1 Introduction

“Toxic stress results from intense adverse experiences that may be sustained over a long period of time-weeks, months, or even years” (Middlebrooks and Audage 2008: 4). School shootings are, arguably, “intense adverse experiences” and the stress they create may have long-lasting effects; stress during early adulthood has been shown to negatively affect health later in life (Grossman et al. 2018). In the United States, school shootings occur regularly, albeit plausibly randomly across the country. The Washington Post reports that 228,000 students (as of May 8, 2019) have lived through a school shooting since the 1999 shooting at Columbine High School (Cox et al. 2019). However, the effects are likely to extend beyond those directly affected. “Much of the cost is not directly linked to actual victims; it is the anticipation of victimization that engenders widespread anxiety, disinvestment in impacted communities, and costly efforts to avoid and mitigate attacks[;]... shootings in schools... are far more important than they appear in victimization statistics” (Cook 2020: 1372). School shootings are known to generate public fear (Muschert 2007). Orcutt et al. (2014; 3) conclude that “although higher levels of exposure are associated with greater distress, the extant research suggests that even low-level exposure results in widespread significant distress after a shooting.” Low-level exposure is even experienced by children in nearby schools, likely throughout the school district of a directly affected school. For example, in the year following the Marjory Stoneman Douglas High School shooting in Parkland, Florida, incidents of drug use or possession, physical attacks, and other offenses increased within the entire school district (Gaudiano 2019).

The literature on school shootings research has examined the proximate effects of these events on the educational and mental health outcomes of exposed students (Beland and Kim 2016; Rossin-Slater et al. 2020; Levine and McKnight 2021). While the literature is clear that exposed students experience negative outcomes immediately following school shootings, there is less research on how exposure to school shootings affects these students later in life as adults, with work by Cabral et al. (2020) focusing on the educational and employment outcomes of exposed students in their early twenties.

In this article, we examine the effect of school shootings on risky behavior, health, and human capital outcomes of exposed middle and high school students as adults in their twenties and early thirties within the contiguous United States. We also study the effect of school shootings on the out-migration of children and young adults from affected counties.

Our analysis relies on data from three sources, the K-12 School Shootings Database (K12SSD), the Behavioral Risk Factor Surveillance System (BRFSS), and the American Community Survey (ACS) (Riedman and O’Neill 2019; Centers for Disease Control and Prevention 2019; Ruggles et al. 2022). We use the school shooting incidents data from the K12SSD to identify school shootings that occurred in middle and high schools. We link these data with BRFSS surveys, which are our source for health, human capital, and demographic characteristics at the individual level. We use a comprehensive set of BRFSS measures to study the medium-term effects of school shootings on plausibly exposed students 6–18 years ex-post. However, the BRFSS provides no variables that can be used to measure in- or out-migration. If families with children affected by school shootings (or the children themselves as young adults), subsequently moved out of the affected counties then, assuming negative causal effects of exposure, our estimated effects would be biased toward zero. If these individuals instead got “locked” into the affected counties then the estimated effects would be biased away from zero. Therefore, we conduct an analysis of out-migration using the ACS.

We find substantial evidence of declines in health and well-being, increases in risky health behaviors and worse education and labor market outcomes among young adults who were exposed to school shootings while in middle or high school. The effects are stronger among individuals for whom 6–12 years have elapsed since the school shooting. Overall, our analyses provide new evidence that school shootings have persistent negative effects on the health, health-related behaviors, and human capital outcomes of exposed students as adults. The negative consequences of school shootings have the capacity to linger for over a decade among the exposed, highlighting the hidden health and human capital costs that potentially compound with each additional school shooting. Back-of-the-envelope calculations conservatively suggest that school shooting exposure depresses the health and human capital outcomes of 1103 women and 912 men annually. Out-migration is unaffected in counties after school shootings occur.

The results remain qualitatively unchanged when we consider plausible, alternative definitions of exposure and intensity of incidents. The results are robust to alternative definitions of exposure, the composition of counties in our analysis, the time period of data we chose to study, and the possibly confounding effects of overall violent crime and unemployment. Placebo and randomization analyses suggest that our regression specifications do not suffer from unobserved confounding. We cannot identify, in the data, whether a school-age individual in a county actually attended the school in which a shooting occurred. This measurement error likely means that our estimates are lower bounds of the true effects of school shootings.

2 Background

Much of the previous work on the effect of school shootings on exposed students has focused on how these events affect the students’ short-term academic performance and mental health. It has been shown that exposure to school shootings adversely affects students along both of these dimensions. Students exposed to school shootings have scored lower on standardized math and English exams, have increased absences and higher rates of chronic absenteeism, and are more likely to repeat a grade relative to their unexposed peers (Beland and Kim 2016; Cabral et al. 2020; Levine and McKnight 2021). Exposure to school shootings also leads to increases in suicides and accidental deaths among exposed students, with male students being more negatively affected than female students (Levine and McKnight 2021). Additionally, following fatal school shootings, youth antidepressant use increases (Rossin-Slater et al. 2020)

Taking a longer time horizon, research that examines the effects of exposure to school shootings and other shootings involving children also finds persistent adverse effects. Students exposed to school shootings are less likely to graduate high school, enroll in and complete college, and have depressed earnings and labor force participation in their early twenties (Cabral et al. 2020). The results are similar when examining the effects of a mass shooting at a youth camp in Norway (Bharadwaj et al. 2021).

Exposure to gun violence also negatively affects economic outcomes in the areas in which they occur (Yousaf 2022). Such exposure reduces employment, earnings, and housing prices at the county level (Brodeur and Yousaf 2019). It results in decreases in community well-being and emotional health, with greater reductions among parents with children under the age of 18 (Soni and Tekin 2020). The negative effects of an adverse event on health are pronounced in children. In-utero exposure to mass shootings increases the occurrence of very low birth weight and very premature births (Dursun 2019). Additionally, childhood adversity, such as mental or physical abuse, or witnessing the abuse of a caregiver, begins to affect health outcomes by early adolescence (Flaherty et al. 2013). Similarly, violence can also be attributed to an “underlying risk profile” in children that may result in the early onset of chronic health conditions in adulthood (Taylor 2010: 1).

We contribute to the literature on the effect of shooting-related violence on the public more broadly, similar to work done by Bor et al. (2018) and Ang (2021), to the literature on school shootings, and to the literature on migration after adverse events. Our research extends the proximate effects findings of Beland and Kim (2016); Rossin-Slater et al. (2020) and Levine and McKnight (2021), and is complementary to work on the medium-term effects of school shootings (Cabral et al. 2020) and to work on the effects of mass shooting events involving children (Bharadwaj et al. 2021).

3 Data

To conduct our analyses, we utilize three publicly available data sources: the K-12 School Shootings Database (K12SSD), the Behavioral Risk Factor Surveillance System (BRFSS), and the American Community Survey (ACS). Using the BRFSS and the K12SSD, we examine the effect school shootings have on the risky behavior, health, and human capital outcomes of exposed students in adulthood. To conduct our analyses on the effect of school shootings on out-migration in exposed localities, we use the ACS and K12SSD.

3.1 K-12 school shootings database (K12SSD)

We use the K-12 School Shooting Database (K12SSD) to identify school shooting incidents (Riedman and O’Neill 2020). This dataset, created by the Naval Postgraduate School’s Center for Homeland Defense and Security, is intended to document “[each and every instance] a gun is brandished, is fired, or a bullet hits school property for any reason, regardless of the number of victims (including zero), time, day of the week, or reason [e.g. planned attack, accidental, domestic violence, gang-related, officer-involved shooting]” (Riedman and O’Neill 2020; 1). The database includes shootings that range from incidents with no casualties (injuries or deaths) to mass shootings with large numbers of casualties. It documents over 1400 shootings from 1970 to mid-2019 when we retrieved the database.

Our analysis is limited to school shootings in the contiguous United States (the 48 adjoining U.S. states plus the District of Columbia). We only consider incidents when the location is known to be “inside the school building” or “outside on school property.” We do not consider shootings where the type of school is “unknown,” “other” or if the school is an elementary school. Elementary school shootings were rare during this period and have only recently become more prevalent capturing public attention. In most analyses, we eliminate shooting incidents in which there were no casualties (injured or killed victims). Following arguments by Levine and McKnight (2020), who demonstrate that different school shooting types affect different student populations, we estimate models using data on exposure limited to shootings that occurred only during school hours and also shootings that resulted in at least one death. We also expand the definition of exposure to include shooting incidents with no casualties.

School shooting incidents from 1994 through 2005 are used in our analysis of risky behavior, health, and human capital outcomes in conjunction with linked BRFSS data. The K12SSD documents 237 incidents with one or more casualties. Of these, 19 counties have 2 incidents in the same year and 3 counties have 5 incidents in the same year. When more than one incident occurs in the same school in a year, we sum up the number of casualties and treat those incidents as one incident. Figure 1 shows the time series properties of school shootings. The number of incidents per year has a U-shape, rising at both ends of the analysis period. In some years, both incidents and casualties are high, but in other years casualties are high even when the number of incidents is low. Figure 2 shows the geographic dispersion of these school shootings. No region of the country is spared such incidents; 103 counties experienced 1 shooting incident, 24 counties experienced 2–3 incidents, and 13 counties experienced 4 or more incidents.

Fig. 1
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Numbers of school shooting incidents and associated casualties over time. Note: Includes school shootings from 1994 to 2005

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Fig. 2
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Counties in which school shooting incidents occurred. Note: Includes school shootings from 1994 to 2005

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We use data on school shootings from 1996 to 2018 for the migration analysis using the ACS. The characteristics of shootings over time and space are qualitatively similar to those described above.

3.2 The Behavioral Risk Factor Surveillance System (BRFSS)

The 2003–2012 Behavioral Risk Factor Surveillance System (BRFSS) surveys allow us to measure health, health-related behaviors, human capital, and labor market outcomes of individuals 23–32 years old. The BRFSS is a nationwide telephone survey that collects data about US residents’ self-perceived health status, health-related behaviors, and chronic health conditions. It also includes measures of education, labor market status, and income. Sponsored by the Centers for Disease Control and Prevention (CDC) and supported by a number of federal and state government agencies, the BRFSS currently collects data in all 50 states, the District of Columbia, and three US territories (Centers for Disease Control and Prevention 2019). The BRFSS stopped providing county identifiers after 2012, limiting our analysis to end in that survey year.

We link these data with the K12SSD using the county and year of school shooting incidents as identifiers. We restrict incidents to those that occur inside the school building or outside on school property. One county with a school shooting incident is not identifiable in the BRFSS data. In addition, 757 counties without shootings are not identifiable in the BRFSS data. Unidentified counties tend to be smaller counties or counties with few BRFSS respondents. In the BRFSS, through 2005, the county code is set to missing if there were less than 50 respondents for a county or if the population of the county was less than 10,000 adults, (D. Flegel personal communication, February 3, 2021). Taking these features into account, our primary sample has data on individuals living in 1402 counties in the contiguous US. Figure 2 shows their locations.

3.3 American Community Survey (ACS)

Data from the 2004 to 2018 years of the American Community Survey (ACS) are used to analyze the effects of school shootings on migration. We retrieved these data from IPUMS USA (Ruggles et al. 2022). Public Use Microdata Area (PUMA) is the primary geographic identifier in the publicly available ACS (United States Census Bureau 2022). When the respondent lives in a county with a sufficiently, large population, the county is also identified. Each year, the ACS asks respondents whether they moved homes in the previous year. Therefore, we replace the value of the year used in our analysis with the year prior to the survey year. If the respondent did not move, then the location of that respondent in the previous year is the same as that in the survey year. If the respondent did move, the ACS records the respondent’s geographic location prior to the move. We use that location associated with the year prior to the survey year in our analysis. Overall, 3,669 PUMAs are identified in our sample. About 60% of the ACS sample respondents live in one of the 472 identifiable counties. We merge these data with the K12SSD using the county and year and also by PUMA and year.

3.4 Exposure

A BRFSS respondent is defined as being exposed to a school shooting incident if that respondent lives in a county where a school shooting occurred and if they were between 11 and 17 years old in the year of the shooting. Individuals in our sample who lived in counties with a school shooting but who were either younger than 11 years old or older than 17 years old in the year of the shooting are defined as being unexposed. In addition, all other 23–32-year-old BRFSS respondents who lived in counties without school shootings are defined as unexposed. Consider a shooting incident that occurred in 1998 in a particular county. Respondents of the 2012 BRFSS survey who were 25–31 years old and who lived in the county of the incident are defined as exposed. Respondents in the 2012 BRFSS who lived in the same county but were 23–24 or 32 years old would be defined as not exposed; they are contemporaneous event-time, treated-geography controls. Appendix Figure A1 represents this information visually. In addition, 2012 BRFSS, 25–31-year-old respondents who lived in counties that did not experience the shooting would be contemporaneous age and event-time controls. Those who were 23–24 or 32 years old in counties without the event would also serve as controls, plausibly accounting for confounding due to age. Note that, as we specify formally below, our regression specifications will include age, survey year, and county fixed effects so that the effects are identified by within age-year-county variation. In other words, each treated observation is compared to a contemporaneous older cohort in the same county and shooting year, and to the same and older cohorts in counties that did not experience a shooting in that year.

Appendix Figure A1 also shows ranges of possibly exposed ages for shootings that occurred in 1994, the earliest shooting year, 1998, an intermediate year, and 2005, the latest shooting year. Note that the latest shooting year only contributes possibly exposed individuals in the 2011 and 2012 BRFSS. The earliest shooting year, 1994, contributes possibly exposed individuals in 2003–2012. A shooting in 1994 results in plausibly exposed 23–26-year-olds in the 2003 BRFSS, and plausibly exposed 29–32-year-olds in the 2012 BRFSS. Also, note that we treat 18-year-old individuals as unexposed because we cannot be sure of their schooling status.

In our primary analysis using the BRFSS, we define the treatment variable as taking the value of zero if the individual was not exposed to a school shooting inside the school building or outside on school property and as taking the value equal to the number of casualties (injured or killed) in the shooting incident inside the school building or outside on school property that the individual was exposed to. Table 1 shows that 8.2% of our sample was exposed to a school shooting. The median number of casualties among the exposed is 1, the mean is 2.3, and the 95th percentile value is 5. In analyses to determine whether effects might be heterogeneous across definitions of shootings, exposure, and intensity, we define the treatment variable using incidents that occurred only during school days and separately using only those incidents that resulted in at least one death and measuring intensity using only counts of deaths. We also expand the definition of exposure to include shooting incidents with no casualties and use a more narrow definition to include only mass shootings, i.e., shootings that resulted in 3 or more casualties.

Table 1 Characteristics of casualties and duration in primary sample and strata of duration since exposure
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In the analysis of migration using the ACS, we conducted one analysis using individuals between 12 and 18 years old for whom exposure could have occurred 1–4 years ago. We conduct another analysis using individuals 19–23 years old for whom exposure could have occurred 2–8 years ago. We estimate regressions using counties as the geographic unit for a subsample of the ACS observations as well as regressions using PUMAs as the geographic unit. Table 4 shows the average intensity among those exposed — about 2 for each of the samples considered regardless of whether counties or PUMAs are used as the geographic unit.

Table 2 Means of covariates in primary samples of women and men in analysis of risky behavior, health, and human capital
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Table 3 Means of risky behavior, health, and human capital in primary samples of women and men
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Table 4 Means of covariates and migration outcome in the analysis of migration
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3.5 Covariates

Our primary BRFSS sample consists of 197,426 women and 122,519 men between 23 and 32 years old (see Table 1). We conduct our analysis separately for men and women as previous research has shown that exposure to school shootings results in heterogeneous effects by sex (Levine and McKnight 2021). The median age in the primary sample is 28.

Given our choice of ages of BRFSS respondents, the ages at which they were at risk of exposure, 6 to 18 years would have elapsed since the shooting up to the year of the survey. In the primary sample, among those exposed, the median time elapsed from shooting is 12 years. In order to differentiate between individuals who may have shorter time elapsed from the date of the shooting as compared to those with longer elapsed times, we also estimate the models after restricting our sample to those exposed 6–12 years ago, and those exposed between 13 and 18 years ago. In the shorter elapsed time sample, the median time elapsed since shooting in this sample is 10 years; the median age is 28 years. In the longer elapsed time sample, the median cohort time elapsed is 15 years and the median age is 29 years.

Among respondents not exposed to school shootings, 12% of women and 7% of men identify as Black (see Table 2). In contrast, among those exposed to a school shooting, about 24% of women and 15% of men identify as Black. Table 2 also shows that women and men in other minority groups are also overrepresented in the exposed group relative to the unexposed.

Table 4 presents summary statistics for the ACS samples of men and women. As with the BRFSS sample, the rates of minority women and men exposed to school shootings are higher than those rates among the unexposed.

3.6 Outcomes

We examine the effects of exposure to school shootings on measures of risky behavior, health, and human capital outcomes. Table 3 lists all the measures and presents summary statistics.

We examine cigarette smoking, alcohol consumption, and physical exercise as measures of risky behaviors. We measure cigarette smoking using a binary indicator ever smoked for whether a person smoked at least 100 cigarettes in their lifetime. Current smoking status among those who had ever smoked is examined using a multinomial variable that takes 3 values: quit, smokes daily, and smokes occasionally. We use counts of the number of drinking days, the maximum number of drinks on one occasion, and the number of days \(\ge \) 5 drinks to measure alcohol consumption. We use a binary indicator for no physical exercise.

Self-reported health and mental health status are our health measures. Self-reported health status is measured as a multinomial variable defined by excellent or very good health, good health, and fair or poor health. Mental health is measured as a count of the number of not good mental health days.

Education status is measured as a multinomial variable with levels: high school graduate, not a high school graduate, attended technical school or college, and graduated technical school or college. Income is measured in 8 intervals with lower limits set at $0, $10,000, $15,000, $20,000, $25,000, $35,000, $50,000, and $75,000. For employment status, we use a binary indicator for working in contrast to not working for the sample of men. However, in the preliminary analysis of the sample of women, we observed differences between women who were not employed because they were homemakers and women who reported other reasons for not working. Therefore, we chose to model employment status for the sample of women using a multinomial variable with three categories: employed, homemaker, and not working.

We measure migration in two ways using the ACS. First, we limit the samples to those who lived in a county identified by its FIPS code in the year prior to the survey. We define a person as having moved if that person lived in a different county in the year of the survey as compared to the county in the year prior to the survey. We allow for moves to counties that are not specifically identified, e.g., most rural counties. The sample restriction only applies to the identity of the county prior to the move. Second, we define a person as having moved if that person moved between PUMAs from the year prior to the survey year. We use the identity of the PUMA in the year prior to the survey for merging with the school shootings database, but not to determine the move; the ACS has a variable that identifies all moves.

The rates of cross-county moves in the samples are restricted to those respondents for whom the origin county is known and the rates of cross-PUMA moves are very similar in areas that are unexposed to school shootings (Table 4). For 12–18-year-olds the rate is about 8%; for 19–23-year-olds the rate is about 13%. Among areas that are exposed, the rates of cross-county moves are similar to those in unexposed areas. But the rates of cross-PUMA moves are substantially lower than the other rates. The migration regressions confirm our initial conjecture that these differences are due to the types of PUMAs where school shootings occur rather than being the effect of the incidents themselves. Our concerns about migration are further mitigated by the findings in Cabral et al. (2020), where using more granular data, the authors find no evidence of students switching schools, or leaving the public school system after a school shooting.

4 Econometric specification

4.1 Model

Denote individuals by \(i = 1,2,..., N\), counties in the US by \(j = 1,2,..., J\) and years of the survey in the study by \(t = 1,2,..., T\). Denote the number of casualties due to exposure to a school shooting for individual i in county j at time t by \(c_{ijt}\). Let \(a = 24,25,...,32\) denote the age (in years) of the respondent and \(\varvec{x}_{ijt}\) denote the vector of individual level covariates which comprise of race indicators in this study. Let \(d_{ict}\) denote the duration from the school shooting to the year of the survey for an exposed individual. Duration is set to zero for unexposed individuals.

For each outcome, we estimate a regression model with the following functional form:

$$\begin{aligned} \textrm{E}(y_{ijt}) = f(c_{ijt} \beta _c + \varvec{x}_{ijt} \varvec{\beta }_{\varvec{x}} + \beta _{d} d_{ijt} + \alpha _a + \nu _j + \omega _t) \end{aligned}$$
(1)

where \(\alpha _a\) denotes age fixed effects, \(\nu _j\) denotes county fixed effects and \(\omega _t\) denotes year fixed effects. Note that we enter duration as a linear, continuous variable to avoid the identification issues introduced if indicators for age and year and duration are all entered together (Mason and Fienberg 1985; Heckman and Robb 1985). Also, note that this equation makes clear that estimates of \(\beta _c\) (and other coefficients) are identified by within age-year-county variation.

In the cases where the outcome, \(y_{ijt}\) is binary, we estimate a logistic regression with Eq. 1 guiding the specification. In the cases where the outcome is multinomial, we estimate a multinomial logit regression. When the outcome is measured as a count variable, we estimate Poisson regressions specified according to Eq. 1. Finally, for income, which is reported as an interval measure in the BRFSS, we estimate an interval regression. Because income is substantially skewed, while the distribution of the log of income is roughly symmetric, our interval regression is based on the logarithm of income instead.

For each regression, we report exponentiated coefficients on exposure, \(\exp (\beta _c)\). These have the virtue of being interpretable as percentage changes in the outcome across all measure types. Standard errors of these coefficients are cluster-robust at the state level to account for the unobserved ways states differ vis-a-vis gun laws and school policies. We report p-values of the null hypothesis that the exponentiated coefficient equals 1 along with 95% confidence intervals in the figures and tables described below.

The current literature suggests that school shootings affect boys and girls differently (Levine and McKnight 2021). McClellan and Tekin (2017) show that shootings related to Stand Your Ground laws affect men disproportionately. Policy surrounding gun ownership and control such as extreme risk protection orders or red flag laws are invoked differentially by gender (Zeoli et al. 2022). Therefore, for substantive understanding and potential policy reasons, after showing a set of results for both genders pooled, we estimate models for men and women separately.

4.2 Heterogeneity of effects

We expect the effects of school shootings to be heterogeneous across a number of dimensions. First, we expect effects to be larger among more recently exposed individuals. Therefore, in one set of regressions, we keep only individuals exposed 6–12 years ago and, in another, we keep only individuals exposed 13–18 years ago. In both, the sample of unexposed individuals remains the same. Second, counties in which school shootings are “commonplace” occurrences might be quite different than those in which school shootings are more infrequent, leading to substantively different effects across these county types. To evaluate this, we eliminate counties that had more than 4 shootings during the sample period. Third, while most counties have a small number of schools, some have many schools and the effects may be diluted in such counties. As a counterargument to this possibility, note that Gaudiano (2019) reports that effects of school shootings do spread through entire school districts which are often geographically aligned with counties. We conduct an analysis after dropping counties with more than 20 schools (about 12% of all counties) to focus on a priori more proximate impacts.

As described above, our primary analysis defines intensity of exposure as the number of injured or killed persons in an incident that occurred inside the school building or outside on school property. Not all shootings are the same. The accuracy of measurement might vary by the nature of the incident. Students and others might be affected in different ways (Levine and McKnight 2020). Because it is plausible that deaths lead to more intense responses among the exposed, we conduct an analysis using only those incidents that resulted in deaths with the measure of intensity being the number of deaths. Second, we limit exposure to incidents that occurred only during regular school days as those events are arguably more salient. On the other hand, we cannot rule out the possibility that all shooting events are salient, even those with no casualties. Therefore, we conducted an analysis in which we included additional shooting incidents in which there were no casualties. Finally, mass shootings may have the biggest effects on those who were exposed. Therefore, in a final analysis of heterogeneous effects, we limit incidents to those defined as mass shootings only, i.e., those with three or more casualties.

4.3 Specification checks

In our specification checks, we conduct two analyses that change the period of shooting incidents used in the analysis to ensure that there is nothing idiosyncratic about our choice of years. Relative to the main sample period of 1994–2005, first, we expand the shooting incidents period to be from 1993 to 2006. Second, we contract the period to be from 1995 to 2004. We then address a concern arising from the fact that individuals who were exposed to shootings are, on average, younger and more likely to be of minority race and/or Hispanic ethnicity. To counter this, we balance the exposed and unexposed samples on these characteristics, by calculating sampling weights for the unexposed sample using an entropy balancing technique developed by Hainmueller (2012). We estimate effects using entropy-balance weights as sampling weights in the regressions. Entropy balance combined with regression is doubly robust (Zhao and Percival 2017).

Although our regressions always have a contemporaneous, within-county control group, there may be a concern that local time-varying socioeconomic conditions might confound the treatment effects. Therefore, we estimate regression specifications that control for county unemployment and crime rates. Data on annual county unemployment rates were obtained from the Bureau of Labor Statistics (2021). We use the annual county-level homicide rates as a proxy for overall crime (Kaplan 2021). Finally, we estimate regressions after excluding high-migration counties. Data on net migration was obtained from the University of Wisconsin-Madison’s Center for Demography and Ecology (Voss et al. 2004). We calculated net migration rates of counties over the 1990–2000 decade for 20–35-year-old individuals (in the year 2000). By eliminating counties that were in the top 5th percentile of net in-migration and those in the top 5th percentile of net out-migration (a total of 134 counties), we restrict the sample to individuals who were more likely to have lived in the same county throughout.

Two of the specification checks described above involve including additional control variables on the right-hand side of the regression, implicitly arguing that our results are robust if their inclusion does not significantly affect coefficients of interest. But Pei et al. (2019) show that such insignificance may be due to the fact that these variables are poor measures of the underlying confounders. They recommend using these variables as outcomes in the regression specifications as more powerful tests of the identifying assumption. We follow their guidance as additional checks of specification.

It is important to recognize that the empirical design is not a standard event study or staggered difference-in-difference design for two reasons. First, each county in which a shooting incident may or may not occur always has a contemporaneous never-treated group. Second, because exposure is limited to individuals who would have been in high school at the time of the incident, the treatment assignment of a county is not an absorbing state. Nevertheless, the findings in Callaway and Sant’Anna (2021); Goodman-Bacon (2021); de Chaisemartin and D’Haultfoeuille (2020) and Sun and Abraham (2021) raise potential concerns of the interpretability of our estimates because of the staggered nature of the shooting events over time. The results of those studies suggest that any bias is a priori expected to be negligible in our situation because of the existence of a large number of never-treated units (only 8.2% of observations in BRFSS are exposed). Nevertheless, we use the approach derived in Wooldridge (2021) (extended to the repeated cross-section context) to estimate two sets of heterogeneous effects models. In the first specification, we allow the effects to be distinct at each calendar year of the survey. Such heterogeneity might arise, for example, from different local area circumstances over the period of study. In the second specification, we allow the effects to be distinct depending on whether the shootings occurred in the 1990s or in the 2000s. Because of the rarity of shooting events, we are unable to disaggregate shootings further without creating collinearities. We report population-weighted averages of the effects to compare with our primary specification.

We also estimate two sets of regressions in which assignments to treatment are placebos. In the first set of placebo regressions, a BRFSS respondent is defined as being exposed to a school shooting incident if that respondent lived in a county where a school shooting occurred and if they were between 4 and 10 years old in the year of the shooting. These individuals are 7 years younger than the actual treated individuals. For this specification, the sample includes 20–29-year-old individuals, who are 3 years younger than those chosen for the primary sample. Ideally, we would have preferred to lower the ages of sampled individuals by 7 years to be consistent with the placebo-treated individuals. Unfortunately, using 18 and 19-year-olds in the sample would likely contaminate the placebo assignment with actual exposure. In the second set of placebo regressions, respondents who lived in counties where a shooting occurred when they were between 20 and 26 years old were defined as being exposed, 9 years older than the actual treated individuals. In keeping with the spirit of the cohorts for the first set of placebo regressions, for this specification, the sample includes 28–37-year-old individuals who are 5 years older than those in the primary sample. We should note that these are not strictly placebo regressions because we cannot rule out possible exposure among these older and younger individuals. For example, some of these individuals may have been siblings of exposed middle and high schoolers. Others may attend schools that were geographically contiguous or close to the schools in which shootings occurred.

Finally, we conduct specification checks by randomly assigning the school shooting incidents (date and intensity) to counties among those that experienced no school shootings and estimating treatment effects using that sample. Because these shootings are randomly assigned to control counties, they can be interpreted as placebo treatments so the estimated coefficients should be close to zero. We conducted this analysis 20 times, assigning shooting incidents to randomly chosen unaffected counties each time. We report the central tendencies of the distributions of these estimates and conduct nonparametric inference on the null hypothesis that the median of the distributions is zero (Snedecor and Cochran 1989).

We also consider a set of specification checks for the migration regressions using the ACS. In the primary specification, a respondent is exposed to a shooting incident only if it occurred at least 1 year prior to the potential move year, and up to 4 years prior. But that means if a respondent moved “immediately” in response to a school shooting, that exposure would not be recorded as such. So, in a specification check, we define exposure using incidents from the year of a potential move as contributing to exposure. This check introduces the possibility of a different measurement error – that moves prior to the shooting incident in the year of the incident would be recorded as exposure when it should not.

5 Results

5.1 Risky behavior, health, and human capital

For the primary sample of data from the BRFSS, Table 5 displays effects reported as exponentiated coefficients with p-values and 95% confidence intervals associated with the effect of being exposed to a shooting incident for each outcome described above. While exposure does not significantly affect the likelihood of having ever smoked, it does significantly increase the likelihood of smoking daily by about 1%, among those who smoked at some point during their lives to date. We find that exposure to school shootings also affects drinking behavior. The number of drinking days and the maximum number of drinks consumed on one occasion significantly increased by about 0.5%. The number of drinking days where 5 or more drinks are consumed increases by 1.3%. Exposed individuals are significantly less likely to engage in physical exercise and report worse health status. Exposure to an additional shooting casualty increases the likelihood of having attended but not graduated from college or attended a technical school. Relative to the unexposed, exposed individuals have 0.5% lower incomes and are 1% more likely to be not working.

Table 5 Effects of exposure to school shootings on risky behavior, health, and human capital
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Fig. 3
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Effects of exposure to school shootings on risky behavior, health, and human capital among women. Note: The primary sample consists of individuals living in 1402 counties from 2003 to 2012 BRFSS. Covariates include indicators for age, race and ethnicity, county and year, and duration. Exponentiated coefficients along with cluster-adjusted p-values for statistical significance and associated 95% confidence intervals are reported. Confidence limits are bottom and top coded in [0.95,1.05] to enhance readability

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Next, we report results separately for the samples of women and men. For our primary sample of women using data from the BRFSS, Fig. 3 displays effects reported as exponentiated coefficients with 95% confidence intervals associated with the effect of being exposed to a shooting incident on each of the outcomes described above. We find that exposure to school shooting affects drinking behavior. Among exposed women the number of drinking days increases (p-value 0.158); this outcome is not statistically significant. However, there is statistically significant evidence that an additional shooting casualty increases the maximum number of drinks an affected woman drinks on one occasion by 0.5% and increases the number of drinking days where five or more drinks are consumed by 1.8%. On average, an unexposed woman drinks a maximum of 3.3 drinks on one occasion. Our estimates imply that exposure to a school shooting casualty would result in the consumption of an additional 0.02 drinks. Among unexposed women, the mean number of drinking days where five or more drinks are consumed is 0.9 days; exposure to a casualty would increase this behavior by 0.02 days. Given that our measures of drinking behavior are self-reported we view these estimates as conservative lower bounds of the effect of school shootings on the drinking behavior of exposed women.

We also find that school shootings affect educational attainment, income, and labor force participation among women. Relative to being a high school graduate, exposure to an additional shooting casualty increases the likelihood of not being a high school graduate by 1.1%. To contextualize our findings, we use the average county population of 12–17-year-old girls (4085) in 2012 obtained from the Surveillance, Epidemiology, and End Results (SEER) Program Populations (1969–2020) estimates (National Cancer Institute DCCPS 2021). Assuming the 12–17-year-olds were previously unexposed to a shooting casualty, and then became exposed, our results imply that the marginal effect of exposure to a casualty would result in an additional 7 women not graduating high school in the county. Additionally, exposure to a school shooting casualty increases the likelihood of attending college or technical school, but not graduating, by 0.7%, implying that, per casualty, 9 additional women would attend, but not complete college or technical school in the county. However, the likelihood of graduating college is not significantly affected by exposure to school shootings. Exposure to a school shooting casualty also reduces women’s income by 0.5% relative to unexposed women. As described above, we also examine female labor force participation using a multinomial variable with three categories. We find that, relative to the likelihood of being employed, exposure to a school shooting casualty increases the likelihood of being unemployed by 2.2% and the likelihood of being a homemaker by 1.2%. These estimates imply that exposure to a casualty would result in 24 women not engaging in the formal labor force with 15 unemployed and 9 engaged in home management.

In our sample of women, we find that exposure to school shootings has no effects on smoking, both as measured by the likelihood of ever having smoked cigarettes and on the likelihood of being a current smoker or a past smoker (but having quit) among those who had ever smoked. Exposure to school shootings also has no statistically significant effect on the ways in which women report their own general health. Exposed women also do not report significantly different numbers of not good mental health days compared to the unexposed.

Fig. 4
figure 4

Effects of exposure to school shootings on risky behavior, health, and human capital among men. Note: The primary sample consists of individuals living in 1402 counties from 2003 to 2012 BRFSS. Covariates include indicators for age, race and ethnicity, county and year, and duration. Exponentiated coefficients along with cluster-adjusted p-values for statistical significance and associated 95% confidence intervals are reported. Confidence limits are bottom and top coded in [0.95,1.05] to enhance readability

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Figure 4 displays the effects of exposure to school shootings for the primary sample of men using data from the BRFSS. In contrast to the results for women, the risk of smoking among men is modified by exposure. Exposure to a school shooting casualty increases the risk of smoking daily among men who have ever smoked by 1.7% relative to men who were not exposed. Using the average county population of 12–17-year-old boys (4267) in 2012, exposure to a casualty, would result in 6 additional men smoking daily among men who ever smoked. Analogous to the results for women, we find substantial, statistically significant effects of exposure to school shootings on the alcohol consumption behavior of men. Exposure to a shooting increases, per casualty, the number of drinking days by 0.5%, increases the maximum number of drinks an affected man drinks on one occasion by 0.3%, and increases the number of drinking days where five or more drinks are consumed by 1.2%. Among unexposed men, the mean number of drinking days is 6.85, marginal exposure increases this mean by 0.03 days. The maximum number of drinks consumed would increase by 0.02 drinks, and the number of drinking days where five or more drinks are consumed (mean 2.17) would increase by 0.03 days. We also view these estimates as conservative lower bounds of the effect of school shootings on the drinking behavior of exposed men. Men are also much less likely to engage in physical exercise post-exposure; the likelihood of not engaging in physical exercise increases by 1.5%, per school shooting casualty. This implies that exposure to a casualty among unexposed men would result in an additional 11 men who do not engage in physical exercise.

Among men, exposure to school shootings also has human capital effects, although the effects are less noticeable compared to the effects observed in our sample of women. Exposure to a school shooting increases the likelihood of attending college or technical school by 1.4% with no changes in the likelihood of not graduating from high school or graduating from college relative to graduating from high school. This implies that exposure to a school shooting casualty would result in an additional 16 men who attend but do not graduate college or technical school in the average county. Income decreases by 0.5%, per casualty, among exposed men as compared to those not exposed. The effect on employment status is small and statistically insignificant.

Across our primary sample period, each year, on average, there are 12 school shootings with one or more casualties. The mean number of casualties is 2.3. Using these averages, our results conservatively imply that school shooting exposure depresses the health and human capital outcomes of 1103 women and 912 men annually. As a result of annual exposure, 193 women do not graduate from high school, 248 attend college or technical school but do not graduate, and 662 do not engage in the formal labor force, with 414 unemployed and 248 engaged in home management. Among exposed men, 166 additional men smoke daily than would otherwise, 304 do not engage in physical exercise, and 442 attend college or technical school, but do not graduate. These findings suggest that policymakers use the means at their disposal to mitigate school shootings and their costly societal effects.

Our findings on educational attainment and labor force participation are in line with those found in Cabral et al. (2020) which uses longitudinal data from Texas; the authors find that exposure to a school shooting reduces the likelihood of being a high school graduate (3.7%), of obtaining a bachelor’s degree by 26 (15.3%), and of employment (6.3%). Our results are smaller in magnitude most likely due to our inability to identify whether a middle or high school-age individual actually attended the school in which a shooting occurred.

5.2 Migration

The top panel of Table 6 show the effects of exposure to school shooting incidents among 12–18-year-olds exposed 1–4 years prior to the potential move year. Recall that the potential move year is 1 year prior to the ACS survey year. There is no indication of moves out of the county or PUMA in response to a school shooting. There is weak evidence, for the sample of men, that 12–18-year-olds may be less likely to move following a school shooting. The bottom panel of Table 6 shows the effects of exposure to school shooting incidents among 19–23-year-olds exposed 1–8 years prior to the potential move year. This age group has the ability to move by themselves, i.e., without a parent; they may move away to college, or for jobs elsewhere. There is no evidence whatsoever of differential probabilities of migration by exposure to school shootings.

Table 6 Effects of exposure to school shootings on migration
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This analysis provides confidence in the causal interpretations of the effects of school shootings on health and human capital outcomes. Recall that the BRFSS provides no indication of whether the person moved into the current county of residence recently or whether they have lived there all their lives. In other words, we cannot identify in- or out-migration in the data. The results of these regressions show conclusively that exposure to school shootings does not lead to significant migration.

5.3 Heterogeneity of effects

Figure 5 reports the estimates of effects for a number of subsamples and alternative definitions where we a priori might expect effect heterogeneity. In the analysis of women restricted to those whose exposures occurred 6–12 years prior to the survey, we find that the results are consistent with those obtained using the corresponding full sample. We find that the effects diminish in magnitudes for many outcomes when exposure occurred 13–24 years ago (Fig. 5).

Fig. 5
figure 5

Heterogeneity in effects of exposure to school shootings on risky behavior, health, and human capital among women. Note: The primary sample consists of individuals living in 1402 counties from 2003 to 2012 BRFSS. Covariates include indicators for age, race and ethnicity, county and year, and duration. Exponentiated coefficients are reported

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Fig. 6
figure 6

Heterogeneity in effects of exposure to school shootings on risky behavior, health, and human capital among men. Note: The primary sample consists of individuals living in 1402 counties from 2003 to 2012 BRFSS. Covariates include indicators for age, race and ethnicity, county and year, and duration. Exponentiated coefficients are reported

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When we eliminate counties that had more than 4 shootings during the sample period on grounds that counties in which school shootings are “more frequent” occurrences might be quite different than those in which school shootings are more infrequent, we find that results are qualitatively very similar to those from the primary sample. Similarly, results do not change much when counties with more than 20 schools are dropped from the sample. The one exception is that there appears to be some evidence of greater smoking propensities among women exposed to school shootings in smaller counties.

The analysis in which deaths are used to define incidents and intensity (rather than all casualties) produces substantially bigger effects for most outcomes but retains the same sign and significance as in the primary analysis among women. This feature may have a simple explanation. For every death in a school shooting incident, there are likely non-fatal casualties as well. So, if the effect of a shooting is independent of whether the casualty is fatal or not, the marginal effect of an additional death would be larger than the marginal effect of a casualty, all else equal. The exception is the results of smoking. Although the effects of school shootings on smoking are not significant among women in the primary analysis, school shootings significantly decrease the likelihood of smoking among women, and daily smoking among those who smoked during their lifetimes. Note that school shootings with deaths are quite infrequent so we cannot rule out the possibility that these results are spurious. When we limit exposure to incidents that occurred only during regular school days, or include additional shooting incidents in which there were no casualties, or limit incidents to mass shootings only, the results are very similar to those in the primary analysis (see Fig.  5).

Results of the heterogeneity analyses among men are shown in Fig. 6. In the analysis of men restricted to those whose exposures occurred 6–12 years prior to the survey, we find that the results are consistent with those obtained using the corresponding full sample. We find that the effects diminish in magnitudes for many outcomes when exposure occurred 13–24 years ago. When we eliminate counties that had more than 4 shootings or when counties with more than 20 schools are dropped from the sample, the results do not qualitatively change for the sample of men.

As in the analyses among women, the analyses in which deaths are used to define incidents and intensity produce substantially bigger effects for most outcomes among men but retain the same sign and significance as in the primary analysis. When we limit exposure to incidents that occurred only during regular school days, or include additional shooting incidents in which there were no casualties, or limit incidents to mass shootings only, the results are very similar to those in the primary analysis.

5.4 Specification checks

We conduct a number of checks to validate the estimates from our primary specifications. The results of these analyses, for the samples of women and men, are shown in Appendix Figs. A2 and  A3 respectively. Specifically, we conduct analyses that change the period of shooting incidents, address some imbalance in covariates by using entropy balance weights, include controls for local time-varying socioeconomic conditions that might confound the treatment effects, and eliminate high migration counties. Overall, the primary results are remarkably robust to changes in specification.

We also estimate two specifications that allow for heterogeneous treatment effects by cohort. Cohorts are defined by the year of the BRFSS survey in one specification and by the decade of the school shooting event (1990s and 2000s) in the other. We use the approach derived in Wooldridge (2021) to estimate cohort-level heterogeneous effects. The population-weighted averages of those effects are qualitatively very similar to the effects estimates in the primary specifications (see Appendix Figs. A2 and  A3).

Specifications that control for annual county unemployment rates or for annual county-level homicide rates do not change results in any substantive ways. To take the criticism of such additional control checks of Pei et al. (2019) into account, we estimate regressions with county-level unemployment and homicide rates as outcomes, holding the right-hand sides of the specifications the same. Results shown in Appendix Table A1 show that the effects of shooting exposure are small and statistically insignificant, which we interpret as another confirmation of the validity of our results. Regressions based on samples that eliminate counties with the highest levels of net in- and out-migration also produce very similar results.

We also conduct two sets of placebo-like regressions, the results of which are available in Appendix Table A2. In the first set of placebo regressions, individuals who were between 4 and 10 years old in the year (and county) of a shooting are defined as exposed. The effects are overwhelmingly insignificant. In the second set of placebo regressions, individuals who lived in counties where a shooting occurred when they were between 20 and 26 years old were defined as being exposed. Again, the effects are overwhelmingly insignificant. In the small number of cases where the estimate is statistically significant, the effects are opposite in sign to the results we find in the primary sample suggesting, if anything, that the bias in the primary regression estimates is toward zero.

The results of additional specification checks in which we randomly assign the school shooting incidents (date and intensity) to counties among those that experienced no school shootings are reported in Appendix Table A3. The table shows the means and medians of the exponentiated coefficients from 20 replications of the exercise and the p-value of a nonparametric test of the hypothesis that the median of the exponentiated coefficients is equal to one. The results show that the null hypothesis cannot be rejected across the board, lending additional credence to our primary results.

We also consider a set of specification checks for the migration regressions using the ACS. In the primary specification, a respondent is exposed to a shooting incident only if it occurred at least 1 year prior to the potential move year, and up to 4 years prior. But that means if a respondent moved “immediately” in response to a school shooting, that exposure would not be recorded as such. So, in a specification check, we define exposure using incidents from the year of a potential move as contributing to exposure. These results are reported in Appendix Table A4. This check introduces the possibility of a different measurement error – that moves prior to the shooting incident in the year of the incident would be recorded as exposure when it should not. Nevertheless, the results provide additional confidence in the finding that there is no evidence of differential migration following school shooting incidents.

6 Conclusion

In this paper, we examine the effects of school shootings on health, health-related, behaviors, and human capital outcomes of exposed students as adults in their twenties and early thirties. We use data from K12SSD, a comprehensive database of school shootings, the BRFSS, and the ACS, to estimate the effects of exposure to school shootings while in middle or high school.

Our study has three main limitations. First, because we are only able to match BRFSS respondents to the shooting incidents by county, we cannot identify whether a school-age individual in a county actually attended the school in which a shooting occurred. This measurement error likely means that our estimates are lower bounds of the true effects of school shootings. We also recognize that we do not fully address the effect of being exposed to a school shooting by race. We are unable to do so because the samples of individuals who identify as belonging to a minority racial group are too small, creating power issues. Finally, we are not able to test the mechanisms through which exposure to school shootings affects our outcomes of interest. As we alluded to earlier in our paper, the “toxic stress” from these “intense adverse experiences” may be a mechanism worth exploring. We leave this to future research.

However, despite our limitations, among women and men, we find substantial evidence of declines in health and well-being, worse health-related behaviors, and worse education and labor market outcomes. The results are robust in a variety of specification checks. We use data from the ACS to show that exposure to school shootings does not lead to significant migration. We cannot identify in- or out-migration in the BRFSS data. Therefore the analysis of migration using the ACS provides confidence in the causal interpretations of the effects of school shootings on health and human capital outcomes.