + ei,h,p ,

where i is the outcome of interest (type of reported crime or 911 call), h is the hour of the day, and p is the location (PD in DC, or city-wide in Oakland). A number of fixed effects (location, hour of day, month of year, and year) control for omitted variables that might affect both the number of gunfire incidents and reported crime, to better isolate the effect of a specific gunfire incident. The fixed effects also absorb variation in the outcome measure to help us detect gunfire’s effects. The outcomes of interest are: number of homicides, number of AWDWs, number of 911 calls, number of 911 calls for police assistance, and number of 911 calls to report gunfire. (Recall that we have 911 call data for DC only.) Gunshots is the number of gunshot incidents detected by ShotSpotter during the given hour in that location. LaggedOutcome is the number 3 Note

that an incident where someone was shot but not killed, or shot at but not hit, would be considered an AWDW.

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of reports or calls in the same location during the previous hour or during the same hour the previous day (i.e., 24 hours earlier); this controls for the recent level of reported crime or 911 calls in that location (which might not be fully absorbed by the fixed effects). The coefficient of interest is β1 .

4.3

Results

The results of these regressions are presented in Tables 3 and 4. In Washington, DC, there are strong correlations between gunshot incidents and reported crime, and between gunshot incidents and 911 calls. The first column of Table 3 shows the unconditional effects of a gunfire incident on the number of reported crimes and 911 calls. These suggest that in DC there is 1 reported homicide for every 181 gunfire incidents, and 1 AWDW for every 29 gunshot incidents. Turning to 911 calls, there is 1 call for service for every 1.6 gunshot incidents in a given hour, 1 call for police assistance for every 1.8 gunshot incidents, and 1 call to report gunshots for every 7 gunshot incidents detected by ShotSpotter. Columns 2–5 each add an additional set of fixed effects. Controlling for the hour of the day has the biggest effect on the estimated coefficient. Most of the controls have little to no impact, which suggests that the timing of gunshot incidents is indeed random with respect to other factors that might affect crime reports or 911 calls. Columns 6 and 7 add the lagged outcome measure (lagged by 1 hour or 24 hours, respectively), which have little effect on the estimates. The estimates in Column 7 suggest that, after controlling for all of these other factors, the number of gunfire incidents has a statistically-significant effect on all of the outcomes of interest. These estimates imply that 0.5% of gunfire incidents result in a homicide, and 2.3% result in a reported AWDW. Note that while not all gunfire kills someone, most gunfire is probably intended to be threatening (and so constitutes an AWDW). 22.0% of gunfire incidents result in a 911 call, 20.7% result in a 911 call for police assistance, and only 12.4% result in a 911 call to report gunfire. Appendix Table 7 shows Column 7 for each PD separately. The effect of gunfire incidents on homicides ranges from 0.004 to 0.008. The effect of gunfire incidents on AWDW reports ranges from 0.018 to 0.039. The effect of gunfire incidents on 911 calls ranges from near-zero (and statistically insignificant) to 0.267. The effect of gunfire incidents on 911 calls for police ranges from 0.136 to 0.403. The effect of gunfire incidents on 911 calls to report gunshots ranges from 0.093 to 0.180. These estimates imply that underreporting varies from place to place, which could result in selection bias in empirical estimates based on traditional data sources. Table 4 presents results for reported crime in Oakland. Column 1 shows that there is 1 homicide for every 62 gunshot incidents in Oakland, and 1 reported AWDW for every 10 gunshot incidents. Columns 2–4 each add an additional set of fixed effects. As in DC, controlling for hour of the day

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makes the most difference. Columns 5 and 6 add lagged outcome measures (lagged by 1 hour or 24 hours, respectively); these have very small effects on the coefficients. The estimates in Column 6 suggest that the number of gunfire incidents has a statistically-significant effect on the number of homicides and AWDWs. The magnitudes imply that 1.0% of gunfire incidents result in a homicide, and 6.4% of gunfire incidents results in a reported AWDW. These results present strong evidence that gunfire incidents are underreported in these cities. Note that the estimated effects of gunfire on both homicide and AWDWs varies across these jurisdictions. It is interesting that gunfire in Oakland appears to be about twice as deadly as gunfire in DC. Homicide is reported with near-accuracy, so this difference is probably not due to a difference in reporting. There might be differences across cities in terms of the nature of victims’ injuries, or the speed with which they get to a hospital, that could affect the likelihood of surviving.

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Estimating the effect of police hiring on crime reporting

The results above suggest that underreporting of gun violence is a problem. This implies that it’s possible for policy interventions to improve reporting rates. We now turn to a policy lever that has long been assumed to affect crime reporting: police hiring. Levitt (1998) noted that measuring the effect of police hiring on crime is complicated by the fact that police hiring should also affect the reporting of crime. In particular, if additional police result in higher reporting rates, conditional on the same amount of criminal activity, then the estimated effect of police on crime will be biased upward – perhaps even resulting in a positive coefficient that suggests police increase crime. (Alternatively, in a context where "over-policing" degrades the relationship between law enforcement and the community, police hiring could decrease the reporting of crime, leading to downwardly-biased estimates.) He uses homicide, which is expected to be accurately reported, to test the effect of police hiring on reporting rates for other serious crimes. His approach is to estimate the effect of the (logged) number of police officers on the (logged) ratio of other crimes to homicides. In the case of robbery:

Ratio of reported crimes =

(Probability that robbery is reported) ∗ (Number of robberies) (Probability that homicide is reported) ∗ (Number of homicides)

(2)

If we assume that the amounts of robbery and homicide move in fixed proportion (let the ratio of robberies to homicides be a fixed constant, C), and that homicide is reported with probability 1, then any observed

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change in the ratio of reported crimes is due to a change in the reporting of the robbery:

Ratio of reported crimes =

(Probability that robbery is reported) ∗ C 1

(3)

For instance, if we observe that the ratio of reported robberies to homicides is 10 at baseline, and 15 after additional police are hired, we would interpret the increase as evidence that the additional police increased the reporting of robbery by 50%. Based on the above assumptions, that is the only part of the ratio that can change. The limitation of this approach is the relative infrequency of homicides, particularly in recent years. Since homicide is a relatively-rare event, it will be difficult to precisely measure the effect of police on reporting using this method. We need data on criminal activity where there is more variation but where, as for homicide, police hiring will not affect the rate of reporting. ShotSpotter data on gunfire are ideal for this type of analysis. To estimate the effect of police hiring on crime reporting, we first replicate Levitt’s approach using homicide in the denominator, then using gunfire incidents in the denominator.

5.1

Data

We use aggregated monthly data on reported crimes from the UCR, for the years 2000 through 2013. Crime types included are: homicide, forcible rape, aggravated assault, robbery, burglary, larceny, and motor vehicle theft. We use annual data from 2000 through 2013 on the number of police officers employed by each jurisdiction from the Law Enforcement Officers Killed and Assaulted (LEOKA) database. We use the sum of male and female officers as the total number of sworn officers in a jurisdiction. Finally, we use data from all ShotSpotter cities for which we obtained data from 2013 or earlier4 . The periods for which data are available vary by city; together they span the years 2000–20135 . Data are aggregated to the month level. Note that ShotSpotter was implemented in phases in DC, beginning in January 2006 and expanding in March and July of 2008. We will control for the changing composition of reporting Police Districts (PDs) with PD-by-phase indicator variables for DC. In all cases, we calculate logged rates by dividing the measure of interest (crime, gunfire, or police) by the local population, multiplying by 1000, then taking the natural log of the result. 4 We exclude three jurisdictions that sent us data: Peoria, IL, because the time period included only one month in 2013; Canton, OH, because there was no variation in the number of sworn officers during the sample period; and Nassau County, NY, because the data exhibited very odd patterns and we ultimately concluded they are unreliable. 5 Washington, DC: January 2006–June 2013. Oakland, CA: January 2008–October 2013, excluding January through July of 2011. Beloit, WI: April 2009–November 2012. Redwood City, CA: March 2000–May 2014. Youngstown, OH: March 2010–June 2014.

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Summary statistics are presented in Table 5.

5.2

Empirical strategy

We replicate Levitt’s (1998) specifications as closely as possible, though we exclude time-varying city characteristics because we are using data from much shorter time periods. Because our data are from a different set of cities and more recent years, we first replicate Levitt’s analysis using homicide in the denominator. We then conduct the same analysis using ShotSpotter data in the denominator. Our specifications are as follows, using homicide and gunfire, respectively, as our measures of accurately-reported crime:

Ln(Crime/Homicide)i,j,t = α + β1 Ln(Sworn Officers)j, t + λJurisdiction + γY ear + ei,j,t

(4)

Ln(Crime/Gunfire)i,j,t = α + β1 Ln(Sworn Officers)j, t + λJurisdiction + γY ear + ei,j,t

(5)

As Levitt did, we include jurisdiction and year fixed effects. The New Year’s Eve and July 4th holidays are outlier events in the gunfire data: there are probably a large number of false positives due to fireworks, as well as celebratory gunfire (which is not the type of gunfire we’re interested in measuring here). Because the UCR data are aggregated to the month-level, we exclude December, January, June and July from this analysis so that these holidays do not affect our results.

5.3

Results

Results are shown in Table 6. The first panel replicates Levitt (1998), using the logged ratio of reported nonhomicides to homicides. Our sample is quite different from that used in Levitt (1998); he focused on large cities (populations greater than 250,000), during the years 1971–92. It is unsurprising that our estimates differ from his. Overall, we find no clear relationship; the effect of sworn officers on reported vehicle theft is positive and marginally significant, but the other effects are statistically insignificant and inconsistentlysigned. This is undoubtedly due in part to the small sample of five cities; the standard errors in each case are large, and the relatively small number of homicides (especially given the low homicide rate during the 2000s) makes it difficult to pick up any effect of police hiring on the ratios of crimes. Panel two shows the results using gunfire incident data in place of homicides. As for homicide, reporting of gunfire (via ShotSpotter) should not change when more police are hired. However, there is much more variation in gunfire, allowing us to pick up statistically significant effects here. We see positive and statistically significant effects of police hiring on the reporting of crime, for all crime types except homicide (which should not change) and robbery.

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Note that vehicle theft is often assumed to be a type of crime that is accurately reported, because owners have an incentive to report a theft to their insurance company. We find a statistically significant and positive effect of police hiring on the reporting of vehicle theft, using both homicides (p<0.10) and gunfire (p<0.01) as the reference crime. This could indicate that others’ assumption that vehicle thefts are accurately reported is incorrect, or it could indicate that the assumption in this empirical strategy — that the amounts of actual crime move in fixed proportions — is not a good one in this case. If we relax that assumption, the positive coefficients could then suggest that more police result in more vehicle thefts per homicide (or gunfire incident). That would imply that police are better at preventing homicides (and gunfire) than they are at preventing vehicle thefts – that is, the denominator is falling more rapidly than the numerator.

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Discussion

This paper describes a new source of data on gun violence that is unaffected by selective underreporting and therefore might be more useful for researchers than traditional crime data. These data are representative of the highly-scaleable "big data" generated by surveillance technology. We show that underreporting of gun violence is a real concern in two major cities: Washington, DC, and Oakland, CA. In DC, only 12.4% of gunfire incidents result in a 911 call to report shots fired, and only 2.3% of gunfire incidents result in a reported AWDW (the crime that is committed when someone fires a gun in a threatening manner). In Oakland, 6.4% of gunfire incidents result in a reported AWDW, still very low. These results are consistent with a model of violent crime where neither the victim or offender is interested in involving the police (e.g. gang or drug-related violence). We also find evidence that the extent of underreporting varies across areas within cities. In DC, the probability that a gunfire incident results in a 911 call to report shots fired ranges from 9.3% in Police District 3 to 18.0% in Police District 5. Given these low reporting rates, and the variation across communities, it is very likely that policy interventions that might affect crime also affect reporting rates. In other words, there is a lot of room for reporting to increase. Indeed, this is what we find when we replicate and extend Levitt (1998) to test the effect of police hiring on crime reporting. We use ShotSpotter data instead of homicide as the baseline crime where reporting is unaffected by police hiring, and find evidence that – even in this small sample of cities, during a relatively low-crime period – hiring additional police officers results in higher rates of reporting for most categories of serious crime. Given this, it is likely that changes in reporting are biasing many estimated policy effects. The increasing availability of surveillance data should be helpful to crime researchers, as they do not depend on reporting by victims, witnesses, or police. Using such data will lead to a better understanding

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of crime patterns, as well as more accurate empirical estimates. Ultimately, these better data may lead to better policy interventions and less crime.

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References Goode, E. (2012): “Shots Fired, Pinpointed and Argued Over,” New York Times. Levitt, S. D. (1998): “The Relationship Between Crime Reporting and Police: Implications for the Use of Uniform Crime Reports,” Journal of Quantitative Criminology, 14(1). Litch, M., and G. A. Orrison (2011): “Draft Technical Report for SECURES Demonstration in Hampton and Newport News, Virginia,” US DOJ report. Mazerolle, L. G., J. Frank, D. Rogan, and C. Watkins (2000): “Field Evaluation of the ShotSpotter Gunshot Location System: Final Report on the Redwood City Field Trial,” US DOJ report. Pepper, J., C. Petrie, and S. Sullivan (2010): “Measurement Error in Criminal Justice Data,” in Handbook of Quantitative Criminology, ed. by A. Piquero, and D. Weisburd. Springer. ShotSpotter (2013): “National Gunfire 2013-NatGunfireIndex-FINAL.pdf.

Index,”

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Available

at:

http://shotspotter.com/pdf/

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Main tables and figures

Table 1: Crime by Year in Washington, DC

All Days SST-detected incidents Reported homicide Reported AWDW 911 calls 911 calls for police 911 calls reporting gunshots

2011

2012

2013*

5196 105 2179 183955 142675 1712

3920 88 2294 193821 149868 1685

1514 38 1073 141963 110205 1112

Excluding Outlier Days (NYE, week of July 4th) SST-detected incidents 2388 2234 898 Reported homicide 94 81 33 Reported AWDW 2015 2130 991 911 calls 170491 179334 131192 911 calls for police 132025 138704 101637 911 calls reporting gunshots 1522 1520 995 * 2013 data include January through June only

Table 2: Crime by Year in Oakland, CA 2008

2009

2010

2011*

2012

2013**

3260 201 1518

3642 202 1007

2852 192 1208

1062 91 695

3622 218 1497

2738 124 1092

Excluding Outlier Days (NYE, week of July 4th) SST-detected incidents 2984 3110 2266 984 2968 Reported homicide 180 190 182 90 203 Reported AWDW 1388 935 1153 689 1412

2349 113 988

All Days SST-detected incidents Reported homicide Reported AWDW

* 2011 data include August through December only ** 2013 data include January through September only

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Table 3: Effects of gunfire incidents on traditional crime measures in Washington, DC Homicide Gunshots Observations AWDW Gunshots Observations 911 Call Gunshots Observations 911 Call for Police Gunshots

(1)

(2)

(3)

(4)

(5)

(6)

(7)

0.0055∗∗∗ (0.0004) 85056

0.0054∗∗∗ (0.0004)

0.0048∗∗∗ (0.0004)

0.0048∗∗∗ (0.0004)

0.0048∗∗∗ (0.0004)

0.0048∗∗∗ (0.0004)

0.0048∗∗∗ (0.0004)

0.0339∗∗∗ (0.0021) 85056

0.0303∗∗∗ (0.0021)

0.0236∗∗∗ (0.0021)

0.0237∗∗∗ (0.0021)

0.0233∗∗∗ (0.0021)

0.0233∗∗∗ (0.0018)

0.0233∗∗∗ (0.0021)

0.6442∗∗∗ (0.0306) 85056

0.5497∗∗∗ (0.0304)

0.2999∗∗∗ (0.0268)

0.2901∗∗∗ (0.0265)

0.2552∗∗∗ (0.0261)

0.2191∗∗∗ (0.0255)

0.2204∗∗∗ (0.0260)

0.5690∗∗∗ (0.0258) 85056

0.5219∗∗∗ (0.0258)

0.2741∗∗∗ (0.0230)

0.2663∗∗∗ (0.0228)

0.2360∗∗∗ (0.0224)

0.2025∗∗∗ (0.0219)

0.2072∗∗∗ (0.0223)

0.1400∗∗∗ (0.0022)

0.1236∗∗∗ (0.0022)

0.1234∗∗∗ (0.0022)

0.1229∗∗∗ (0.0022)

0.1221∗∗∗ (0.0022)

0.1242∗∗∗ (0.0022)

X

X X

X X X

X X X X

X X X X X

X X X X

Observations 911 Call to Report Gunshots Gunshots 0.1427∗∗∗ (0.0333) Observations 85056 Controls: Police District FE Hour of Day FE Year FE Month of Year FE Lagged Outcome (t - 1 hour) Lagged Outcome (t - 24 hours) ∗ p < .10, ∗∗ p < .05, ∗∗∗ p < .01

X

Table 4: Effects of gunfire incidents on traditional crime measures in Oakland, CA Homicide Gunshots Observations AWDW Gunshots Observations Controls: Hour of Day FE Year FE Month FE Lagged Outcome (t - 1 hour) Lagged Outcome (t - 24 hours) ∗ p < .10, ∗∗ p < .05, ∗∗∗ p < .01

(1)

(2)

(3)

(4)

(5)

(6)

0.0162∗∗∗ (0.0013) 44376

0.0099∗∗∗ (0.0013)

0.0100∗∗∗ (0.0013)

0.0101∗∗∗ (0.0014)

0.0100∗∗∗ (0.0014)

0.0100∗∗∗ (0.0014)

0.1034∗∗∗ (0.0034) 44376

0.0642∗∗∗ (0.0036) 44376

0.0648∗∗∗ (0.0036) 44376

0.0646∗∗∗ (0.0036) 44376

0.0642∗∗∗ (0.0036) 44375

0.0637∗∗∗ (0.0036) 44352

X

X X

X X X

X X X X

X X X X

18

19

Oakland, California

Beloit, Wisconsin

Redwood City, California Year 2009 (2.193) 2010 (1.775) 2011 (1.102) 2007 (4.118) Sworn officers (per 1000 residents) 6.489 (0.260) 1.742 (0.160) 2.000 (0.056) 1.233 (0.065) Homicides (per 1000 residents) 0.019 (0.008) 0.022 (0.010) 0.005 (0.013) 0.002 (0.006) Rape (per 1000 residents) 0.026 (0.010) 0.060 (0.022) 0.024 (0.024) 0.023 (0.017) Aggravated Assault (per 1000 residents) 1.881 (0.259) 2.199 (0.229) 1.124 (0.239) 0.525 (0.221) Robbery (per 1000 residents) 0.519 (0.094) 0.764 (0.198) 0.125 (0.070) 0.082 (0.037) Burglary (per 1000 residents) 0.513 (0.113) 1.047 (0.163) 0.701 (0.309) 0.421 (0.141) Larceny (per 1000 residents) 2.524 (0.402) 2.121 (0.496) 2.245 (0.410) 1.488 (0.436) Motor Vehicle Theft (per 1000 residents) 0.713 (0.243) 1.354 (0.276) 0.136 (0.084) 0.261 (0.132) Gunfire Incidents (per 1000 residents) 0.458 (0.202) 0.599 (0.181) 0.319 (0.223) 0.303 (0.278) Observations 60 43 30 105 Data sources: UCR for crime data. Local police departments for ShotSpotter data on gunfire incidents. LEOKA for data on sworn officers.

Washington, DC

Table 5: Demographic characteristics

2012 (1.121) 2.413 (0.336) 0.025 (0.020) 0.035 (0.021) 3.197 (0.416) 0.261 (0.084) 2.407 (0.475) 2.104 (0.355) 0.465 (0.310) 1.314 (0.629) 31

Youngstown, Ohio

20

Assault/Homicide 1.383 (1.013) 141 Assault/gunshot 2.695∗∗ (1.059) 269

Robbery/Homicide -0.048 (0.980) 141 Robbery/gunshot 1.555 (1.104) 267

Burglary/Homicide -0.408 (0.907) 141 Burglary/gunshot 2.425∗∗ (1.040) 269

ln(Sworn Officers)

Homicide/gunshot 1.449 (1.173) Observations 141 ∗ p < .10, ∗∗ p < .05, ∗∗∗ p < .01 January, June, July, and December excluded. Sample restricted to months when SST data are available. Specifications include ORI and Year fixed effects. SST specifications include indicators of three expansion phases in DC.

Observations

ln(Sworn Officers)

Table 6: Association between Police and Reporting of Crime Rape/Homicide 0.570 (1.488) 134 Rape/gunshot 3.318∗∗ (1.288) 240

Larceny/Homicide 1.082 (0.912) 141 Larceny/gunshot 2.299∗∗ (1.024) 269

Vehicle theft/Homicide 1.765∗ (1.021) 141 Vehicle theft/gunshot 3.523∗∗∗ (1.105) 268

Table 7: Effects of gunfire incidents on traditional crime measures in Washington, DC, by Police District Homicide Gunshots Observations AWDW Gunshots Observations 911 Call Gunshots Observations 911 Call for Police Gunshots

District 3

District 5

District 6

District 7

0.0080∗∗∗ (0.0010) 21264

0.0066∗∗∗ (0.0013) 21264

0.0046∗∗∗ (0.0008) 21264

0.0035∗∗∗ (0.0008) 21264

0.0271∗∗∗ (0.0057) 21264

0.0389∗∗∗ (0.0057) 21264

0.0221∗∗∗ (0.0036) 21264

0.0181∗∗∗ (0.0039) 21264

0.1343 (0.0904) 21264

-0.0014 (0.0071) 21264

0.1326∗∗∗ (0.0402) 21264

0.2683∗∗∗ (0.0415) 21264

0.1458∗ (0.0789) 21264

0.4034∗∗∗ (0.0661) 21264

0.1356∗∗∗ (0.0344) 21264

0.2564∗∗∗ (0.0354) 21264

0.1799∗∗∗ (0.0063) 21264

0.1060∗∗∗ (0.0037) 21264

0.1249∗∗∗ (0.0042) 21264

X X X X X

X X X X X

X X X X X

Observations 911 Call to Report Gunshots Gunshots 0.0933∗∗∗ (0.0052) Observations 21264 Controls: Police District FE X Hour of Day FE X Year FE X Month of Year FE X Lagged Outcome (t - 24 hours) X ∗ p < .10, ∗∗ p < .05, ∗∗∗ p < .01

21

A

For Online Publication

A.1

Appendix: Data construction

Specific geographic descriptors in the ShotSpotter Technologies (SST) data allow us to study the geographic effects of policy on gun crime, but they also create unique challenges. In this data appendix, we seek to describe the data in detail to shed light on potential uses as well as detail some of the more important GIS processes necessary for the most likely uses. There are many GIS software options (some of them free) and online geocoders (again, some of them free) which can be used to process the geographic data. In this appendix, all of the processing will occur in ArcMap. All operations described are available on an "ArcView" level license. Additionally, the data may be available in various forms, and we will suggest resources for dealing with various issues.

A.1.1

Mapping Points

For this study, we aggregate the SST data to geographic divisions and we compare the locations of various points of interest. We use ESRI’s ArcMap GIS software to first map the gunshots. If the data include latitude and longitude, we can use that to add the gunshots to a map document. If they only include street addresses, then the data will have to be geocoded first. In this project, we have used Texas A&M Geoservices online tools6 in order to geocode the data. If the addresses do not include zip codes, this task is a bit more complicated, but many cities have only one or two zip codes. Most geocoding services or programs provide an indication of the match quality of of each geocoded point. More specific matches indicate higher quality (i.e. matching to the exact parcel is better than the zip code) as well as a higher percentage match score. These tools can help determine which matches should be considered reliable, especially in a situation where the zip codes are unknown. ArcMap allows users to input data as comma separated values text files; we input the data including latitude and longitude in this form using the "Add Data" button. Next, we use the "Display XY Data" option (found by right-clicking on the dataset in the Table of Contents window) in order to add the gunshots to the map as point data. In the "Display XY Data" options window that pops up, we specify longitude as the "X field" and latitude as the "Y field." The "Z field" is left as "." Importantly, the linear units for the map must be set to "Degree" either before or during this operation because the program will not recognize that the units should be degrees despite the field names indicating that. If the map document already contains data in a coordinate system for which the unit is degree, then 6 http://geoservices.tamu.edu/

22

nothing further needs to be done. This can be verified by looking at the bottom right corner of the ArcMap window, where the cursor’s current location is given in the units of the map. If the map has another unit, the points will be mapped in an incorrect place. Some cities (with more coordinated GIS offices) may use another coordinate system across the city’s publicly available data. This is the case for Washington, D.C., for example. Instead of listing latitude and longitude, some table-style data are given X and Y coordinates in meters. If any other city data (like a shapefile) has already been added to the map, adding this new data using the process described above is the same, but uses the X and Y coordinates from the city GIS system. This is the best case scenario because using the same coordinate system across the city reduces the likelihood of error.

A.1.2

Joining Points to Administrative Boundaries

Once the gunshot incidents are mapped, we perform a spatial join in order to determine in which geography they lie. Before joining, another shapefile containing the areas (a shapefile of polygons) to which we plan to match is added to the map. Right-clicking the point-type layer of the SST data in the Table of Contents window brings up a number of options, we select "Joins and Relates" and then "Join." We then opt to "Join data from another layer based on spatial location" in the first drop down menu, and then select the polygon shapefile7 to which to match in the second drop down menu. If all of the points fall within a polygon, and the polygons do not overlap, the default join settings should be fine. If there are gunshot points that fall outside of the polygon layer, then they can either be dropped or matched to the nearest polygon. In this analysis, we drop those points because most occur outside of city limits, and inference is clearer without them. The output of the spatial join is a new point layer of gunshot incidents containing additional columns from the polygon to which each point was joined. These columns will typically contain information such as the area of the polygon, as well as an unique identifier or "name" and whatever additional variables were in the initial polygon dataset. The resulting joined dataset can be output into a text file for use in a variety of statistical software packages.

7 for

example, D.C.’s PSA shapefile is available at http://data.dc.gov/.

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