In 2016, firearms killed 38,658 people in the United States.1 Suicide and homicide are the second and third leading causes of death among people 15–34 years old, and firearms are involved in over 60% of these deaths.2 Firearm ownership, alcohol abuse, and a history of violence are known risk factors for firearm violence.3–6 One important approach to firearm violence prevention has been the implementation of policies that seek to limit ownership among those considered to be at elevated risk of violence.
Federal law prohibits the purchase and possession of firearms by felons, those convicted of domestic violence crimes or subject to final domestic violence restraining orders, anyone “who is an unlawful user of or addicted to any controlled substance,” who “has been adjudicated as a mental defective or who has been committed to a mental institution,” and others (18 U.S.C. § 922(g)).7 Beginning in 1994, the Brady Handgun Violence Prevention Act required licensed retailers (e.g., gun dealers and pawnbrokers), but not private party sellers, to conduct background checks on prospective purchasers with the goal of preventing prohibited persons from obtaining firearms.8
Currently, 19 states and Washington D.C. have additional laws extending background check requirements to private sales, though exemptions remain.9 For example, in some states, background checks are required for handgun transfers among private parties, but long gun transfers among private parties may be exempt. The private party exception to background check requirements leads to more than a fifth (22%) of firearm transactions occurring without a background check.10 For legally prohibited prospective purchasers, private party transactions are the most common means of obtaining firearms.11
In November 1998, Indiana and Tennessee repealed their requirements for background checks on private handgun transfers, creating an opportunity to conduct a quasi-experimental study of changes in firearm homicide and suicide following the repeal of comprehensive background check policies. Both states had similar requirements for comprehensive background checks, and both states repealed these laws in the same month.
Three studies have estimated the impact of permit-to-purchase laws on firearm death.12–14 Permit-to-purchase laws are similar to comprehensive background check policies in that they apply to all handgun buyers (not just those from a licensed dealer) and typically require a background check to obtain the permit. In addition, permit-to-purchase laws require the buyer to apply for the permit in person at a law enforcement agency or apply to the agency via U.S. mail before the sale can be made. Purchase permits also make it easy for private sellers to differentiate potential purchasers who satisfied requirements for firearm acquisition such as background checks. All 3 studies found permit-to-purchase laws were associated with lower firearm death rates.12–14 Tennessee and Indiana did not have permit-to-purchase requirements.
Our objective was to estimate the impact of repealing comprehensive background check policies in Indiana and Tennessee on state level firearm homicide and suicide rates. To assess the specificity of any observed associations, we also tested whether repeal was associated with changes in nonfirearm homicide and suicide rates. We hypothesized that repeal would be associated with an increase in firearm homicide and suicide rates and not in nonfirearm homicide and suicide rates.
Study Design and Sample
We used a quasi-experimental comparative case study design, described further below, to simulate the counterfactual firearm homicide and suicide rates for Indiana and Tennessee had they not repealed their comprehensive background check policies. The estimate of the counterfactual was constructed using data from control states. The study period began in 1981 in Indiana, the earliest year state level data on firearm and nonfirearm deaths are available, and 1994 in Tennessee, the year Tennessee implemented its comprehensive background check law. The postintervention period began in 1999 and continued through 2008, 10 years after repeal. Because the focus was on the impact of repealing, rather than enacting, comprehensive background check laws, only states with comprehensive background check or similar policies, such as permit-to-purchase licensing for handgun buyers during the entire study period were included in the donor pool of control states (Hawaii, Illinois, Iowa, Massachusetts, Michigan, New Jersey, New York, North Carolina, and Rhode Island). California and Nebraska implemented comprehensive background check laws in 1991 and were only included in the donor pool for Tennessee. Hawaii was excluded from the analyses of firearm homicide because of low numbers in multiple years (< 10 deaths), which can lead to unstable rates; it was included in all other analyses. The year 2001 was excluded from the analyses of homicide because of the large number of nonfirearm homicides resulting from the terrorist attack in New York on 11 September 2001.
Our main outcomes were age-adjusted firearm homicide and suicide rates per 100,000 state residents. Nonfirearm homicide and suicide rates were included as secondary outcomes to assess the specificity of the associations. These data are available from the U.S. Centers for Disease Control’s Web-based Injury Statistics Query and Reporting System (WISQARS) Fatal Injury Reports.1 WISQARS provides age-adjusted rates using the 2000 U.S. population. Nonfirearm homicide rate data for Rhode Island in 2003 was missing. We imputed this value using linear regression with all homicide and firearm homicide as predictors.
Information on race/ethnicity (% black, % Hispanic) and sex (% male) were obtained from WISQARS.1 Socioeconomic indicators, including percentage with a high school degree, median income, and state Gini coefficient were obtained from the American Community Survey.15 Percentage below the poverty line came from the Current Population Survey.16 Unemployment (% of population over age 16) came from the Bureau of Labor Statistics,17 and incarceration (incarcerated per 100,000) came from the Sourcebook of Criminal Justice Statistics.18 Data on violent crimes (homicide, rape, robbery, aggravated assault per 100,000) and law enforcement employees (sworn officers per 100,000) were available from Federal Bureau of Investigation (FBI) annual report data on crime in the United States.19 We included a measure of the crack-cocaine epidemic that incorporates cocaine-induced emergency room visits, cocaine-induced drug deaths, cocaine-related arrests, Drug Enforcement Administration drug seizures, and stories of crack-cocaine in newspapers20 as well as a measure of alcohol consumption (gallons of ethanol from spirits per capita 14 years and older).21,22 We also used FBI data to calculate the percentage of the population living in metropolitan statistical areas.19 Finally, a measure of firearm availability in the population was estimated using the ratio of firearm suicides to all suicides (WISQARS).1 Previous studies have demonstrated the ability for this measure to closely approximate firearm prevalence in a population.23,24 The analyses of suicide excluded the measures of incarceration, violent crime, and law enforcement officers and included 2 additional measures: veterans per 100,000,15 and people adhering to a religion per 100,000.25
We used the synthetic control method to estimate counterfactual firearm and nonfirearm homicide and suicide rates for Indiana and Tennessee.26,27 Using preintervention data on the outcome and factors that are predictive of the outcome, the synthetic control method generates weights for the control states in the donor pool such that the weighted combination of control states mirrors the intervention state as closely as possible during the preintervention period. To accomplish this, the synthetic control method weights the covariates and the control states with the goal of minimizing the root mean square prediction error over the pretreatment period. States may receive a weight of zero, dropping them from the synthetic control. The weighted average of states is then used to approximate the counterfactual in the posttreatment period. Our models included all covariates described above, averaged over the preintervention time period, as well as the outcome measured in 1997.28 We explored various ways of including the outcome measured in the preintervention period. We used 1 year (1997 for both states), 3 years (1994, 1996, and 1998 for Tennessee and 1981, 1990, and 1998 for Indiana), and the average of the prepolicy years. Using only 1997 resulted in the most consistently good fit. eTable 1; https://links.lww.com/EDE/B341 lists the years available for each covariate.
We created synthetic controls for each state (Indiana and Tennessee) and outcome (firearm and nonfirearm homicide and suicide rates). We used these synthetic controls to estimate the effect of the repeal on firearm and nonfirearm death by comparing the postintervention rates of each treatment state with its synthetic control over the period 1999–2008. We also estimated effects over the period 1999–2003 to limit extrapolation (eTable 4; https://links.lww.com/EDE/B341).
The synthetic control method relies on placebo tests rather than usual hypothesis testing methods. Therefore, in order to estimate the probability of witnessing a difference in homicide and suicide rates equal to or greater than the differences witnessed for our treatment states by chance alone, we conducted in-place placebo tests. For each state in the donor pool, we created a synthetic control and calculated the effect size for an imaginary intervention occurring in 1998. This allowed us to estimate the distribution of effect sizes occurring over the same time period when in fact there was no intervention. States with a poor preintervention fit (root mean square prediction error > 5 times that of the intervention state) were excluded from these calculations.26 This work was completed using Stata version 14.2.29 Stata code is available in eAppendix 7; https://links.lww.com/EDE/B341.
We conducted alternative analyses to test the robustness of our findings. First, we extended the preintervention period for Tennessee to include 1981–1998. Prior to 1994, buyer information was sent to law enforcement, but law enforcement was not required to conduct a background check. Second, we added California and Nebraska to the donor pool for Indiana. Both states implemented comprehensive background check policies in 1991, so we dropped the preintervention years 1981–1990. Third, we repeated the synthetic control method among high-risk subgroups. For homicide, we included only men 20–39 years old, and for suicide, we included only men 60 years and older. Fourth, we conducted an analysis using generalized least squares regression following the example of Webster et al.13 The regression models included state and year fixed effects and robust standard errors as well as the same set of covariates used in the synthetic control analysis, with the exception of violent crime rates and gun availability to avoid controlling for potential mediators. We also excluded the crack index as it was only available through the year 2000. We used permutation tests to generate P values. Descriptions of the alternative analyses are available in the Supplementary Materials (eAppendices 2–6; https://links.lww.com/EDE/B341).
Indiana and Tennessee saw elevated rates of firearm homicide in the 1990s followed by a sharp decline heading into the turn of the century (Figure 1A). Firearm homicide rates were highly variable over this time period. The mean firearm homicide rates in Indiana and Tennessee declined by 5% and 21% from their prerepeal to their postrepeal periods (Table 1). For both states, the decline happened after a similar decline in the population-weighted average of control states.
Suicide rates declined more gradually over the study period (Figure 1B). In Indiana, suicide rates declined by 12%, and in Tennessee, suicide rates declined by 5% from their prerepeal to their postrepeal periods (Table 1). Firearm suicide rates also declined in the population-weighted average of states eligible to serve as controls.
Results from the Synthetic Control Method
Table 2 shows the weights applied to each donor state to form the synthetic controls and the resulting root mean square prediction errors. The root mean square prediction errors indicated an adequate fit with the exception of Tennessee’s firearm suicide analysis. Tennessee’s firearm suicide trend was higher than that in any of the states in the donor pool. As a result, no weighted combination of state rates provided a good estimate of the counterfactual trend in firearm suicides for Tennessee. To address the problem created by Tennessee’s high intercept, we subtracted the mean preintervention firearm suicide rate from the annual rates in each state and reran the synthetic control analysis for Tennessee using these demeaned values.30 These results provided an improved estimate of the counterfactual (root mean square prediction error = 0.38 vs. 1.19) and were used in place of the original synthetic control model.
Covariate balance for each state and its synthetic control is given in eTables 2 and 3; https://links.lww.com/EDE/B341. In some cases, small absolute differences resulted in apparently large relative differences (e.g., % Hispanic). Differences in the outcomes in 1997 were also apparent. However, when assessing preintervention balance for the outcomes, more weight should be placed on the root mean square prediction error, which takes into account all preintervention time points. The root mean square prediction errors of 4 placebo tests (1 for firearm homicide and 2 for nonfirearm suicide in Indiana, and 1 for nonfirearm suicide in Tennessee) exceeded the pre-established threshold of 5 times that of the intervention state and were removed. Detailed results, including difference-in-differences and postrepeal slopes are provided in eTable 4; https://links.lww.com/EDE/B341.
Comparing Indiana to Synthetic Indiana over the first 10 years in the postintervention period, the difference in mean firearm homicide rates after the repeal of comprehensive background check policies was 0.7 firearm homicides per 100,000, representing a relative increase of 22% over Synthetic Indiana, or an additional 43 deaths per year (Table 3, Figure 2). In 2 of the 7 placebo tests, the magnitude of the differences in firearm homicide rates after repeal was larger than that witnessed in Indiana (eFigure 1; https://links.lww.com/EDE/B341). The mean rate of nonfirearm homicide comparing Indiana to Synthetic Indiana was 0.4 per 100,000, or 23%, higher than the nonfirearm homicide rate in Synthetic Indiana. This translates to an additional 21 deaths per year. None of the 9 in-place placebo tests showed larger differences postrepeal.
The difference in average firearm homicide rates after repeal between Tennessee and Synthetic Tennessee was 0.4 homicides per 100,000, which translates to an 8% increase in the firearm homicide rate or an additional 23 deaths per year (Table 3, Figure 2). Five of the 10 in-place placebo tests showed a difference in firearm homicide rates of greater magnitude than that witnessed in Tennessee. The rate of nonfirearm homicides was 0.1 per 100,000 higher than in Synthetic Tennessee. This equates to 8 additional deaths per year. Six of the 11 placebo tests showed larger differences than those witnessed comparing Tennessee to Synthetic Tennessee.
The mean rate of firearm suicides after the repeal of Comprehensive Background Check policies was 0.5 per 100,000 higher in Indiana compared with Synthetic Indiana, representing a relative increase of 8% or 29 additional deaths per year (Table 3, Figure 2). In 2 of the 9 placebo tests, the magnitude of the difference in firearm suicide rates after repeal was larger than that witnessed in Indiana (eFigure 2; https://links.lww.com/EDE/B341). The mean rate of nonfirearm suicide in Indiana was 0.04 per 100,000 lower than the rate in Synthetic Indiana, a difference of 0.7% or 2 deaths per year. Six of the 7 in-place placebo tests showed larger differences postrepeal.
Demeaned firearm suicide rates in Tennessee after the repeal of comprehensive background check policies were 0.3 per 100,000 higher than the rate in Synthetic Tennessee, which translates to a 3% increase in the firearm homicide rate or 16 additional deaths per year (Table 3, Figure 2). Two of the 11 in-place placebo tests showed differences in firearm suicide rates of greater magnitude than that witnessed in Tennessee (eFigure 2; https://links.lww.com/EDE/B341). Tennessee had a 0.6% higher rate of nonfirearm suicides than Synthetic Tennessee. This is equivalent to 2 more deaths per year. All 10 of the placebo tests showed larger differences than that witnessed comparing Tennessee to Synthetic Tennessee.
Alternative Analyses and Specifications
The results from the alternative analyses were similarly small in absolute magnitude and within the range of natural variation (eAppendices 2–6; https://links.lww.com/EDE/B341).
We did not find changes in firearm mortality rates associated with the repeal of comprehensive background check policies for firearm acquisition in Indiana and Tennessee. Our results showed small absolute increases in firearm homicide and suicide rates relative to controls, but these differences were within the range of what could be expected, given natural variation. We also found changes in nonfirearm homicide and suicide. These changes were smaller in magnitude and, with the exception of the change in the nonfirearm homicide rate in Indiana, within the estimated range of natural variation; we would expect the repeal of comprehensive background check policies to result in changes in firearm homicide and suicide but not other causes of homicide and suicide.
Previous studies in Missouri and Connecticut found stronger evidence for an association between firearm homicide and suicide rates and changes in permit-to-purchase handgun laws.12–14 Two Missouri studies reported increases in the firearm homicide and suicide rates of 23% and 15%, respectively, following the repeal of a permit-to-purchase law.13,14 Studies of the effects of implementing a permit-to-purchase law in Connecticut found that the implementation of the law was associated with a 40% reduction in firearm homicide rates and a 16% reduction in firearm suicide rates.12,14 It should be noted that the magnitude of the relative difference in firearm homicide rates in Indiana (22%) nearly matched the magnitude of the association from the Missouri homicide study. However, there were 2 key differences between our results and the results from these previous studies. First, the results reported in this study were within the range of natural variation. Second, a similar pattern occurred with our negative control, nonfirearm homicide, which saw a relative difference of 23%. The Missouri and Connecticut studies found no evidence of concurrent change in nonfirearm homicide rates.
The results from the current study may differ from previous studies for a variety of reasons. One important difference is that Indiana and Tennessee repealed comprehensive background check laws, where Missouri repealed and Connecticut enacted permit-to-purchase laws. There are several reasons to believe that a permit-to-purchase law may be more effective at deterring high risk gun buyers than a comprehensive background check law without a permit requirement. Permit-to-purchase laws generally require contact with law enforcement to obtain the permit. Straw buyers or others with criminal intent may be less willing to risk law enforcement scrutiny. In addition, in many permit-to-purchase states, permit issuing authorities have more time to conduct the background check and identify potentially disqualifying factors. Finally, it may be easier for law-abiding sellers, who wish to ensure that the prospective buyer is not prohibited, to merely ask to see the required permit, rather than involving a gun dealer to conduct the mandated background check (as in non-permit-to-purchase comprehensive background check states). As a result, compliance may be greater in permit-to-purchase states.
More generally, noncompliance with comprehensive background check laws may be widespread. A recent survey estimated that in states with such laws, as many as 26% of firearm owners who purchased a firearm in the prior 2 years through a private party transfer did so without obtaining a background check.10 Another study showed little change in firearm background checks following the implementation of comprehensive background check laws in Colorado and Washington.31
Strengths and Limitations
This study benefits from the use of multiple comparison years, the application of a rigorous statistical method for estimating the counterfactual, and the application of multiple alternative analyses. We were also able to include a robust set of covariates and reliable measures of our outcomes.
This study is subject to a number of limitations. First, the study was challenged by the ability of the synthetic states to mirror the treatment states, given the small number of at-risk controls eligible for inclusion in the donor pool and the small number of preintervention years available for Tennessee. As a result, some covariates remained unbalanced between treatment and synthetic states, such as the measure of percentage Hispanic. However, to bias the projection of the counterfactual postintervention, these covariates would need to change from the pre- to postintervention periods. Second, the small number of control states also limited our ability to characterize the role of natural variation in our outcomes over time. Third, the study measured the impact of the repeal of comprehensive background check laws during a period of rapid decline in firearm homicide nationally,32 making it more difficult to detect a signal in the homicide analyses. Fourth, the year of comprehensive background check repeal, 1998, was also the year the National Instant Criminal Background Check System (NICS) was launched, the interim provision of the Brady Law requiring a 5-day waiting period was removed, and federal law requiring background checks for transfers at licensed retailers was extended to apply to all firearms, including long guns. The transition to NICS was a procedural change that we assume had little impact on firearm transfer behavior. The change in policies affecting waiting periods and long gun purchasers, however, could bias our results. In terms of the change in waiting period laws, only Indiana and Tennessee repealed state waiting period laws at this time.33,34 The states in the donor pool did not repeal waiting periods. If waiting periods reduce firearm death, we would expect this change to bias our results away from the null. As a result, we cannot attribute results entirely to changes in comprehensive background check policy.
The extension of federal background check requirements to long gun transfers affected treatment and donor states unequally. California, Hawaii, Illinois, Massachusetts, New Jersey, and Rhode Island had state background check requirements for long gun transfers prior to 1998 and thus did not experience a change in policy.35 States without a policy, however, did experience a change in 1998. If background checks for long guns reduced firearm deaths, the treatment states and some states in the control group would have experienced a drop in firearm deaths, biasing the results toward the null. In 2014, 8% of firearm homicides in which the type of firearm used was known were committed with rifles or shotguns.36 For comparison, handguns were used in 90% of firearm homicides. Available data from 2008 suggest that 26% of firearm suicides were committed with shotguns or rifles, while 66% were committed with handguns.37 This suggests that changes in long gun acquisition policy are less likely to have an impact on firearm death than changes in handgun acquisition policy.
Finally, the synthetic control group is an estimate of the counterfactual and relies on a number of assumptions. To interpret differences postintervention, we must assume the preintervention fit was adequate, there were no unmeasured confounders that changed between pre- and postintervention, and the projection of the counterfactual over the postintervention time period continued to approximate what would have happened in the absence of repeal.
The findings from this study suggest that there was no association between repealing comprehensive background check policies and changes in firearm homicides and suicides in Indiana and Tennessee. This is in contrast to previous studies that found changes in firearm homicide, and suicide rates were associated with the implementation and repeal of permit-to-purchase laws. This suggests that comprehensive background check and permit-to-purchase laws have different effects. However, given the heterogeneity in responses to 2 policies requiring background checks, understanding whether and how comprehensive background check and permit-to-purchase laws influence firearm homicide and suicide rates requires further study. Future research is needed to assess the impact of comprehensive background check and similar policies on firearm homicide and suicide rates in other states. Additionally, future studies should explore differences in implementation and enforcement of comprehensive background check policies in order to understand effects at a more granular level. Understanding the causes of the variation in effects across states will be important for informing implementation and enforcement of comprehensive background check policies.
The authors gratefully acknowledge Philip J. Cook for his contributions to this work. This study was funded by the Joyce Foundation (grant ID 15-36377), the Robertson Fellowship in Violence Prevention Research, Becas Chile as part of the National Commission for Scientific and Technological Research, and the Heising-Simons Foundation (grant ID 2016–219).
1. Fatal injury reports. Web-based Injury Statistics Query and Analysis System (WISQARS). Accessed January 22, 2018.
2. Leading causes of death 1981–2016. Web-based Injury Statistics Query and Analysis System (WISQARS). Accessed February 2, 2018.
3. Anglemyer A, Horvath T, Rutherford GThe accessibility of firearms and risk for suicide and homicide victimization among household members: a systematic review and meta-analysis. Ann Intern Med. 2014;160:101110.
4. Wintemute GJ, Drake CM, Beaumont JJ, Wright MA, Parham CAPrior misdemeanor convictions as a risk factor for later violent and firearm-related criminal activity among authorized purchasers of handguns. JAMA. 1998;280:20832087.
5. Wintemute GJ, Wright MA, Castillo-Carniglia A, Shev A, Cerdá MFirearms, alcohol and crime: convictions for driving under the influence (DUI) and other alcohol-related crimes and risk for future criminal activity among authorised purchasers of handguns. Inj Prev. 2018;24:6872.
6. Kaplan MS, McFarland BH, Huguet N, et al.Acute alcohol intoxication and suicide: a gender-stratified analysis of the National Violent Death Reporting System. Inj Prev. 2013;19:3843.
7. The Gun Control Act. 18 U.S.C. § 922(g). 1968.
8. Brady Handgun Violence Prevention Act. Pub.L. 103–159, 107 Stat. 15361993.
9. Law Center to Prevent Gun Violence. Universal background checks. 2017. Available at: http://smartgunlaws.org/gun-laws/policy-areas/background-checks/universal-background-checks/
. Accessed August 21, 2017.
10. Miller M, Hepburn L, Azrael DFirearm acquisition without background checks: results of a national survey. Ann Intern Med. 2017;166:233239.
11. Vittes KA, Vernick JS, Webster DWLegal status and source of offenders’ firearms in states with the least stringent criteria for gun ownership. Inj Prev. 2013;19:2631.
12. Rudolph KE, Stuart EA, Vernick JS, Webster DWAssociation between Connecticut’s permit-to-purchase handgun law and homicides. Am J Public Health. 2015;105:e49e54.
13. Webster D, Crifasi CK, Vernick JSEffects of the repeal of Missouri’s handgun purchaser licensing law on homicides. J Urban Health. 2014;91:293302.
14. Crifasi CK, Meyers JS, Vernick JS, Webster DWEffects of changes in permit-to-purchase handgun laws in Connecticut and Missouri on suicide rates. Prev Med. 2015;79:4349.
15. United States Census Bureau. American Community Survey. Available at: http://www.census.gov/programs-surveys/acs/
. Accessed October 26, 2016.
16. United States Census Bureau. Current Population Survey. Available at: https://www.census.gov/programs-surveys/cps/data-detail.html
. Accessed October 26, 2016.
17. Bureau of Labor Statistics. Local Area Unemployment Statistics. 2013. Available at: http://www.bls.gov/lau/home.htm
. Accessed June 23, 2013.
18. Hindelang Criminal Justice Research Center. Sourcebook of Criminal Justice Statistics. Available at: http://www.albany.edu/sourcebook/index.html
. Accessed April 15, 2013.
19. Federal Bureau of Investigation. Crime in the United States, 1999, 2000, 2001, 2002, 2003, 2004, 2005, 2006, 2007, 2008, 2009, 2010. Ann Rep. Available at: http://www.fbi.gov/about-us/cjis/ucr/ucr-publications -Crime
. Accessed August 8, 2016.
20. Fryer RG, Heaton PS, Levitt SD, Murphy KMMeasuring crack cocaine and its impact. Economic Inquiry. 2013;51:16511681.
21. Nephew TM, Yi H, Williams GD, Stinson FS, Dufour MCU.S. Apparent Consumption of Alcoholic Beverages Based on State Sales, Taxation, or Receipt Data. 2004.Bethesda, MD: NIAAAA, Alcohol Epidemiologic Data System;
22. LaVallee RA, Kim T, Yi HApparent Per Capita Alcohol Consumption: National, State, and Regional Trends, 1977–2012. 2014:98.Bethesda, MD: NIAAA, Alcohol Epidemiologic Data System;
23. Azrael D, Cook PJ, Miller MState and local prevalence of firearms ownership measurement, structure, and trends. J Quant Criminol. 2004;20:4362.
24. Cook PJ, Ludwig JThe social costs of gun ownership. J Public Econ. 2006;90:379391.
25. The Association of Religion Data Archives. Religion and congregation membership survey. Available at: http://www.thearda.com/Archive/ChState.asp
. Accessed October 26, 2016.
26. Abadie A, Diamond A, Hainmueller JSynthetic control methods for comparative case studies: estimating the effect of California’s tobacco control program. J Am Stat Assoc. 2007;105:493505.
27. Abadie A, Gardeazabal JThe economic costs of conflict: a case study of the Basque country. Am Econ Rev. 2003;93:113132.
28. Kaul A, Klobner S, Pfeifer G, Schieler MSynthetic control methods: never use all pre-intervention outcomes as economic predictors. Available at: http://www/oekonometrie uni-saarland de/papers/SCM_ Predictors pdf
. Accessed November 23, 2016.
29. Stata Statistical Software: Release 14 [computer program]. 2015.College Station, TX: StataCorp LP;
30. Doudchenko N, Imbens GWBalancing, Regression, Difference-in-differences and Synthetic Control Methods: A Synthesis. 2016.Cambridge, MA: National Bureau of Economic Research;
31. Castillo-Carniglia A, Kagawa RM, Webster D, et al.Comprehensive background check policy: effects on firearm background checks in three states. Injury Prevention. 2017. doi: 10.1136/injuryprev-2017–042475.
32. Wintemute GJThe epidemiology of firearm violence in the twenty-first century United States. Annu Rev Public Health. 2015;36:519.
33. Regional Justice Information Service. Survey of State Procedures Related to Firearm Sales, Midyear 1999. Available at: http://www.ojp.usdoj.gov/bjs/
. Bureau of Justice Statistics, U.S. Department of Justice; 2000. Accessed January 17, 2017.
34. Manson DA, Gilliard DK, Lauver GPresale Handgun Checks, the Brady Interim Period, 1994–98. Available at: http://www.bjs.gov/
. Bureau of Justice Statistics, U.S. Department of Justice; 1999.
35. Regional Justice Information Service. Survey of State Procedures Related to Firearm Sales, 1997. Available at: http://www.ojp.usdoj.gov/bjs/
. Bureau of Justice Statistics, U.S. Department of Justice; 1998.
36. Uniform Crime Reporting Program. Expanded homicide data table 8: murder victims by weapon, 2010–2014 In: expanded_homicide_data_table_8_murder_victims_by_weapon_2010-2014, ed. Available at: https://ucr.fbi.gov/crime-in-the-u.s/
. Federal Bureau of Investigation; 2014.
37. National Violent Death Reporting System. Web-based Injury Statistics Query and Analysis System (WISQARS). Available at: https://wisqars.cdc.gov:8443/nvdrs/nvdrsDisplay.jsp
. Accessed August 22, 2017.