Methodological Challenges to Identifying the Effects of Gun Policies

Summary: Research on the effects of gun policies has a history of producing contradictory results and contentious debates about appropriate research methods. Our review of this literature identified several problems that, if addressed in future research, could result in stronger and more-compelling evidence. These problems—which will chiefly be of interest to researchers familiar with statistical modeling—concern low statistical power and associated errors in the magnitude and direction of effect estimates, poorly calibrated standard errors, inflation of error rates due to multiple testing, problems with the coding of state laws and the time course of policy effects, the interpretation of spline and hybrid model effects, and the possibility of reciprocal causation. We discuss our observations on these problems and propose strategies for addressing them.

A review by the National Research Council (NRC) (2004) highlighted important problems with the methods used in many studies examining the effects of gun policies. Since then, the literature has grown, often in a series of critiques and counter- critiques of the statistical methods used by different sets of researchers. Having carefully reviewed, discussed, and debated among our own project team the relative merits of different methods used in this literature, we offer here our assessment of the principal methodological challenges that future research on gun policy should seek to overcome.

Power

Statistical models using variation in state policies to identify causal effects of gun policies sometimes face serious problems with statistical power, meaning that the models may have little chance to detect effects even when they exist, and any statistically significant effects the models detect are likely to have greatly exaggerated magnitudes and may often get the direction of the effect wrong. These serious problems are common when effects of interest are small relative to other sources of variation in the outcomes (Gelman and Carlin, 2014). This is likely the case for the effects of gun policies (like those we examined in this report) that might affect new purchases of firearms but not the much larger stock of firearms available for use or that might have a modest effect on a small number of firearm incidents.

Nevertheless, even small effects may be important. For example, a 3-percent reduction in firearm deaths corresponds to 1,000 fewer deaths per year nationally. But a 3-percent effect, or an incidence rate ratio (IRR) of 0.97, is small relative to the much larger variation in firearm death rates over time or across U.S. states. Many observations (for instance, years of data for each state) may be required before a model has sufficient power to detect such an effect. Moreover, power is diminished as large numbers of covariates are added to the model.

To illustrate, consider the preferred model reported by one set of researchers reviewed here. The reported effect for one policy was an IRR of 0.97 (confidence interval [CI]: 0.72, 1.15). We can infer from these statistics that such a model could detect a realistically small 3-percent reduction in the outcome at the p < 0.05 level of significance with a power of just 6 percent, well below the 80-percent level researchers typically seek when designing research.[1] Moreover, there is a nearly one in four chance that any statistically significant effect identified is in the wrong direction, and any statistically significant effect the model identifies will necessarily describe an effect size vastly greater than the true effect size. In the present example in which the true effect has an IRR of 0.97, the model would not identify a statistically significant effect any smaller in magnitude than an IRR of about 0.74. That is, the true 3-percent reduction would be found to be significant only if the model estimates it to actually be a 26-percent reduction in the outcome.

In other words, models like some that we find in the existing literature have almost no chance of detecting realistically small effects of firearm policies, and any significant effects the models do discover are likely to be grossly exaggerated in their magnitude and almost equally likely to be in the wrong direction as the right one. While this problem is by no means universally true in this literature, it is common enough that we present it as a general concern rather than citing by name the article from which we drew our example.

Overfitting

The problem of poorly powered models is exacerbated when, as is common in this field, investigators include many covariates and fixed effects in their models of the effects of policies. Most guidance on reliable regression modeling emphasizes that models should have at least ten or 15 times as many observations as parameters being estimated (­Cavanaugh, 1997; Draper and Smith, 1998; Good and Hardin, 2012). However, with fixed effects for each year in time-series data; fixed effects for each state; and a wide range of demographic, social, and economic covariates, models in this field frequently violate such recommendations, sometimes falling below even five observations per parameter (Schell and Morral, 2016). Such models are likely to be overfit, meaning, among other things, that their estimates are unreliable or unlikely to describe generalizable relationships between covariates of interest (such as policies) and the modeled outcomes.

Although problems with statistical power are common in this literature, they may not be inevitable. Models that do a good job explaining sources of variance across time or among states will have more statistical power than those that explain less of this variance. In a separate line of work, RAND’s Gun Policy in America project has examined the performance (power, bias, and error rates) for many gun policy model specifications using simulations for which the true effect of policies is known. This work demonstrates that many statistical models commonly used in gun policy research have quite poor performance in terms of type 1 error, power, and bias but that there are modeling approaches with comparatively good characteristics on these and other criteria.[2]

Standard Errors

Most of the studies meeting our inclusion criteria identified the effects of policies by examining state-level changes in an outcome (such as homicides) over time. In many such models, there is a strong correlation within states among the error terms over time. Whether this clustering of error components mandates some adjustment to ensure that standard errors and even parameter estimates are unbiased has been a source of contention and confusion in the field. According to NRC (2004), cluster adjustments for fixed-effects models like many we reviewed in this report were unnecessary and produced misleadingly large CIs.

As Aneja, Donohue, and Zhang (2014) have argued, however, NRC did not properly consider how serial correlations in panel data can produce misleading standard errors when no adjustments are made for state-level clustering within the data. The authors provided compelling evidence that, without adjustment, standard errors are so severely underestimated that two-thirds or more of effects known to have no systematic association with the outcome variable appear to be statistically significant, a proportion far higher than the 5 percent expected for significance levels set at the p < 0.05 level. They further showed that even a common cluster adjustment procedure does not fully correct the underestimation of standard errors. Although state-level cluster adjustment vastly improves upon unadjusted estimates, standard errors are still inflated, frequently leading to statistically significant null effects at rates between 10 percent and 15 percent where a properly calibrated standard error would produce such errors in only 5 percent of cases.

Longitudinal analyses of state firearm policies that take no steps to address clustering continue to be published, although there is good evidence that the kinds of serial correlation found in state panel data used in gun policy research can result in large biases in estimated standard errors (Aneja, Donohue, and Zhang, 2014). The significance of the effects that these studies report should be regarded with deep skepticism. Similarly, studies frequently use robust standard error corrections or weight the regression models by state or county populations, but neither approach is likely to satisfactorily account for bias resulting from serial correlation, and population weighting could make it worse (Aneja, Donohue, and Zhang, 2014; Durlauf, Navarro, and Rivers, 2016). Further challenges for estimating standard errors arise for studies that use difference-in-differences approaches in which policy effects are identified from only a small number of states (or jurisdictions), because inference based on clustered standard errors has been shown to severely over-reject in these cases (Conley and Taber, 2011; MacKinnon and Webb, 2017).

Multiple Testing

Among studies examining the effects of firearm policies, it is common to present multiple model specifications, each with multiple effect estimates and sometimes run on multiple subsets of the population (e.g., deaths of those under age 19 or over age 55). In some cases, additional models may have been explored using alternative covariates or design characteristics. This type of exploratory modeling is valuable. It clarifies how robust findings are to different aspects of model specification, and it can detect associations or effects that are important but might otherwise have been overlooked.

In the context of such exploratory modeling, however, conventional interpretations of statistical significance erode. Whereas a significant effect at the p < 0.05 level is designed to occur in only one of 20 tests where there is, in fact, no effect, a study that conducts 20 such tests stands a good chance of identifying at least one statistically significant effect, even when no true effects are present. Such accidental statistically significant effects could contribute to the confusing and sometimes contradictory findings reported in the literature.

There are procedures for adjusting levels of statistical significance in the presence of multiple hypotheses testing that could help to reduce erroneous findings (Shaffer, 1995), but these were rarely used in the studies we examined. Moreover, these procedures would not address all sources of questionable findings that can occur in exploratory analysis. Instead, we believe that studies of the effects of state policies should be explicitly treated as exploratory rather than as testing a specific hypothesis. Therefore, strong conclusions about the apparent effects of policies should almost never be made. Instead, effects should be regarded with suspicion until they have been confirmed through independent studies. Because results in this field tend to be sensitive to details of the model specification and covariates, we propose that anyone undertaking such confirmatory analyses preregister the details of their models and data before assembling an analytic data set. Such preregistration does not prevent investigators from making changes to the analytic plan that may become necessary once results become available, but departing from the preregistered plan should signal to the researchers that their analysis should be considered exploratory rather than confirmatory.

Coding State Laws

Gun policy analysts need a reliable and shared database of state laws. There are many well-known problems associated with the coding of state laws. As noted by NRC (2004) and Hahn et al. (2005), there are frequently inconsistencies across studies in the specification of which states or jurisdictions have which laws and when they took effect. In some cases, researchers have used the year in which bills were passed into law as the year the law was implemented; in others, researchers have used the year the law was designed to take effect or the first full year after the law took effect. Although some researchers (e.g., Aneja, Donohue, and Zhang, 2014; Lott and Mustard, 1997; Rosengart et al., 2005; Vernick and Hepburn, 2003) have published or shared their coding of laws, which allows for debate and improvement of the coding schemes, such coding often is not transparent and cannot be reviewed for accuracy or to understand what assumptions about laws were made. More generally, public databases of gun laws over time are unavailable for many laws. Because of the cost and complexity of constructing such data sets, researchers interested in the effectiveness of gun laws have often favored weak, cross-sectional study designs or have collected proprietary data sets of laws that are not shared.

One important assumption that all such efforts necessarily must make concerns the features of different laws that make them sufficiently similar to be grouped together under a broad class of laws. For instance, states differ in whether penalties for violating a child-access prevention law result in criminal, misdemeanor, or civil penalties, and there is evidence (albeit inconclusive) that criminal penalties may have different and stronger effects than other approaches. Such variation in laws and their associated effects means that combining them within a particular class of laws, such as child-access prevention laws, may obscure important effects that some variants of the law have (Alcorn and Burris, 2016). On the other hand, distinguishing each variant of a law reduces the number of jurisdictions implementing any particular version of the law, which reduces the statistical power of most models used to identify the causal effects of the law. Therefore, specification of a homogenous set of laws could increase the average effect size, but it also can reduce the statistical power that models have to detect the larger effects. Rarely, however, have published analyses explicitly addressed this conflict or the choices and assumptions made to address it.

We believe that the science of gun policy will be substantially advanced with the public release of comprehensive state law time-series data, and we have made that one of the goals of the Gun Policy in America project. Specifically, we have assembled a state-law database for 1979–2016 that codes our 13 broad classes of state gun policies and many subcategories. As noted, this database will be available on the Gun Policy in America project website for use and further improvement by the scientific community.

Coding the Time Course of a Policy's Effects

Even with a reliable database of state laws, however, investigators of gun policy effects face a further complication in coding the time course over which gun laws exert their effects. Frequently, investigators assume that a policy’s full effects occur in the year it is implemented or the first full year after the year of implementation. This coding implies that all of a policy’s effect is observed shortly after its implementation, which may be reasonable for some types of policies. Others, however, might accumulate their effects over longer periods. For instance, laws that expand the class of prohibited possessors will primarily affect those members of the class who are seeking to buy new firearms but not those who already own firearms. Indeed, it may be many years before such a law affects firearm ownership of a sizable proportion of the population. The proper coding of this type of effect might involve additive or multiplicative effects over several years.

Similarly, the effects of some policies, such as child-access prevention laws, may not be fully realized until a large proportion of gun owners become aware of them, meaning that the time course of the effect may depend on media campaigns to raise awareness or high-profile prosecutions under the law. Unfortunately, however, unless investigators know when these effects occur, their effect estimates will under­estimate the policy’s true effects. For this reason, we believe that researchers modeling the effects of policies should carefully consider when effects are likely to appear and should make these assumptions and the corresponding model specifications explicit in their analyses.

Spline and Hybrid Effect Coding

Several studies investigating the effects of concealed-carry policies and studies of Australia's 1996 National Firearms Agreement have used model specifications referred to as spline or hybrid models within this field. In most models investigating the causal effects of a policy on an outcome, the effect is assumed to produce a shift in the level of the outcome; for example, a policy may result in a lower homicide rate after implementation relative to before. The type of spline models used in this field differ from standard causal effect models because the policy is assumed to modify the trajectory of the outcome over time rather than the level or in addition to a change in the level. More specifically, these models assume that the states or counties that implement the policy will diverge from the national trend at a constant rate for an indefinite period.[3]

Although we discuss the reported results of these models, for practical and theoretical reasons, we do not present effect sizes from these spline models (or from spline and dummy hybrid models), even when the authors preferred those models. The practical reason is that the effect size is assumed to vary over time, so there is no single effect size to report. In fact, at a date sufficiently long after implementation, these models often assume that the states that implemented the policy will have extremely large or small effects on the outcome. In such cases, the effect size one presents is based entirely on a relatively arbitrary decision about the length of time over which to compute the effect. Moreover, even if we had arbitrarily selected a specific time interval over which to compute the effect, the research articles do not contain the information necessary to assess the CIs around those estimates.

Furthermore, two features of these spline models make them difficult to interpret as the causal effects of a gun policy. First, the spline coefficient is highly sensitive to the timing of any shifts in the outcome, and it responds to the timing in the opposite way as would standard methods for causal inference. A large increase in crime that does not occur until many years after a policy has been implemented will yield a large positive spline coefficient, suggesting that the policy is harmful. However, a similarly large increase in crime that occurs immediately after the policy is implemented will yield a negative spline coefficient, suggesting that the policy is beneficial even though it was followed immediately by an increase in crime.[4] Standard frameworks for inferring causality from observations (e.g., Mill, 1843) would suggest that an increase in crime immediately after the policy was implemented is the strongest evidence that the policy was harmful, and if a similar increase did not occur until years after implementation, it would constitute weaker evidence of a harmful effect of the policy. However, inferring causation from the spline coefficient leads to the opposite inferences, with an immediate increase in the outcome interpreted as the policy causing a decrease in the outcome but a delayed increase interpreted as evidence that the policy caused the outcome to increase. It is important to note that this interpretational challenge occurs in models that use only the spline to indicate the causal effect, as well as in hybrid models that use both a dummy variable and a spline (i.e., a step and a slope). (See the gray box for more information.)

Stated more generally, the direction and size of the spline coefficient serves as an unbiased estimator of the causal effect if, and only if, the duration of the spline’s slope corresponds to the actual period over which the policy’s effects are increasing in magnitude. If the true effect phases in earlier than assumed by the chosen spline function, the spline coefficient will be biased away from the true direction of the causal effect, possibly even reversing the sign of the true effect. Thus, researchers should probably avoid using splines that assume that the effect of the policy increases linearly into perpetuity. Such an assumption makes it likely that the true effect of the policy is in the opposite direction of the spline coefficient.

The second challenge in the interpretation of the spline coefficient as a causal effect comes from the null hypothesis that is typically used when testing the spline coefficient. Specifically, the state-specific linear slope in the outcome with respect to time after the implementation of the policy is compared with the state-specific linear slope over the years prior to implementation. The null hypothesis in this case is that a given state’s deviation from a national trend in the pre-policy period should be expected to continue in a linear manner, absent any intervention, indefinitely. Thus, the null hypothesis being tested is derived from a time trend that has been extrapolated, often many years into the future. This assumption has not been justified within this field, neither with a theory about an underlying data-generating mechanism for which the assumption is appropriate nor by showing that it is a good fit to the available data. In contrast, our analysis of U.S. crime data suggests that the data do not show the pattern predicted by this assumption.[5] Moreover, making an assumption of constant state-specific trends in crime can result in obvious research artifacts. Many types of data show regression to the mean, which describes a pattern of data generated by a random process in which an extreme observation is more likely to be followed by a less extreme observation than a more extreme observation. Failure to account for regression to the mean can result in spurious research conclusions. For example, if legislators pass gun legislation as a response to rising crime rates, any tendency for crime rates to return toward more-typical levels due to regression to the mean may be misinterpreted as evidence that the legislation lowered crime.

The risk of this type of error is much greater in spline models because the assumption used to generate the null hypothesis is that the data display regression away from the mean. Essentially, these models assume a process in which extreme observations are likely to be followed by observations that become progressively more extreme in the same direction—the opposite of regression to the mean. In contrast, in data showing regression to the mean, the null hypothesis that the trend before a given date equals the trend after the date is routinely rejected. That is, the null hypothesis that state-specific deviations from the national crime trend will continue to grow indefinitely can often be rejected in the states that implemented the policy of interest, as well as many of those that did not.[6] Rejecting this implausible null hypothesis is not evidence of a causal effect of any policy.

In spite of clear statistical problems with inferring causal effects of policy on crime data using these methods, some researchers advocate this approach. In our view, their arguments misinterpret conventional effects identified by a shift in the mean (e.g., dummy-coded effects) and spline effects based on changes in slope. For example, Lott, Moody, and Whitley (2016) stated,

The problems with using the dummy variable can be illustrated using results of 3 other papers. Santaella-Tenorio et al. [2016] reported the dummy model from Table 8b of the article by Ayres and Donohue [2003a]. Had they reported the other specification in Table 8b (or other tables) that showed the trends before and after implementation of the law (specifications that reject the assumptions behind the simple dummy approach), they would have shown the statistically significant downward trend in murder rates that indicated that the longer the right-to-carry laws were in effect, the greater the drop in murder rates was.

That is, the three papers interpret the spline coefficient as a “statistically significant downward trend in murder rates.” This is incorrect; the negative spline term indicates that the slope coefficient is of lower value after implementation than before, but it does not imply that rates are actually declining over time either in absolute terms or relative to the other states that did not implement shall-issue (or right-to-carry) laws. It is quite possible to get a negative spline coefficient even if shall-issue laws cause a large and immediate spike in murder. Similarly, such a negative coefficient could occur even if the law has no effect on murder, because it is not reasonable to extrapolate a pre-implementation trend of increasing murder rates indefinitely into the future. Historically, state-specific increases in murder have been followed by later reversion to more-typical values, even without passage of shall-issue laws. Indeed, if the authors’ descriptions of the data as showing progressively larger drops in murder rates over time had been correct, there would have been a lower murder rate after implementation than before. That is, if their descriptions of the data were correct, there would have been a significant negative coefficient on the dummy variable that they dismissed as unimportant, but there may or may not have been a significant negative spline coefficient.

It is important to note that our critique of how spline models have been used in this field is not, in any way, a critique of the use of splines more generally. Splines are extremely general regression tools to allow variations in slopes across a predictor variable. It is entirely reasonable to assume, for example, that the effects of a policy on crime phase in over several years. In such a case, a simple dummy-coded effect may underestimate the true effect size, while using a spline that is designed for that particular phase-in period would not. In our view, using these types of splines to identify a causal effect of policy on some crime outcome would require the following three things:

  1. The model would need to be constructed so that the researchers would not conclude that increases in crime immediately after policy implementation are evidence that the policy lowers crime. This is a typical feature of spline models, particularly when the change in slope is modeled as persisting for a long period. This problem can be limited by using splines whose slopes operate over a narrow time frame, which can be justified as the phase-in period of the policy’s effect (e.g., as used in the preferred specifications in Donohue, 2004). Such splines are similar to dummy-coded variables but with a gradual transition between 0 and 1 rather than an abrupt transition. If the phase-in period is hypothesized to last more than a few years, it may be necessary to estimate a more complex function to avoid making the wrong causal inference.
  2. The null hypothesis that is interpreted as no causal effect must be something that is reasonably true in the absence of the policy in question. The null should be a hypothesis that would not be routinely rejected if tested within states that never implemented the policy or if tested using randomized implementation dates. In practice, this usually requires a null hypothesis that does not extrapolate pre-policy crime trends indefinitely into the future. Instead, the null should be based on deviations from the pre-policy average crime level or on deviations from a state-specific trend that is identified by both pre-implementation and post-implementation crime rates (i.e., based on deviations from an interpolated rather than extrapolated trend).
  3. When regression models contain multiple effects of the policy, such as hybrid models that contain a spline and a dummy variable, the various effects cannot be tested or interpreted independently. The effect size and statistical significance can be assessed only by integrating all of the ways in which the policy influences the outcome within the model. For example, researchers should not claim that a policy is associated with a reduction in crime based on a significant negative spline coefficient when the model includes another effect that simultaneously predicts increased crime following implementation of the policy. Despite the significant negative spline, the model may still predict that the policy is associated with a subsequent increase in crime in all years represented in the data. Thus, while hybrid models can avoid some of the interpretational problems of spline models, any conclusions about the effect of the policy on crime must reflect all of the modeled effects relating the policy to the outcome within the model. Ideally, this analysis would test the effect at some point after the policy is hypothesized to be fully phased in but well within the period that states were typically followed in the data set. This requirement applies to the direction, size, and statistical significance of the joint effect.

Our view of the existing literature is that none of the available studies presents a spline or hybrid model that meets these three requirements for interpreting the effects. Some of the models in the literature meet some of these requirements, but none is readily interpreted as estimating a causal effect of gun policies. For this reason, we generally present the simple dummy-coded causal effect when it is provided by the authors, although we do discuss the authors’ preferred specification in the text.

Simultaneity and Reciprocal Causation

To obtain an unbiased estimate for the causal effect of firearm policy changes, the ideal research design would be akin to a randomized trial in which policies were randomly assigned across states and over time (Aneja, Donohue, and Zhang, 2014; Donohue, 2003). This type of experimental design is infeasible in the context of gun policies, so researchers have had to rely on quasi-experimental methods in which the implicit assumptions require that state adoption of a given firearm policy is unconfounded by omitted factors that influence both law passage and the outcome of interest (i.e., omitted variables bias) and that changes in firearm policy are not themselves driven by changes in the outcome of interest (i.e., simultaneity bias). These issues are not unique to the study of firearm policies and merit consideration across a broad range of program and policy evaluations.

Potential issues of simultaneity have been discussed primarily in the research on shall-issue laws and crime (see more discussion of shall-issue and other concealed-carry laws). Specifically, many studies have noted the potential for reciprocal causation—that is, that state legislatures pass shall-issue laws as a response to high or rising rates of violent crime (Aneja, Donohue, and Zhang, 2014; Grambsch, 2008; Kovandzic, Marvell, and Vieraitis, 2005; Ayres and Donohue, 2003a; ­Donohue, 2003; Manning, 2003; Kovandzic and Marvell, 2003; Plassman and Whitley, 2003; Lott and Mustard, 1997). Indeed, Grossman and Lee (2008) found that the percentage change in the violent crime rate over the preceding five years had a statistically significant positive effect on the likelihood that states with may-issue laws switch to shall-issue laws; Luca, Deepak, and Poliquin (2016) found that the occurrence of a public mass shooting significantly increased the number of firearm bills introduced within a state one year later. If such reciprocal causation exists, the estimated effects of firearm policies on crime rates from the difference-in-differences strategy employed by most of the qualifying studies we identified may be inconsistent and biased, although the direction of such bias is ambiguous. While some studies have tested for potential reciprocal causation and found little evidence of bias driven by differential pre-trends in law-enacting states (Rosengart et al., 2005; Plassman and Whitley 2003), other studies have found this to be an issue of concern for shall-issue laws (Aneja, Donohue, and Zhang, 2014; Grambsch, 2008; Donohue, 2003).

The presence of reciprocal causation complicates causal identification of the true effects of firearm policy changes and requires alternative approaches to those used most commonly in the literature we identified. Unfortunately, some of the existing methods for handling simultaneity problems may not be feasible or may face other limitations. For instance, Lott and Mustard (1997) and Gius (2015a) employ instrumental variables techniques, but the instruments chosen are questionable and neither study provides sufficient evidence to assess instrument validity (Manning, 2003). Synthetic control methods (Abadie, Diamond, and Hainmueller, 2010) have been used to construct a counterfactual “control state” that matches the pre-trend of the law-passing state (Crifasi et al., 2015; Rudolph et al., 2015), but these methods do not readily accommodate inferential statistics and provide estimated effects that are often identified from a policy change in only one state or one state-year, meaning the observed effect is confounded with many other changes in the state that might equally explain any observed differences between the state and its synthetic controls.

More research and methodological innovation is required to address simultaneity and reciprocal causation challenges to causal inference in this and other fields of research. In particular, it would be useful to understand better the factors leading to state or municipal decisions to pass different types of policies. Studies estimating the effects of laws should explore and report whether states that passed the laws differed systematically from those that did not, in terms of their recent gun use or violence trends. In some cases, explorations of the possible effects of reciprocal causation on effect estimates may provide useful insights.

Notes

  1. The inferences about power in this paragraph rely on power calculations and calculations of the probability of an error in the sign of the estimate and the magnitude of the estimate using methods described in Gelman and Carlin (2014). We assume that the standard error of the (unexponentiated) model estimate is (log(IRR) – log(LB))/1.96, where IRR is the reported effect size, and LB is the lower (or higher) bound of the 95-percent CI reported for the estimate. Return to content
  2. A report on this effort is forthcoming and will be available on the Gun Policy in America project website. Return to content
  3. Typically in gun policy models, a spline will be entered as a predictor in a regression equation that takes on values of zero before the policy was implemented (as well as in states that never implemented) and then takes on values that increase linearly in time for a given state once the policy is implemented in that state. For the models used in this field, these state-specific trends are estimated while controlling for national trends by including year fixed effects in the same model. Thus, the splines are state trends that should be interpreted as deviations from the national trend. Return to content
  4. More technically, the spline predictor in the regression equation has a mean value that corresponds to a specific time after implementation. This spline’s mean typically falls a few years after implementation, but precisely when it occurs depends on the number of states that implemented the law and how long the study follows the states. Any increase in crime that occurs before this mean spline creates a more negative spline coefficient. An increase in crime, no matter how large, that occurs at that mean has no effect on the spline coefficient. Any increase in crime that occurs after that mean results in a more positive spline coefficient, with progressively greater leverage over the coefficient occurring with greater time. Return to content
  5. Specifically, the assumption predicts that state trends that deviate from the national trend in a positive direction (increasing crime rates relative to the nation) will continue to get progressively higher over time, while those states that deviate negatively (decreasing crime rates relative to the nation) will continue to decrease indefinitely. This predicts a “fan” pattern in crime trends in which the divergence in crime rates across states perpetually increases over time. Actual crime data do not show any consistent divergence of trends across states. Return to content
  6. For example, imagine that the states that implemented a given policy had an aggregate firearm homicide rate of eight homicides per 100,000 population in the year leading up to implementation and nine homicides per 100,000 in the year prior to that. The null hypothesis based on extrapolating this trend is that the rate of homicides will be seven per 100,000 the year after implementation and will decline to exactly zero homicides within eight years in all of the states that implemented the policy. It is likely that the null hypothesis will be correctly rejected because the states do not actually have zero homicides after eight years, but it would also be rejected because it incorrectly assumed that preexisting trends would continue, unchanged and indefinitely. The null would be rejected for reasons that have nothing to do with any causal effect of firearm policy. Return to content

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  • U.S. General Accounting Office, Firearms Purchased from Federal Firearm Licensees Using Bogus Identification, Washington, D.C., GAO-01–427NI, 2001.
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  • Vernick, J. S., and L. M. Hepburn, “State and Federal Gun Laws: Trends for 1970–1999,” in Jens Ludwig and Philip J. Cook, eds., Evaluating Gun Policy: Effects on Crime and Violence, Washington D.C.: Brookings Institution Press, 2003, pp. 345–402.
  • Vespa, Jonathan, Jamie M. Lewis, and Rose M. Kreider, America’s Families and Living Arrangements: 2012, Current Population Reports, Washington, D.C.: U.S. Census Bureau, P20–570, 2013.
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  • Vigdor, E. R., and J. A. Mercy, “Do Laws Restricting Access to Firearms by Domestic Violence Offenders Prevent Intimate Partner Homicide?” Evaluation Review, Vol. 30, No. 3, 2006, pp. 313–346.
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  • Vittes, K. A., J. S. Vernick, and D. W. Webster, “Legal Status and Source of Offenders’ Firearms for States with the Least Stringent Criteria for Gun Ownership,” Injury Prevention, Vol. 19, No. 1, June 23, 2012, pp. 26–31.
  • Vyrostek, S. B., J. L. Annest, and G. W. Ryan, “Surveillance for Fatal and Nonfatal Injuries—United States, 2001,” MMWR Surveillance Summary, Vol. 53, 2004, pp. 1–57.
  • Wadsworth, T., C. E. Kubrin, and J. R. Herting, “Investigating the Rise (and Fall) of Young Black Male Suicide in the United States, 1982–2001,” Journal of African American Studies, Vol. 18, No. 1, 2014, pp. 72–91.
  • Wallace, Lacey N., “Castle Doctrine Legislation: Unintended Effects for Gun Ownership?” Justice Policy Journal, Vol. 11, No. 2, Fall 2014.
  • Watkins, Adam M., and Alan J. Lizotte, “Does Household Gun Access Increase the Risk of Attempted Suicide? Evidence from a National Sample of Adolescents,” Youth and Society, Vol. 45, No. 3, 2013, pp. 324–346.
  • Webster, D., C. K. Crifasi, and J. S. Vernick, “Effects of the Repeal of Missouri’s Handgun Purchaser Licensing Law on Homicides,” Journal of Urban Health, Vol. 91, No. 2, 2014, pp. 293–302.
  • Webster, D. W., L. H. Freed, S. Frattaroli, and M. H. Wilson, “How Delinquent Youths Acquire Guns: Initial Versus Most Recent Gun Acquisitions,” Journal of Urban Health, Vol. 79, No. 1, 2002, pp. 60–69.
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  • Webster, Daniel W., Jon S. Vernick, and Maria T. Bulzacchelli, “Effects of State-Level Firearm Seller Accountability Policies on Firearm Trafficking,” Journal of Urban Health: Bulletin of the New York Academy of Medicine, Vol. 86, No. 4, 2009, pp. 525–537.
  • Webster, Daniel W., Jon S. Vernick, and Lisa M. Hepburn, “Relationship Between Licensing, Registration, and Other Gun Sales Laws and the Source State of Crime Guns,” Injury Prevention, Vol. 7, 2001, pp. 184–189.
  • Webster, D. W., J. S. Vernick, A. M. Zeoli, and J. A. Manganello, “Association Between Youth-Focused Firearm Laws and Youth Suicides,” JAMA, Vol. 292, No. 5, 2004, pp. 594–601.
  • Webster, D. W., and G. J. Wintemute, “Effects of Policies Designed to Keep Firearms from High-Risk Individuals,” Annual Review of Public Health, Vol. 36, 2015, pp. 21–37.
  • Weil, Douglas S., and Rebecca C. Knox, “Effects of Limiting Handgun Purchase on Interstate Transfer of Firearms,” JAMA, Vol. 275, No. 22, 1996, pp. 1759–1761.
  • Wiebe, Douglas J., “Homicide and Suicide Risks Associated with Firearms in the Home: A National Case-Control Study,” Annals of Emergency Medicine, Vol. 41, No. 6, 2003, pp. 771–782.
  • Wintemute, G. J., D. Hemenway, D. Webster, G. Pierce, and A. A. Braga, “Gun Shows and Gun Violence: Fatally Flawed Study Yields Misleading Results,” American Journal of Public Health, Vol. 100, No. 10, 2010, pp. 1856–1860.
  • Wintemute, G. J., C. A. Parham, J. J. Beaumont, M. Wright, and C. Drake, “Mortality Among Recent Purchasers of Handguns,” New England Journal of Medicine, Vol. 341, No. 21, 1999, pp. 1583–1589.
  • Wintemute, Garen J., Marian E. Betz, and Megan L. Ranney, “Yes, You Can: Physicians, Patients, and Firearms,” Annals of Internal Medicine, Vol. 165, No. 3, 2016, pp. 205–213.
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  • Wright, M. A., and G. J. Wintemute, “Felonious of Violent Criminal Activity that Prohibits Gun Ownership Among Prior Purchasers of Handguns: Incidence and Risk Factors,” Journal of Trauma and Acute Care Surgery, Vol. 69, No. 4, 2010, pp. 948–955.
  • Wright, M. A., G. J. Wintemute, and B. E. Claire, “Gun Suicide by Young People in California: Descriptive Epidemiology and Gun Ownership,” Journal of Adolescent Health, Vol. 43, No. 6, 2008, pp. 619–622.
  • Wright, M. A., G. J. Wintemute, and F. P. Rivara, “Effectiveness of Denial of Handgun Purchase to Persons Believed to Be at High Risk for Firearm Violence,” American Journal of Public Health, Vol. 89, No. 1, 1999, pp. 88–90.
  • Zeoli, A. M., and D. W. Webster, “Effects of Domestic Violence Policies, Alcohol Taxes and Police Staffing Levels on Intimate Partner Homicide in Large U.S. Cities,” Injury Prevention, Vol. 16, No. 2, 2010, pp. 90–95.

View the full project bibliography