Proxies for legal firearm prevalence

We take an expansive view of the links between policy, quantitative marketing and economics. Any empirical economic analysis of regulated markets must condition on the acquisition policies that define legal transactions in those markets. Marketers operating in regulated markets can influence policy through a variety of actions, including directly via lobbying, or indirectly via demarketing, public relations or product design.

We think the findings make several contributions to quantitative marketing and economics. Evaluating durable goods’ market potential requires estimation of market saturation, which in turn requires estimation of durable goods’ served available market. To our knowledge, this is the first research to show that durable good acquisitions reliably indicate overall levels of a durable good’s penetration. Prevalence and sales are directly related by construction, yet prevalence may also be affected by migration, divestiture or death. Additionally, collectors’ purchases may increase sales without increasing overall prevalence. Surprisingly, we find that the number of product retailers does not reliably predict durable good prevalence. We further believe this is the first study of archival firearm purchase data in the marketing literature. Finally, some of the methods we employ might help to guide proxy evaluation in other marketing contexts.

More broadly, we hope to contribute to the policy evaluation literature that spans several fields, including economics, marketing, medicine, public health and public policy. We offer the first evaluation of proxies for LFP, as opposed to TFP, and introduce two new retail-based proxies for LFP. We also find that FSS is highly correlated with LFP cross-sectionally, but changes in FSS do not reliably indicate changes in LFP. This latter finding may be relevant to several dozen published studies which have used FSS as a proxy for TFP in cross-temporal research designs. Finally, we provide the first assessments of FBI background checks as a proxy for LFP.

Azrael et al. (2004) and Kleck (2004) compared candidate proxies for TFP to surveys of firearm prevalence. The two surveys used were the General Social Survey (GSS) and the Behavioral Risk Factor Surveillance System Survey (BRFSS). GSS is a biennial national interview-based survey with a response rate of 77% (Kleck 2004). However, the high cost of the interview format limited the national sample size to about 3,000 respondents per year (Azrael et al. 2004), too few to reliably estimate firearm prevalence at the state level. BRFSS is a telephone survey conducted by state health departments with a median response rate of 67% and a median of 2,061 respondents per state per year (Azrael et al. 2004; Powell et al. 1998).

One might ask whether survey data can measure firearm prevalence directly, without need for a proxy. Most literature has not taken that approach. Surveys often feature small samples, design inconsistencies, and insufficient frequency to estimate granular studies of firearm policy effects. Further, firearm surveys may feature nonrandom response rates, question ambiguities, and respondent misreporting, considering the political and personal sensitivity of the topic.

Prior research has used a variety of behavioral proxies for TFP. Duggan (2001) uses Guns & Ammo magazine circulation data to proxy for firearm prevalence. Azrael et al. (2004) and Kleck (2004) evaluated a range of firearm proxies including concealed carry permits, NRA memberships, crime and arrest data, unintentional firearm deaths, outdoor magazine subscriptions and federal firearm licensees. Lang (2013), Briggs and Tabarrok (2014) and Vitt et al. (2018) use FBI background checks as a proxy for prevalence. Kovandzic et al. (2011; 2013) use outdoor sports magazines subscriptions, percentage of those voting Republican in the 1988 presidential election, and numbers of military veterans as instruments for their proxy FSS.⁵

A variety of earlier papers have studied firearm license data. Krug (1967), Stolzenberg and D’ alessio (2000), and Haas et al. (2007) interpreted concealed carry permits as a proxy for firearm prevalence. Fisher (1976) uses data on handgun licenses and registrations in Detroit to measure firearm availability. Bordua (1986) uses Firearm Owners Identification Cards in Illinois to measure firearm prevalence. Sloan et al. (1988) use concealed-weapons permits issued in Seattle and restricted-weapons permits in Vancouver in their comparison of crime data between the two regions. McDowall (1991) uses handgun purchase licenses issued in Detroit, in addition to FSS. Moody et al. (2010) and Bangalore and Messerli (2013) use gun registration rates to proxy for gun ownership across nations. Hunting licenses have been used to proxy for firearm prevalence and augment other firearm proxies (Andrés and Hempstead, 2011; Kleck 2004; Siegel et al. 2014a; 2014b). Unfortunately, hunting license data are often limited by locally imposed quotas and “therefore may have limited use in identifying changes in firearm ownership over time.” (Schell et al. 2020, p. 17) Hunting license quotas may be more related to local animal populations than changes in firearm prevalence. Although firearm licenses have been studied previously, we do not know of any prior work that distinguished TFP from LFP or evaluated proxies for LFP.

Kleck (2015) documents the extensive use of proxies for firearm prevalence in the literature studying links between guns and crime. He counts 19 proxies used by 41 published studies, but concludes that "none of the proxies used in prior research, including [FSS], have been shown to be valid for purposes of judging trends over time.”

Schell et al. (2020), motivated by some of the same observations as us, estimate a latent state/year index of household firearm ownership combining survey and proxy data. We view this as an important effort and a worthy goal. Yet one limitation is that measures of ground truth are needed to establish the validity of latent empirical constructs. This concerns us because the Schell et al. (2020) index estimates Massachusetts firearm penetration to have fallen by about one third between 2010 and 2016 (from 12.2% in 2010 down to 9% in 2016), whereas the state’s license data showed that the proportion of individuals with valid firearm licenses increased by about half from 2010 to 2016, from 4% to 6%. A second concern is that the latent index uses FSS intertemporally, which has been questioned by Kovandzic et al. (2013) and Hayo et al. (2019), among others.⁶

We measure Legal Firearm Prevalence (LFP) using firearm license data from Massachusetts. All adults in Massachusetts are legally required to maintain an active license in order to purchase or possess a firearm. Firearm licenses expire after six years. New licenses cost $100, as do license renewals.

We observe all new firearm licenses and license renewals issued between January 1, 2006 and December 31, 2017. For each record, we observe the license issue date, type, status (new or renewal), licensing authority (typically a local police agency), and an anonymous licensee identifier. We use the term “license” to include all firearm licenses that enable legal firearm purchase and possession in Massachusetts. The data consist mainly of Class A Licenses (90%) and Firearm Identification Cards (9%).

We map each licensing authority into the county that contains it. We then measure LFP by counting firearm licensees with one or more active licenses in each county in each month. Counting licensees, rather than licenses, avoids double-counting people who hold multiple valid licenses concurrently. Web Appendix A describes potential left-censoring of LFP in 2010 and 2011 and how we resolve the issue.

Figure 1 shows that the number of firearm licensees increased by 74% over an eight-year period, rising monotonically from 3.9% of the state population in January 2010 to 6.8% in December 2017. The rate of growth was nearly constant, with minor accelerations in 2013 and 2016.

Figure 2 shows the time series of LFP per capita within each of the fourteen Massachusetts counties. Growth rates vary across counties, but downturns are remarkably rare. Franklin County had the highest average LFP, reaching 14.1% in December 2017. The counties with the highest initial LFP in 2010 grew most during the next 7 years, with the exception of Nantucket. Suffolk County had the lowest average LFP, growing from 0.9% to 2.2% over 8 years.

LFP has several strengths. Most importantly, it counts all firearm licensees based on official government records. It is a population rather than a small or self-selected sample drawn from a population. The fact that licenses must be renewed regularly at substantial cost suggests that LFP should meaningfully reflect both new acquisitions and divestitures of legal firearm access. Unlike survey data, it does not rely on firearm owners’ self-reports, and therefore is not subject to sampling error, nonresponse bias, survey design problems or respondent misreporting. Finally, the measure counts distinct people, rather than individual licenses issued or individual firearms, an important property when one individual may hold multiple license types and collect multiple firearms.

The measure also has some weaknesses. Most importantly, we only have data from Massachusetts. Although we filed similar Freedom of Information Act (FOIA) requests with three other states (California, Connecticut and Hawaii), none responded by providing comparable data, despite our repeated inquiries. Second, LFP does not measure firearm lethality, concealability, or concentration of weapons among households or individuals.

We do not claim that LFP also indicates illegal firearm prevalence; hence the term "Legal" in Legal Firearm Prevalence. One of the primary reasons to conduct firearm research is to inform firearm policy, and LFP is a direct outcome of firearm acquisition policies. Therefore, if we seek to understand the effects of policy changes on legal firearm acquisitions, we should distinguish LFP from illegal firearm prevalence. We view measurement of IFP and evaluation of IFP proxies as important topics for future research.

Firearm retailing activity leads directly to firearm acquisitions, suggesting that retail-based measures may proxy for legal firearm prevalence. However, retail-based proxies have two limitations. First, no national database of firearm acquisitions exists, so direct, comprehensive measures of firearm retailing activity are not available for all areas. Second, any retail-based data source will exclude acquisitions that occurred prior to the data sample. Firearms are durable goods, so retail-based data sources cannot provide a fully accurate measure of firearm prevalence. Still, we have found three sources of retail-based data that offer candidate proxies for LFP.

Massachusetts is one of a few states that requires firearm acquisitions to be registered with the state. Acquisition data include Sales, Transfers and Registrations (“STR”). We received the population of Massachusetts STR along with the firearm license data by filing a FOIA request.

We also obtained data on the population of firearm sales intermediated by an anonymous online firearm retail platform (Online Sales or “OS”). The data report individual transactions and include buyer zip codes, which we use to assign each firearm acquisition to buyer counties.⁷ OS data are less comprehensive than the STR data, as they do not report offline sales transactions through traditional firearm retailers, but they do have two advantages. First, OS data cover the entire United States, suggesting that OS data may provide a retail-based proxy with national scope. Second, some firearm sales might not be legally registered with the state, and therefore excluded from the STR data; or they might not be registered in a timely fashion.

The third retail-based proxy we analyze is the population of Federal Firearms Licensees (FFLs) that sell firearms to consumers, a retail-based proxy that was first considered by Kleck (2004). The data were downloaded from the Bureau of Alcohol, Tobacco, Firearms and Explosives (ATF) website.⁸ We matched each FFL address to the county that contained it using ArcGIS, a popular geocoding software. The FFL proxy counts the number of firearm retailers in each county in each month and shows substantial intertemporal variation. Licenses for FFLs expire after three years. Substantial numbers of FFLs enter and exit during the sample period.

The proportion of firearm suicides, FSS, was validated as the highest cross-sectional correlate of TFP in survey data. We have not found any clear theoretical justification in the literature for FSS as a proxy for firearm prevalence, but FSS is the most frequent proxy for total firearm prevalence in the scientific literature, and is therefore an important proxy to evaluate. We also analyze the proxy’s two components, Firearm Suicides (FS) and Suicides (S), as they are readily available and less volatile over time. We lack a compelling theoretical reason to consider S or FS valid proxies; we consider them because they each contribute to variation in FSS.

We count suicides by county and month using Multiple Causes of Death (MCOD) files from the National Center of Health Statistics (NCHS) division of the Centers for Disease Control and Prevention (CDC). MCOD files report information collected from U.S. death certificates provided by state vital registration offices.⁹

All candidate proxies described above are available monthly from January 2010 through December 2017, except for FFL data. FFL data are available from January 2014 through December 2017, with two months of data missing in September and October of 2015.¹⁰

Firearms are durable goods, so most consumers who acquire firearms retain them for substantial periods of time. However, the proxy measures listed above are counts of transitory events (e.g., suicides, firearm acquisitions). Therefore, we consider two forms of each proxy: static and cumulative. The static version is the count observed within each county and time period. The cumulative version is the accumulation of all activity observed in a county from the beginning of the sample up until a given time period.¹¹ For FFLs, the contemporaneous value of the proxy is the net accumulation of firearm retailers from the start of the sample until the current time period; therefore, we take the static version of the proxy as the change in FFLs from the previous time period to the current time period.

We see a meaningful distinction between cumulative retail-based proxies and cumulative suicide-based proxies. LFP is the totality of accumulated firearm acquisitions and divestitures, so accumulated firearm acquisitions should meaningfully reflect some variation in LFP. However, prior literature provides no similar theoretical connection between LFP and suicide data. We include FSS and its components because FSS is frequently used in existing literature, not because we have a theory that predicts suicide-based proxies will reflect LFP. We consider cumulative versions of the suicide-based proxies because we believe they have not been evaluated previously, and in fact we find they perform better than FSS in cross-temporal research designs.

Table 1 summarizes candidate firearm proxies, labels, data sources, sample periods, and descriptive statistics.

We report cross-sectional correlations between candidate proxies and LFP per capita, following Azrael et al. (2004) and Kleck (2004), using population data from the 2010 Census for the 14 counties in Massachusetts. Unlike subsequent research designs, cross-sectional analysis using the full sample does not allow for distinctions between cumulative and static versions of candidate proxies.

Table 2 shows the cross-sectional correlation matrix of LFP and the candidate proxies using the full sample period. All measures except FSS are per capita. All six suicide-based and retail-based proxies are significantly correlated with LFP, ranging from .56 to .86. STR is the most highly correlated with LFP at .86.

FSS is the second most strongly correlated with LFP at .74. This correlation lies within the .64-.92 range reported by Kleck (2004, Tables 1 and 3) and below the .81-.93 range reported by Azrael et al. (2004, Table 3).¹³

The remaining four proxies have correlations with LFP ranging from .56 (FFL) to .68 (FS). The suicide-based proxies are strongly correlated amongst themselves (.83-.95) by construction, as Suicides include Firearm Suicides, and FSS is the ratio of the two. The retail-based proxies correlate with each other to a lesser degree (.43-.75). Correlations between the two sets of proxies are not significant and some are close to zero, suggesting that the retail-based proxies may offer information that is not available in the suicide-based proxies.

We rely on intertemporal correlations and visual interpretation to assess the utility of each candidate proxy for LFP in trends analysis. Recall that Fig. 1 shows that LFP per capita increased monotonically over time with variable growth rates. In this analysis, LFP and the proxy measures are again measured per capita, except static and cumulative FSS.

Figure 3 shows how static and cumulative suicide-based proxies change over time at the state/month level. The three static proxies are highly variable and their time trends do not track LFP. Suicides correlate with LFP most highly at .28; FSS shows the lowest correlation with LFP at .03.

The cumulative suicide-based proxies are somewhat different. Cumulative FS and S both increase, by construction, and therefore both correlate very highly with LFP at 0.997, although their average growth rates exceed that of LFP. Cumulative FSS, in contrast, correlates negatively with LFP at -.57.

Figure 4 shows how static and cumulative retail-based proxies change over time at the state/month level. The three static proxies are again highly variable. STR correlates with LFP mostly highly at .76, followed by OS at .47; both are statistically significant. Change in FFL correlates negatively with LFP at -.26.

The cumulative retail-based proxies are again somewhat different. Cumulative STR and Cumulative OS both increase monotonically, by construction, and both correlate with LFP at 0.998, although their aggregate growth rates are again larger than LFP. FFL, in contrast, increases slowly but then levels off, and correlates with LFP at 0.73.

Overall, we find that 4 out of 12 candidate proxies correlate very highly with LFP intertemporally, above .997. Among the static proxies, STR and OS are the most promising with correlations of .76 and .47. Static FSS correlates with LFP at just .03, and cumulative FSS is negatively correlated with LFP at -.57.

Web Appendix B reconciles the high cross-sectional correlation and low cross-temporal correlation between FSS and LFP. It repeats the cross-sectional correlation and graphical analyses across four successive two-year subsamples. It shows that FSS is the most volatile of the candidate proxies, thereby explaining its low intertemporal correlation with LFP. Kovandzic et al. (2013) and Cook and Ludwig (2019) treat similar topics in greater depth.

Cross-sectional and intertemporal correlations are elegant and valid ways to estimate empirical relationships, but aggregated data may conceal unmeasured confounds that influence both firearm prevalence and firearm proxies. Next, we consider county/year panel regressions, both with and without county fixed effects and year fixed effects to control for unobservable county-specific and time-specific variables.¹⁴

We do not use per capita measures in the panel regressions, because county populations are only measured directly in the decennial census. The Census provides interpolated population estimates, but those figures are projections rather than direct measurements, and therefore subject to forecasting and interpolation errors. Further, scaling both dependent and independent variables in a regression by common factors can induce spurious correlation (Kronmal 1993; Hayo et al. 2019). Instead, we follow Azrael et al. (2004) in using county populations to weight observations and control for heteroskedasticity. We also cluster standard errors at the county level, following the experimental design rationale described by Abadie et al. (2017). 

We specify and estimate two models:

The Proxy-only Model in Eq. 1 is a regression of LFP in county c in year t on an intercept and one candidate proxy denoted x_ct. The Model with Proxy and Controls in Eq. 2 augments that simple specification with county- and year-specific fixed effects. We investigate both models because some proxies are more highly correlated with the control variables than others. Models with control variables offer more stringent tests of candidate proxies, as unit and time fixed effects typically explain large fractions of variation in panel data sets.

There is no widely agreed-upon set of criteria to establish proxy validity in panel settings. In the context of firearm prevalence, Azrael et al. (2004) and Kleck (2004) focus on size and statistical significance of correlations between candidate proxies and firearm prevalence estimates. Kovandzic et al. (2013, p.484) further emphasize that any valid proxy should explain a large portion of the variance in firearm prevalence. We evaluate the utility of each proxy in each research design using the following criteria:Later in the paper, we also pay attention to the consistency of proxy performance across research designs, as such patterns may suggest proxy utility in untested designs.

Table 3 summarizes the results of both the Proxy-only Model and the Model with Proxy and Controls. Each row of Table 3 reports results from two distinct regressions pertaining to that particular row's candidate proxy. The entire table summarizes 24 distinct regressions.

In the Proxy-only Models, 9 of the 12 candidate proxies are statistically significant predictors of LFP. These 9 proxies explain between 48-90% of the variation in LFP; all have positive relationships with LFP. Three proxies explain less than 1% of the variation in LFP: static FSS, cumulative FSS, and static FFL.

Next we focus on the more stringent Models with Proxy and Controls. 6 candidate proxies each explain more than 50% of the residual variation in LFP. Those 6 include two suicide-based proxies—Cumulative Firearm Suicides and Cumulative Suicides—and four retail-based proxies: Static and Cumulative STR, and Static and Cumulative OS. The t-stat and F-test p-values for these 6 proxies also are significant, indicating the proxy adds important information beyond that provided by the county and year fixed effects.

The remaining 6 proxies explain 0.1-17.8% of the residual variation in LFP after partialing out the controls. Static and Cumulative FSS each explain about 1% of the residual variation in LFP. This echoes the results of Kovandzic et al. (2013), who also find near-zero intertemporal correlations between FSS and survey measures of firearm prevalence.

The Static Suicides proxy is statistically significant and explains 17.8% of the residual variation in LFP. It performs substantially better than FSS, but also substantially less well than the 6 candidate proxies with Partial R² statistics exceeding 0.5.

Three candidate retail-based proxies seem especially promising, with Partial R² statistics ranging from .839 to .971, and effect sizes falling within an order of magnitude of 1: STR (1.4), Cumulative STR (0.2) and Cumulative OS (6.1).

More granular temporal resolutions allow for better controls for unmeasured confounds while reducing potential aggregation biases. Many societal outcomes (e.g., crime) are measured monthly and therefore can be studied in higher-resolution data that enables more extensive controls. Therefore we test the Models with Proxy and Controls again using county/month panel data. We specify and estimate the following models:

The models regress LFP in county c in year/month t on an intercept (β₀), one candidate proxy (x_ct), a county fixed effect (α_c) and a year/month fixed effect (λ_t). In the second model, we replace the contemporaneous value of the candidate proxy x_ct with its first lag, x_ct− 1. We evaluate first lags of candidate proxies because many longitudinal analyses in long panels (e.g., Cook and Ludwig 2006; Duggan 2001; Khalil 2017) have used lagged proxies as informal checks for reverse causation or simultaneity.

Table 4 shows the county/month panel regression results. Each row in the table reports two unique regressions pertaining to that particular row's proxy: one for the contemporaneous value and one for the first lagged value. All regressions included county and year/month fixed effects.

The qualitative conclusions in Table 4 are remarkably similar to the Proxy and Controls models estimated using county/year data. The qualitative results are nearly identical whether using contemporaneous or lagged values of the candidate firearm proxies.

Among the suicide-based proxies, only Cumulative Firearm Suicides and Cumulative Suicides explain large amounts of residual variance in LFP after partialing out the unit and time controls. The remaining contemporaneous and lagged suicide-based proxies explain 0.0-2.2% of the residual variance in LFP. The only major quantitative difference between county/month results and county/year results is that the residual variance in LFP explained by Static Suicides falls from 17.8% in annual data to about 2.0% in monthly data.

Among the retail-based proxies, Static STR, Cumulative STR, and Cumulative OS perform particularly well, with high Partial R² statistics, statistically significant beta coefficients, and effect sizes within one order of magnitude of unity. Cumulative STR again explains the most variation in LFP (98.2%). The two largest quantitative differences between county/month results and county/year results is that the Partial R² of Static STR falls from 83.9% in annual data to 52.3% in monthly data, and the Partial R² of Static OS falls from 51% in annual data to 19.1% in monthly data. These changes in variance explained align with the theory that monthly data allow better controls for unmeasured confounds than annual data.

This section seeks to quantify associations between LFP, candidate proxies, and a frequent state/year-month proxy for firearm prevalence, FBI Background Checks. We treat FBI Background Checks separately from other candidate proxies for two reasons. First, Lang (2013) showed recently that FBI background checks correlate highly with GSS survey measures of firearm prevalence in a panel of census divisions and years. Second, FBI Background Checks are only available at the state/month level, and therefore inevaluable in most of the research designs considered previously.

The Brady Handgun Violence Prevention Act of 1993 required that any person who wants to buy a gun from a federally licensed firearms retailer must submit for a background check conducted by the Federal Bureau of Investigation (FBI). The FBI publishes the number of background checks conducted for firearms purchasers in each state in each month. Most purchasers complete their purchase shortly after the FBI background check, suggesting that FBI background check data reliably indicate firearm purchase intention. Consequently, recent literature has used FBI background checks to proxy for firearm prevalence (e.g., Briggs and Tabarrok 2014; Lang 2013; Vitt et al. 2018).

Still, FBI background check data have some weaknesses. First, like STR, FBI background checks are a flow variable rather than a stock variable. Second, the FBI only publishes background check data at the state/month level, meaning it is not possible for external researchers to access more granular variation in FBI background check data. Third, the FBI publishes the total count of background checks sought rather than the number of background checks passed or the number of people who seek background checks. That means that a single person could account for multiple FBI background checks in a single state/month, and that FBI data count checks that do not lead to firearm purchases alongside those that do lead to firearm purchases (FBI 2017b). Fourth, private party sellers and transactions at gun shows do not require FBI background checks in all states (Lang 2013). Finally, there may be temporal differences between when a background check is conducted and when a weapon is purchased. 10.7% of FBI background checks in 2017 were delayed by incomplete criminal records (FBI 2017a).

Table 5 presents state/month correlations between FBI background checks, LFP and the other candidate proxies at the state/month level for 2010-2017. The most important entry in the table is the correlation between FBI background checks and LFP at 0.41. This is larger than any of the suicide-based proxy correlations over the same period, as those range from 0.03-0.28. However, it also falls short of the STR correlation with LFP of 0.76 over the same time range.

FBI background checks correlate with STR at 0.80 and with OS at 0.80. Figure 5 illustrates the relationship between FBI background checks and STR, showing that they trend similarly with corresponding spikes and dips, but a difference in levels during the first four years of the sample seems to decrease during the second half of the sample.

Overall, the state/month analysis shows that FBI background checks offer a better proxy for LFP than suicide-based proxies, but it is not as strong as other retail-based proxies.

This paper offers clear guidance for researchers who wish to study LFP as a predictor or outcome variable. Table 8 summarizes the results of proxy evaluations across research designs, using our preferred criteria for proxy validity: Partial R² greater than .5, a statistically significant parameter estimate, and positive association between proxy and LFP.

One implication for selecting a proxy for LFP should be uncontroversial: If possible, choose legal firearm acquisitions as a proxy. It was an empirical question whether firearm sales would reflect the large served available market of legal firearms prevalence, but the data indicated STR as the best available proxy in every research design tested. Multiple states maintain firearm transaction registries; see, e.g., Sorenson and Berk (2001) or Berk (2021).

Most states do not register firearm transactions. Therefore, the finding that online firearm sales serve as a valid proxy for LFP in many research designs, despite having just a 2.7% overall market share, is quite promising. We anticipate that new sources of firearm sales may become available in the future. Possible sources include systematic collection of online firearm sales listings, large consumer expenditure panels, credit card transaction data or retailer parking capacity utilization. All of those data sources have been analyzed in other academic research, though not yet within the context of firearms. We recommend inclusion of firearm retail measures in future assessments of firearm data (e.g., NORC 2021).

We also found that FBI background checks correlate highly, at 0.41, with LFP. FBI background checks also correlate with STR and OS, each at 0.80, respectively, showing that background checks are a very good indicator of overall firearm sales. However, the analysis also illustrates limitations of the FBI background checks, since data are only available by state and month. Therefore, they cannot be used in more granular county-level, daily or weekly analyses.

Finally, the suicide-based proxy results provide several clear guidelines. FSS is only a valid proxy for LFP in cross-sectional research designs. Its selection could lead to mistaken conclusions in cross-temporal designs by overcontrolling for LFP. Surprisingly, despite the non-validation of FSS as an intertemporal proxy, the results show that accumulations of the two components of FSS – namely, Firearm Suicides and Suicides – both perform well in all research designs tested. It seems logical that if FSS contains valid but noisy signals about firearm prevalence, the accumulation of those signals may offer helpful information about local changes in firearm prevalence. However, we reach this conclusion with two strong caveats. First, the finding emerged ex post; we did not expect to find this ex ante. Second, we do not know any previous analysis that made the same point or found the same result, despite numerous papers that sought to study firearm prevalence in longitudinal designs. Therefore we would encourage further research on this topic to deepen our collective understanding.

FSS is the most common cross-sectional proxy for firearm prevalence, as validated by comparisons to survey measures of TFP. We found that FSS also correlates cross-sectionally with LFP. Therefore, cross-sectional analyses that use FSS to proxy for TFP could additionally be interpreted as applying to LFP.

We also found that static FSS is nearly uncorrelated with LFP over time, and FSS was not indicated as a valid proxy in any cross-temporal design tested. Further, the analysis in Section 5 found that FSS estimates were misleadingly precise compared to LFP. Therefore, published results that used FSS in intertemporal designs may be unrepresentative of LFP.

Evaluations of firearm acquisition policies’ effects on legal firearm acquisitions require a measure or proxy for LFP. LFP also may be relevant as a moderating variable between policy enactment and other potential policy-relevant outcomes, such as firearm suicides, assaults, defensive gun uses, mass shootings or other variables. A recent report found that “the current firearms data environment is disordered and highly segmented” (NORC 2021).

We would advise caution in designing procedures for firearm acquisitions data collection, reporting and distribution. Firearm market participants do not always comply with restrictive policies (Balakrishna and Wilbur 2021), so we would recommend transparently safeguarding individual privacy. We would also advise that governments and retailers work to develop a coherent data reporting approach in order to maximize comparability of firearm acquisitions data across geography and time. We are confident that such concerns can be resolved, as they have already been considered and addressed in other sensitive contexts, such as the CDC’s mortality data.

We speculate that political leadership and advocacy will be required before such actions become policy. Firearm data production and research has been controversial in the past. A Congressional amendment in 1996 stipulated that “none of the funds made available for injury prevention and control at the Centers for Disease Control and Prevention (CDC) may be used to advocate or promote gun control.” The law effectively froze firearm research, to the later regret of the amendment’s author (Inskeep 2015).

We believe that collecting and publishing privacy-compliant firearm acquisition data would be a helpful step in evaluating firearm acquisition and use policies. It could also help reveal the mechanisms between policy changes and criminal or health outcomes. As an example, it could show how concealed-carry, open-carry or stand-your-ground policies affect legal firearm acquisitions, and then how changes in legal firearm prevalence affect crime, violence or health. However, such analyses may remain incomplete without IFP or TFP data.

The current article has several important limitations. We were only able to collect LFP and STR data for Massachusetts. Massachusetts has some of the strictest firearm laws and lowest firearm ownership rates in the nation, so it remains to be seen whether the results will generalize to other jurisdictions.

We do not have measures of IFP, so we are not able to make empirical statements about TFP or IFP. We expect that IFP will be more strongly related to illegal firearm uses than LFP. We also suspect that LFP and IFP may be related, as increasing LFP may increase supply in illegal firearm markets.

A smaller concern is that, although LFP could have decreased during the sample period, it rose nearly uniformly in every county throughout the observation window. Cumulative proxy variables may perform worse if firearm prevalence sometimes decreases. However, firearms are durable goods and we do not know of any periods of sustained firearm divestitures in recent U.S. history, therefore we are not certain how important this limitation may be. It certainly could become important if, for example, jurisdictions bought back or outlawed particular types of firearms. However, if such policies were enacted, public records might provide firearm divestitures data which could then be used to adjust LFP measures or proxies.

Firearm acquisition and usage policy evaluations require reliable, systematically collected, longitudinally valid proxies for legal firearm prevalence. We hope the present paper can advance firearm research by evaluating proxies for LFP. We hope that collaborative efforts between policy makers, researchers and data providers will enhance scientific knowledge and provide the evidence needed to help evaluate and inform firearm policy.