American Journal of Criminal Justice

, Volume 37, Issue 4, pp 580–601

Revisiting Licensed Handgun Carrying: Personal Protection or Interpersonal Liability?

Authors

    • Coker College
  • Thomas C. Glover
    • Department of GLIAMurray State University
Article

DOI: 10.1007/s12103-011-9140-4

Cite this article as:
La Valle, J.M. & Glover, T.C. Am J Crim Just (2012) 37: 580. doi:10.1007/s12103-011-9140-4

Abstract

No debate is more sensitive or polemical than the question of “gun rights” in the U.S., and licensing private citizens to carry concealed handguns is the most controversial “right” of all. The morally charged nature of this controversy is reflected in the disparate results reported by various researchers who analyze the effects of these laws, and also by the especially intense methodological scrutiny that follows published research. A National Science Academy review of existing gun policy research issues methodological recommendations which may help resolve scientifically the question of whether or how “right to carry” licensing effects rates of lethal firearm violence. Similar efforts have been published previously, but this study improves upon those earlier efforts by increasing the sample cross-section, by further refining the model specification, and by distinguishing conceptually “shall issue” RTC laws from “may issue” RTC laws. The results provisionally suggest that the former increases homicide rates whereas the latter decreases them.

Keywords

Gun-LawsHomicideGun-Crime

Introduction: “Eye of the Storm”

No controversy is more politically polarized or more hotly debated than the question of “gun rights” in the U.S. Over the past 40 years, innumerable political organizations, legislators and public figures have been calling for either stricter gun regulations on the one hand, or proclaiming the “right of the people to keep and bear arms” on the other, with the empirical question of exactly which types of firearm policies are most effective at preventing lethal violence at the center. Moreover, some argue that the proliferation of firearms is a deterrent to lethal crime whereas others hold that such is the root cause of it (e.g., Lott & Mustard, 1997; Lott, 2000; Kleck 1991, 1997; Wright, Rossi, & Daly, 1983vs. Ayers & Donohue, 2003; Ayers, 2003; Duggan, 2001; Cook & Ludwig, 2003). This controversy is presently dominated by the especially provocative question of whether or how “right to carry” laws (henceforth, “RTC” laws) effect aggregated patterns of fatal interpersonal violence.

RTC laws in particular are exceptionally controversial because they conditionally allow for the personal use of deadly force for defense rather than attempting to indiscriminately reduce incidents of gun violence through Government firearm regulation. Where RTC laws are in force, licensed gun carriers are trusted to use their weapons in strict accord with the law, and only in the most clearly imminent and physically threatening of circumstances. Carriers decide when, where and whether to draw their guns, and also the manner in which to use them. They are legally empowered to protect themselves as they conditionally see fit, and may only be required to legally defend such actions ex post facto. Where public gun carrying is licensed, the Government relinquishes some part of its monopoly on the legitimate use of lethal force by offering eligible citizens the option of protecting themselves with concealed firearms. The debate, then, centers on whether citizens should be allowed to wield such lethal force, and if an armed citizenry is preventative or criminogenic in the aggregate.

Theoretically, there are a number of possible outcomes of RTC laws. They may increase violent crime by proliferating gun carrying among the general population in public settings, or they may reduce violent crime by preventing criminals from attempting to victimize potentially armed individuals. It is also possible that the laws may have no detectable effects in either direction if citizens overwhelmingly decline their “right to carry” a concealed handgun; or, perhaps, the effects of the laws are positive in some jurisdictions, negative in others and non-existent in still others due to presently unknown factors such as urbanization, degree of youth gang infestation etc.

Scientific efforts to evaluate the actual outcomes of RTC laws have been focused and extensive (Ayers & Donahue, 2003; Ayers 2003; Duggan, 2001; Lott & Mustard, 1997; Lott, 2000; Ludwig, 1998; Olson & Maltz, 2001; Plasman & Tideman, 2001; Plassman & Whitely, 2003; Vernick & Hepburn, 2003), but they have failed to resolve the question of what effects, if any, result from RTC laws, primarily because the controversy itself rages around conflicting political and moral ideologies rather than scientific quality per se; demonstrably subjective truth claims are frequently embedded in presumably objective methodological critiques. As a recent Research Council Report (2005) poignantly laments, “little can be decided through argumentation over a—priori beliefs and expectations (p. 121)”. As a result, academics remain firmly split over the question of how or whether RTC laws effect rates of violent crime (e.g., Lott & Mustard, 1997; Lott, 2000; Olson & Maltz, 2001; Plassman & Tideman, 2001; Plassman & Whitely, 2003vs. Ayers & Donohue, 2003; Ayers, 2003; Duggan, 2001; Ludwig, 1998).

Fortuitously, the aforementioned Research Council Report (Wellford, Pepper, & Petrie, 2005) also issued an unusually comprehensive and timely methodological critique of the existing gun policy research, which goes so far as to suggest that traditional approaches should be discarded altogether in favor of alternate yet still unarticulated approaches (p. 151). We hold that traditional research methods may be adopted to account for most of the concerns raised by the Research Council (Wellford et al., 2005), which is the goal of the present study.

The Research Council (Wellford et al., 2005) chiefly raises concerns about (a) unacceptably high levels of aggregation such as states or counties, (b) analytical dependence upon observably unreliable county-level data (see Maltz & Targonski, 2002 for a review), (c) artificial statistical confidence produced by excessively large numbers of non-independent sample units, (d) the sensitivity of policy effects to model specification, (e) questionably short or overly extended post-intervention periods, and finally, (f) differences among the various statistical techniques of gun policy outcome estimation (Wellford et al., 2005, pp. 120–151, 223–230; see also McPhedran & Baker, 2008).

The problem with state or county levels of aggregation is that they are too internally heterogeneous to be inferentially reliable levels of analysis; in states such as Texas or California, for example, the cities of Dallas or Los Angeles are very different places than, say, El Paso or Oakland, and these internal dissimilarities may produce different effects in one city versus another thus obscuring policy effects where states or counties are the units of analysis. Sample unit non-independence reduces standard errors, ergo, produces artificial statistical significance, which means that in such cases one must be especially cautious in accepting policy effects as authentically significant where they are so reported. With respect to model specification sensitivity, the research panel (Wellford et al., 2005) found that adding or removing even a single covariate or control frequently changes the magnitude, direction or statistical significance of the policy effects, thus leaving one unsure whether the effects are actually negative, positive or if they even exist at all. The period of time allotted to observe policy effects is critical, too, since there is no clear answer to the question of how long it should take for a gun policy to exert statistically detectable effects. Finally, the research panel (Wellford et al., 2005, pp. 120–151, 223–230) found that different statistical equations and different estimation models produce different results, which also leaves open the question of which models and which statistical approaches are the most valid (see Wellford et al., 2005, pp. 120–151, 223–230 for a more complete review).

The present study adjusts for the interrelated matters of problematically high levels of aggregation, reliance on county-level data, and sample unit non-independence by conducting a city level analysis that includes parameter estimates to control for sample unit clustering (see Babbie, 2007, p. 367 for methodological support, and also Maltz & Targonski, 2002). Second, model specification is improved by including the widest possible range of covariates and controls from the homicide literature, by then factor indexing them to better control for over specification and collinearity, and by accordingly estimating gun-homicide rates and total homicides rates exclusively to maximize the validity and reliability of the response variable with respect to the overall model specification.1,2 Third, the present post intervention periods naturally vary considerably among the sample units and are extended as far as present data availability will allow. Fourth, the present study compares the results of two different pairs of multivariate estimates to more rigorously evaluate the robustness and stability of the effects (see also McPhedran & Baker, 2008).

The present study also improves upon previous city-level efforts to estimate RTC laws (e.g., La Valle, 2007; 2010) by expanding the sample size considerably and by distinguishing conceptually “shall issue” RTC laws from “may issue” RTC laws. In general outline, the present study estimates the effects of RTC laws on gun homicide rates and total homicide rates for 57 U.S. cities over 27 years with refined model specification, statistical corrections for variation in techniques of policy effects estimation, sample unit independence and serial correlated error terms.3 This is the widest cross-section, the longest series, and the most extended post-intervention period the collective data availability will allow for a city level study.

Literature Review: Conflicting Results and Methodological Disagreement

Between 1980 and 2005, the number of states with RTC laws jumped from 14 to over 40 (NRA.org), which understandably alarmed many, even though the actual effects of the laws remain in dispute. In general, those who support the right to carry concealed handguns hold that guns are much more likely to defend citizens against violent criminals than they are to kill innocent people (Lott & Mustard, 1997; Lott, 2000), and there exists some empirical evidence to suggest that this may be the case.

Kleck and Gertz (1995) controversially reported that there are approximately 2.5 million defensive gun uses annually, but subsequent studies do not confirm that number. Hemenway (1997), for instance, raised strong methodological objections to Kleck and Gertz’s (1995) estimate to argue that the annual rate of defensive gun uses cannot realistically be that high (see Wellford et al., 2005, pp. 110–111 for a more comprehensive review).

In apparent support of Hemenway (1997), McDowall, Colin and Wiersmera (1998) used National Crime and Victimization Survey data from 1992 to 1994 to place the annual number of defensive gun uses at approximately 116,000, which is several times the average reported number of gun-homicides reported per year in the United States since the 1980’s (UCR’s, 1980–2005), but nowhere near the number reported by Kleck and Gertz (1995). The Research Council (Wellford et al., 2005) observes that “much of the confusion surrounding the debate seems to center on what is meant by defensive gun use. Whether one is a defender or a perpetrator, for example, may depend on perspective (p. 106).”

An early effort to estimate the effects of RTC laws on aggregated crime patterns was conducted by McDowall, Loftin and Wierserma (1995) who regressed total homicide rates and gun homicide rates on RTC laws in seven counties from three states over a 20 year period, from 1973 to 1992, except for Miami-Dade which was studied from 1983 to 1992. Their statistical method was an autoregressive integrated moving average (ARIMA) type that controlled for the potentially confounding effects of poverty and age structure, and also controlled diagnostically for the effects of national trends that may influence local effects. Drawing Miami-Dade, Hillsborough and Duval counties from Florida; Multnomah, Clackamas and Washington from Oregon;4 and, Jackson county from Mississippi, they report that the laws most likely do not reduce either outcome, but may actually increase them, and that the effects of the laws varied considerably among the different sample counties.

Employing a much larger sample, Lott and Mustard (1997) estimated two-stage least squares equations (2SLS) to regress various index crime rates on RTC laws in over 3,000 counties. They included every right to carry law adopted between 1977 and 1992, and controlled for a wide array of other possible causes of violent crime. In the main, they concluded (1997) that the laws produced significant reductions in violent crime rates. In a subsequent study, Lott (2000, p. 51) again found that higher gun-levels also reduce violent crime rates, including those for homicide. A counter analysis of the Lott and Mustard (1997) study by Black and Nagin (1998) suggests however that the Lott and Mustard study suffers from a number of model specification errors that may have biased the results, but Moody (2001) checked Lott and Mustard’s (1997) analysis for specification errors, and reported the original model specification to be valid, even though the Research Council (Wellford et al., 2005) was unable to replicate Lott’s results using an updated version of the original database.

Ludwig (1998) holds that Lott and Mustard (1997) fail to control for the fact that RTC laws restrict the minimum age at which one may permissibly carry a concealed handgun, which means that the measured effects of RTC laws, regardless of magnitude or direction, should be theoretically concentrated among adults. Ludwig’s (1998) analysis draws data from all fifty states between 1977 and 1994, it distinguishes juvenile homicides (ages 12–17) from adult homicides (18 +), but it excludes homicides involving children because “they have characteristics that are quite different from those involving older children or adults” (1998, p. 243). Employing a “fixed effects” dummy variable statistical approach and comparing states that adopted RTC laws which those that did not over the specified time period, Ludwig (1998) found that the implementation of RTC laws actually increased adult homicide rates, albeit only slightly.5

Olson and Maltz (2001) sought to further investigate the conceptual, statistical and methodological issues surrounding the increasingly controversial Lott and Mustard (1997) study, and they (2001), too, disaggregated homicide into firearm and non-firearm to determine whether the effects vary accordingly. Using Lott and Mustard’s (1997) data and general research design as baselines, they limited the sampled counties to those over 100,000 in population, which reduced the total sample from over 3,000 to 477.6 Using a dummy variable (1-year) lagged and weight least squares regression technique that regressed the natural log of the two different homicide types on RTC laws, they found that the laws reduced total homicide rates by an average of 7.65%, but that they increased non-firearm homicides by 9.75%, difficult results to interpret.

Plassman and Tideman (2001) hold that the weighted least squares estimates employed by previous researchers (e.g., Lott & Mustard, 1997; Black & Nagin, 1998) are inappropriate because “[they] ignore the fact that crime rates cannot fall below zero [thus biasing the results]”, and that a “Markov chain Monte Carlo analysis of a Poisson lognormal (maximum likelihood ‘count’) model” is preferable (p. 772). Their state (N = 10) analysis found that the effects of RTC laws are variable according to state and crime category. Overall, they (2001) reported (a) that RTC laws generally produce statistically significant reductions in murder rates for most of the sampled RTC states; Florida, Georgia, Idaho, Maine, Mississippi, Montana, Oregon, Pennsylvania, Virginia and West Virginia, (b) that three states in the sample reported statistically significant reductions in rape while the other three reported statistically significant increases, (c) that for robbery, six states reported statistically significant decreases, and (d) that only three states reported significant reduction in all three crime categories. A subsequent study by Plassman and Whitley (2003) using a similar approach also reported that the direction and magnitude of the effects depended upon whether the response variables are property crime rates or violent crime rates; they reported that the effects were mostly negative for violent crimes and mostly positive for property crimes, but only rape and robbery were significant at the .05 level.

Duggan (2001) finds differently than most of the aforementioned RTC studies, and with respect to gun ownership levels as well. By demonstrating that gun magazine sales are a more valid and reliable measure of gun ownership levels than previous measures, Duggan (2001) shows that gun ownership levels are strongly, significantly and positively related to gun homicide rates and total homicide rates on both county and state levels, but that their relationship to robbery, assault, larceny, burglary is less statistically clear. He also demonstrates that counties contained within RTC states do not report lower rates of homicide than counties contained within states that do not.

Two more recent studies estimated the effects of RTC laws on homicide rates and gun-homicide rates at the city level (La Valle, 2007, 2010). Both ran general linear “fixed effects” AR-1 equations, both estimated the same 20 city analytic sample save one city, (New York City was replaced with Buffalo for the 2010 study), and both reported that RTC laws exert no statistically detectable effects on homicide rates or gun homicide rates. Both studies rely on sample cross-sections of just 20 cities, and neither distinguished “shall issue” laws from “may issue” laws.

“Shall Issue” vs. “May Issue” RTC Laws

The validity and reliability of the present study chiefly depends upon the precision of its’ classification of “may issue” RTC laws vs. “shall issue” RTC laws, and this conceptualization may also be the most important contribution this study makes to the existing literature, thus exceptional time and care has been taken to develop this typology as carefully and precisely as possible. In general outline, the present method of classifying RTC laws follows the principles of “legal formalism”, which holds that law operates according to the language and wording that defines and informs it (Turk, 1982).

Following original conceptualizations, “shall issue” RTC laws are those that limit eligibility criteria exclusively to purely objective grounds such as (a) American citizenship, (b) county residency, (c) state citizenship, (d) minimum age requirement, (e) no felony convictions, (f) no pending domestic violence orders, (g) never hospitalized in a mental institution, and (h) certificate of completion of a state certified gun safety course.7 To qualify as a true “shall issue” RTC law for the present study, then, the statute must not include any qualifying language whatsoever, even if the language of the statute also includes “shall issue” phrasing.8 Alternately, RTC statutes which include any qualifying subjective language whatsoever that affords the issuing authority subjective discretion are presently classified as “may issue” types; statutes that contain language which would potentially allow the legal option to refuse an otherwise qualified applicant a permit are presently considered “may issue” types.

Minnesota’s concealed carry statute, for example, asserts that permits may be denied to otherwise qualified applicants if there is a “substantial likelihood exists that the applicant is a danger to self or others” (Minn. Stat. Ann. Sect. 624.714 subd.6 (a) (see Appendix). The actual existence of such a condition is of course subjective, and the statue does not specify exactly how “danger” is defined, or how it may be legally established, thus there necessarily exists discretionary latitude on behalf of the issuing authority.9,10

Even following such careful scrutiny, there were statutes that remained ambiguous as to whether they were “shall issue type, “may issue” types, or even “no issue” types, and these included California, New York and New Jersey. In each of these cases, the statute in question was classified as a “no issue” type even though there exists an RTC statute of some sort “on the books”, and this was done based on the preponderant classifications of previous studies combined with additional outside sources (e.g., NRA.org).

Each statute was researched back to the beginning of the series, 1980, and was traced historically to detect when it first appeared, how it read according to our criteria, and when and if it was perhaps revised before the end of the series, 2006. In most instances, the precise date of adoption was not explicitly indicated, thus the year the law first appeared was coded as the year of adoption, and in all but a very few cases, these years of adoption matched previous RTC studies as well as other credible outside sources (e.g., NRA.org).

In the cases of Colorado, Pennsylvania and Virginia, it was determined that “may issue” RTC laws were in place at the beginning of the series, but that they transitioned to “shall issue” types before the end of the series. To sum, 14 cities in the sample have “may issue” RTC laws, 24 have “shall issue” types, 7 cities transitioned from the former to the latter at some point during the series, and 12 cities have no RTC law whatsoever at any point in the series. Table 1 lists which type of RTC laws exists in which cities and when they were adopted, and the appendix lists the relevant state statute codes.
Table 1

Right to carry laws for sampled cities

Sampled City

State

May Issue

Year Adopted

Shall Issue

Year Adopted

Albuquerque

New Mexico

No

N/A

Yes

2004

Arlington

Texas

No

N/A

Yes

1996

Atlanta

Georgia

Yes

1980

No

N/A

Austin

Texas

No

N/A

Yes

1996

Bakersfield

Californiaa

No

N/A

No

N/A

Baltimore

Maryland

No

N/A

Yes

1972

Birmingham

Alabama

Yes

1975

No

N/A

Boston

Massachusetts

Yes

1936

No

N/A

Buffalo

New Yorka

No

N/A

No

N/A

Chicago

Illinois

No

N/A

No

N/A

Cincinnati

Ohio

No

N/A

Yes

2004

Cleveland

Ohio

No

N/A

Yes

2004

Colorado Spr.

Coloradob

Yes

1981

Yes

2003

Columbus

Ohio

No

N/A

Yes

2004

Corpus Cristi

Texas

No

N/A

Yes

1996

Dallas

Texas

No

N/A

Yes

1996

Denver

Coloradob

Yes

1981

Yes

2003

Detroit

Michigan

Yes

2001

No

N/A

El Paso

Texas

No

N/A

Yes

1996

Fort Worth

Texas

No

N/A

Yes

1996

Greenville

South Carolina

No

N/A

Yes

1996

Honolulu

Hawaii

Yes

1988

No

N/A

Houston

Texas

Yes

1996

No

N/A

Kansas City

Missouri

Yes

2003

No

N/A

Las Vegas

Nevada

Yes

1995

No

N/A

Lexington

Kentucky

No

N/A

Yes

1996

Los Angeles

Californiaa

No

N/A

No

N/A

Louisville

Kentucky

No

N/A

Yes

1996

Memphis

Tennessee

No

N/A

Yes

1996

Mesa

Arizona

No

N/A

Yes

1994

Milwaukee

Wisconsin

No

N/A

No

N/A

Minneapolis

Minnesota

Yes

1980

No

N/A

Mobile

Alabama

Yes

1975

No

N/A

Nashville

Tennessee

No

N/A

Yes

1996

New York

New York

No

N/A

No

N/A

Newark

New Jerseya

No

N/A

No

N/A

Norfolk

Virginiab

Yes

1975

Yes

1995

Oakland

Californiaa

No

N/A

No

N/A

Oklahoma City

Oklahoma

No

N/A

Yes

1995

Philadelphia

Pennsylvaniab

Yes

1973

Yes

1988

Phoenix

Arizona

Yes

1980

Yes

1994

Pittsburgh

Pennsylvaniab

Yes

1973

Yes

1980

Portland

Oregon

Yes

1989

No

N/A

Raleigh

North Carolina

No

N/A

Yes

1996

Riverside

Californiaa

No

N/A

No

N/A

Saint Louis

Missouri

Yes

2003

No

N/A

Saint Paul

Minnesota

Yes

2003

No

N/A

Salt Lake City

Utah

Yes

1986

No

N/A

San Antonio

Texas

No

N/A

Yes

1996

San Diego

Californiaa

No

N/A

No

N/A

San Francisco

Californiaa

No

N/A

No

N/A

San Jose

Californiaa

No

N/A

No

N/A

Seattle

Washington

No

N/A

Yes

1971

Toledo

Ohio

No

N/A

Yes

2004

Tucson

Arizona

No

N/A

Yes

1994

Tulsa

Oklahoma

No

N/A

Yes

1995

Virginia Beach

Virginiab

Yes

1975

Yes

1995

aRTC laws on the books, but interpreted and applied too restrictively to be considered as such

bTransitioned from “may issue” to “shall issue” during year of “shall issue” adoption

Data Collection and Factor Analysis

The data for homicide, gun-homicide and police personnel were obtained from the Uniform Crime Reports (1980–1985), Crime in the United States (1986–2006) and the National Archives of Criminal Justice Data. The poverty, ethnic composition and regional data were obtained from the U.S. Census (1980–2006) and the U.S. Census Supplements (1974–2007). The alcohol availability data were obtained from the U.S. Census of Retail Trade (1977–2002), and the RTC statutes from WESLAW.

Much of the requisite data for the present study is collected during census years only, thus the missing observations have been interpolated according to the straight linear function method (Yafee, 2000, p. 3).11,12 Table 2 reports the univariate descriptive statistics for the census year only data, Table 3 reports the same for the interpolated data, and both tables report both the logged and non-logged versions. All four sets are reported to show that logging improved the distributions and to show the similarities between the census year only distributions and the interpolated distributions.
Table 2

Descriptive statistics for continuous variables for census years only variables (N = 228)

Original Variable

Non-Logged Distributions

Logged Distributions

Logged Variable

Mean

Std.

Skew

Mean

Std.

Skew

Populationa

738.72

1087.78

4.77

6.19

.793

.825

LogPop

Number of liq. stores

198.36

247.85

3.65

4.77

1.03

−.131

LogALC1

Number of bars

98.50

146.83

4.08

4.04

.999

.355

LogALC2

Persons per square mile

4.86

4.34

2.12

1.24

.835

.000

LogPopD

Percent of pop. renting

47.26

8.98

.962

3.84

.182

.393

LogRent

Med. family Incomea

36.39

14.50

.461

3.51

.421

−.300

LogFmInc

Med. house-hold incomea

30.42

12.51

.591

3.32

.438

−.321

LogHseInc

Number of patrol officers

2180.01

4528.30

5.81

7.04

.977

.784

LogPolice

Patrol officers per resident

2.49

.933

.930

.845

.358

.249

LogPolPer

Patrol officers per sq. mile

14.47

18.38

2.87

2.09

1.07

.273

LogPolPsm

Less than HS education

23.46

10.81

.835

3.05

.470

−.172

LogLTHS

Percent female head. house.

29.01

8.67

.303

3.32

.311

−.327

LogFemHed

Ind. Poverty percentage

17.38

5.44

.184

2.80

.340

−.588

LogIndPov

Fam. poverty percentage

13.90

5.21

.400

2.56

.401

−.409

LogFamPov

Percent pop. Black

24.30

19.37

.856

2.78

1.01

−.550

LogBlack

Percent pop. Hispanic

15.15

15.91

1.41

2.08

1.24

−.182

LogHispan

Gun homicide rate

10.84

8.82

1.19

2.01

.942

−.640

LogGunHom

Total homicide rate

16.73

12.11

1.18

2.55

.771

−.308

LogTotHom

aMeasured in thousands

Logged and non-logged versions both reported to show improved distributions—only the logged versions are used for analysis

Table 3

Descriptive statistics for continuous variables for interpolated variables (N = 1539)

Original Variable

Non-Logged Distributions

Logged Distributions

Logged Variable

Mean

Std.

Skew

Mean

Std.

Skew

Populationa

738.77

1073.44

4.69

6.20

.787

.825

LogPop

Number of Liquor strs.b

194.56

238.79

3.51

4.77

1.02

−.129

LogALC1

Number of barsb

98.45

142.30

4.02

4.03

.994

.349

LogALC2

Persons per square mile

4.85

4.33

2.06

1.24

.831

.027

LogPopD

Percent of pop. renting

47.46

8.85

.937

3.84

.178

.384

LogRent

Med. family Incomea

35.19

11.94

.703

3.50

.341

−.097

LogFmInc

Med. house-hold incomea

29.58

10.43

.762

3.32

.355

−.132

LogHseInc

Number of patrol officers

2152.92

4453.20

5.70

7.03

.959

.913

LogPolice

Patrol officers per resident

2.45

.905

1.12

.833

.344

.373

LogPolPer

Patrol officers per sq. mile

14.28

18.12

2.60

2.08

1.06

.322

LogPolPsm

Less than HS education

23.64

9.69

.666

3.08

.427

−.302

LogLTHS

Percent female head. house.

29.81

8.24

.231

3.35

.289

−.363

LogFemHed

Ind. Poverty percentage

17.38

5.25

.147

2.81

.327

−.602

LogIndPov

Fam. poverty percentage

13.82

5.07

.375

2.55

.390

−.375

LogFamPov

Percent pop. Black

23.88

19.01

.891

2.77

.999

−.540

LogBlack

pop. Hispanic

14.72

15.74

1.55

2.04

1.23

−.124

LogHispan

Gun homicide rate

10.77

8.89

1.46

2.03

.888

−.426

LogGunHom

Total homicide rate

16.46

11.74

1.31

2.55

.749

−.408

LogTotHom

aMeasured in thousands

bOriginally ratios per square mile and/or per resident, but found to be invalid measure

Logged and non-logged versions both reported to show improved distributions—only the logged versions are used for analysis

All but two of the continuous covariates—LogBlack and LogHispan—are factor analyzed constructs developed from the original univariate measures.13,14 Table 4 reports which uni-dimensional variables were combined with which others and the resulting factor loadings and reliability coefficients (Alpha) of each factor indexed variable or covariate included in the final model specifications (see again footnote #8 herein). For the treatments, “ShallRTC” designates “shall issue” RTC laws whereas “MayRTC” designates “may issue” RTC laws. In response to the panel report (Wellford et al., 2005), “Nested” is a dummy variable that indicates whether a city is located in a state with another city in the sample, and is a control for sample unit non-independence. Finally, all of the treatment variables and categorical dummy variables are coded “1” for yes and “0” for no.
Table 4

Factor analyzed variable combinationsa

Census Years Only

With Interpolated Data

Logged Variable

Factor Loadings

Alphab

Factor Loadings

Alphab

New Variable

LogALC1

.933

 

.934

  

LogALC2

.933

.850

.934

.854

ALCOHOL

LogPop

.774

 

.777

  

LogPopD

.897

 

.893

  

LogRent

.756

.737

.761

.739

DENSITY

LogFmInc

.998

 

.994

  

LogHseInc

.998

.995

.994

.988

INCOME

LogPolice

.881

 

.876

  

LogPolPer

.890

 

.887

  

LogPolPsm

.929

.883

.928

.879

POLICE

LogLTHS

.722

 

.725

  

LogFemHed

.809

 

.833

  

LogIndPov

.917

 

.929

  

LogFamPov

.925

.838

.941

.880

POVERTY

aVermax rotation method

bCronbach’s based on standardized items

Model Specification: Factorial Determinants of Homicide

Each of the control variables and covariates chosen for the present study were taken from the homicide literature where they have been variously identified as probable determinants of homicide. The main categorical control included presently is the U.S. census region within which each city is located—(a) Northeast, (b) Midwest, (c) South, and (d) West. Messner (1983) tested the “southern sub-culture of violence” hypothesis and found that southern regions may exert statistically significant effects on homicide rates due to higher firearm ownership levels even when other important factors such as race are controlled. In response, Dixon and Lizotte (1987) agree that violent crimes such as homicide may be a result of a “subculture of violence”, but that this relationship is not necessarily specific to the south and is unrelated to firearm ownership levels.

The continuous covariates and controls included in the final model specifications estimated presently include (a) alcohol outlet density—“ALCOHOL”, (b) population density—“DENSITY”, (c) average income—“INCOME”, (d) police presence—“POLICE”, (5) proportion below the poverty line—“POVERTY”, (e) the natural logarithm of the proportion of the population Black—“LogBlack”, and (f) the natural logarithm of the proportion of the population Hispanic—“LogHispanic”. These variables, too, have been variously identified by the homicide literature as determinants of homicide.

Parker (1995) posited that, due to socially disorganizing effects of alcohol consumption, alcohol availability may be positively associated with violent crime, and he confirms statistically that alcohol outlet density (“availability”) is positively and significantly associated with rates of violent crime, gang activity and homicide rates. Alaniz, Luisa, Cartmill, and Parker (1998) similarly found that homicide rates are higher in neighborhoods where alcohol availability is higher controlling for other important factors such as income inequality.

Population density is equally prevalent in the homicide literature, but is almost invariably employed as a control, which seems appropriate since denser forms of social organization such as prison populations and juvenile facilities frequently suffer from greater internal social tensions and greater social disorganization which may lead to increased incidents of lethal interpersonal violence (see Tartato & Levy, 2007 for a thorough review of the relevant literature). La Valle’s (2007) city level study of RTC laws and the Brady law also found population density to be statistically significant controlling for other possible determinants of homicide.

Numerous homicide studies have reported that income inequality is detectably associated with homicide rates in a community. Almgren, Guest, Immerwhar, and Spittel (1998) found that joblessness is positively related to homicide rates controlling for both race and gender. Crutchfield (1989), too, found that income inequality is associated with homicide rates controlling for unemployment and poverty rates. Harrer and Steffenshmeir (1992) also reported that income inequality strongly affects the relationship between inter-racial homicide rates. Messner (1983) similarly found that economic opportunities significantly influence rates of interracial homicide.

Police presence has been controlled in previous multivariate estimates of the effects of other important determinants of violent death, as a number of homicide studies demonstrate. Grant, Sherman, and Martinez (1997) found police expenditures to be a statistically significant correlate of homicide controlling for population size, inflation index, unemployment rate, and unionization. Harer and Steffensmeier (1992) actually found police presence to be positively correlated with violent crime rates, which is consistent with the findings of La Valle’s (2007, 2008 & 2010) studies of the effects of gun policies on homicide rates in 20 of the largest cities in the U.S..

Few variables are as widely accepted as poverty as a determinant of homicide, and the confirmatory research stretches back over 40 years. Parker and Smith (1979) found that poverty rates controlling for age structure are robustly and positively correlated with incidents of primary homicide. For a sample of 125 statistical metropolitan areas, Williams (1984) similarly found that poverty is positively correlated to homicide, but that region exerts an additional effect. Bailey (1984), too, found that poverty exerts a statistically significant effect on most violent crimes, including murder. In addition, the most recent city-level estimates of the effects of gun policies on homicide rates consistently find that poverty exerts an especially robust effect on both outcomes controlling for alcohol availability, population density, and police presence (La Valle, 2007, 2008, 2010).

Ethnic composition has also been found to be a factorial determinant of homicide controlling for other factors. Analyzing data for Columbus, Ohio in 1990, Kirvo and Peterson (1996) reported that racial differences reflected in structural inequality accounts for black-white differences in violent criminality. Krivo, Peterson, Rizzo, and Reynolds (1998), too, found that racial inequality produces racially segregated concentrations of community disadvantage which, in turn, lead to increased rates of violent crime including homicide. Harer and Steffensmeier (1992) found that the effects of economic inequality are different for Blacks than for Whites, and that these effects are actually greater for Whites than for Blacks.

Gun Policy and Homicide

There are five methodological reasons why gun homicide rates and total homicide rates are the measured outcomes for the present study, and the corresponding justifications are reliability, validity or generalizability based. First, the validity of the present model specification has been maximized by including the widest range possible of variables from the homicide literature (review previous section) in the final multivariate analyses; the variables included in the final estimates are those identified to be factorial determinants of homicide.

Second, since the dependent variable is regressed on the independent variables, the reliability and validity of the D.V is most critical to the validity of multiple regression analyses. Homicide is the most reliably identified and reported of all index crimes; whereas other violent crimes such as, say, rape, assault or even burglary are frequently subject to various situational ambiguities or investigational contingencies, the victim is always found deceased or at least permanently missing in cases of a homicide.

Third, the Uniform Crime Reports only record the most serious crime in cases of multiple offenses, which means that official measures of homicide and gun-homicide necessarily capture incidences of “felony murder”, an overall rate which should decrease if criminals are deterred by potentially armed victims, but increase if RTC laws introduce criminal homicide. Moreover, then, RTC laws should exert stronger, more significant and more reliable effects, regardless of direction, on homicide rates and gun-homicide rates as compared to other index crimes (see Marvell & Moody, 1995, p. 250).15

Fourth, the present study does not disaggregate homicide rates into general type or offender-victim relationship in the interest of generalizability. True, RTC laws are more likely to affect some types of homicide more than others (see Ludwig, 1998 for a complete review), but the larger question in our view is whether the net effect of these laws are lives saved, people killed or neither.

Fifth and finally, gun homicide rates and total homicide rates are the most common outcomes measured by previous gun-policy analyses to include the RTC studies reviewed presently (see especially McDowall, Loftin, & Wierserma, 1995; Olson & Maltz, 2001; Plassman & Tideman, 2001; Plassman & Whitely; La Valle, 2007, 2008, 2010 for a review and justification), and the importance and validity of this outcome is not challenged by the National Science Academy Panel (Wellford et al., 2005:121–223).

Sample and Statistics

The present study is a naturalistic quasi-experimental multivariate pooled time-series research design. The analytic sample consists of 57 cities (Table 1), and the series spans 27 years–1980 through 2006. It employs dual estimation models, fixed effects for each unit observation, correction for serial correlation of error and controls for sample unit non-independence. Two pairs of models are estimated; both (a) employ “fixed effects” for each city and year, both (b) include a homogeneous first-order auto-regressive covariance structure,16 both (c) estimate the same analytic sample over the same overall time period, both (d) include the same covariates and controls, and both (e) evaluate the effects RTC laws may or may not exert on gun homicide rates and total homicide rates exclusively. The first pair estimate the effects of RTC laws using the available census data only, whereas the second pair are weighted according to population size and include the interpolated data observations.17

A comparison of the first pair of estimates with the second pair provides a means of determining if the inclusion of the interpolated observations alters the direction or magnitude of any of the coefficients, and if it affects the magnitude of the covariance structure coefficient (“rho” statistic). Such changes would suggest that the interpolated observations are somehow problematic, whereas no such changes would provisionally confirm that they are not. This comparison also provides a method of evaluating the robustness of the results; if the treatment variables are only significant for the interpolated models, that would obliquely confirm that the effects of RTC laws are not robust as the National Science Academy Report suggests (Wellford et al., 2005). None of the estimates have been lagged in accord with Marvell and Moody (2008) who observe that lagging “can bias the results if few time periods are used” (p. 361).18

Results

The present research design addresses the main concerns of the National Science Academy report (Wellford et al., 2005), but in so doing, it is forced into one particular methodological choice that should be evaluated before examining the results. The imputation of interpolated observations increase both the sample size and the power of the current design (the observations for homicide and gun homicide rates are not interpolated), which could overstate the statistical significance of the policy variables. For the same reason, the magnitude of the auto-regressive coefficients should also be considered with additional caution. Tables 5 and 6 estimates the policy effects for census years only and Tables 7 and 8 reports the weighted and interpolated effects.
Table 5

Estimates for census years only

“Fixed Effects” Gun Homicide Model

Parameter

Estimate

Std. Error

MayRTC

−.304*

.124

ShallRTC

.029

.098

Nested

.111

.121

NorthEast

−.813*

.210

MidWest

−.681*

.190

South

−.610*

.160

West

0aa

0

LogBlack

.690*

.069

LogHispan

.190*

.048

ALCOHOL

.000

.080

DENSITY

−.160*

.069

INCOME

−.262*

.049

POLICE

.162

.094

POVERTY

.109

.061

AR−1 = .72

2LL = 337.93

*P < .05

aRedundant

Table 6

Estimates for census years only

“Fixed Effects” Total Homicide Model

Parameter

Estimate

Std. Error

MayRTC

−.231*

.102

ShallRTC

−.093

.080

Nested

.008

.101

NorthEast

−.682*

.177

MidWest

−.522*

.161

South

−.459*

.134

West

0aa

0

LogBlack

.528*

.060

LogHispan

.108*

.039

ALCOHOL

.021

.066

DENSITY

.097

.059

INCOME

−.229*

.040

POLICE

.129

.081

POVERTY

.154*

.049

AR−1 = .48

2LL = 242.58

*P < .05

aRedundant

Table 7

Weighted estimates w/interpolated data

“Fixed Effects” Gun Homicide Model

Parameter

Estimate

Std. Error

MayRTC

−.263*

.080

ShallRTC

.274*

.075

Nested

.131

.088

NorthEast

−.954*

.141

MidWest

−.713*

.133

South

−.590*

.116

West

0aa

0

LogBlack

.724*

.062

LogHispan

.168*

.039

ALCOHOL

.009

.039

DENSITY

−.028

.047

INCOME

−.168*

.034

POLICE

.018

.050

POVERTY

.214*

.057

AR−1 = .80

2LL = 1236.71

*P < .05

aRedundant

Table 8

Weighted estimates w/interpolated data

“Fixed Effects” Total Homicide Model

Parameter

Estimate

Std. Error

MayRTC

−.214*

.065

ShallRTC

.206*

.080

Nested

.038

.073

NorthEast

−.796*

.116

MidWest

−.569*

.110

South

−.447*

.095

West

0aa

0

LogBlack

.538*

.051

LogHispan

.115*

.032

ALCOHOL

.045

.032

DENSITY

.012

.038

INCOME

−.197*

.027

POLICE

.015

.040

POVERTY

.184*

.046

AR−1 = .81

2LL = 541.45

*P < .05

aRedundant

Both tables report that the homogeneous first order auto-regressive co-variance structure is a reasonable correction for serial correlated error terms; AR-1 = .72, .48, .80 and .81, respectively. That the coefficient for the non-interpolated total homicide model (Tables 5 and 6, right hand column) is substantially lower than the others is somewhat troublesome and perhaps a bit difficult to interpret. This result could suggest that the magnitudes of the autoregressive coefficients for the interpolated estimates are an artifact of the interpolation itself, but the other three estimates are consistent in this regard, which differently suggests that the interpolated data may not present a problem at all. Compounding the matter somewhat is that “ShallRTC” changes in direction between the gun homicide estimates and the total homicide estimates (Tables 5 and 6), and in both magnitude and significance with the addition of the interpolated observations (Tables 7 and 8).

For the controls, all of the census regions are significant, in the same direction and of very similar magnitude throughout. In each and every case, there is a strong negative correlation between census region and the outcomes. “Nested” reports that whether a city is clustered with other cities in the same state is insignificant. It may be that the considerable attention that has been paid to sample-unit non-independence is somewhat misguided (Wellford et al., 2005), and that Moody (2001) is correct that Lott and Mustard’s (1997) original model specification is valid.

The ethnic composition variables—LogBlack and LogHispan--are also quite stable; all are in the same direction, of much the same general magnitude, and statistically significant throughout. In the case of local effects, the results are equally consistent among all four estimates. “ALCOHOL”, “DENSITY” and “POLICE” are insignificant throughout, whereas both “POVERTY” and “INCOME” remain consistently significant and directionally stable throughout.

One would expect effects to gain statistical significant with the larger sample size, and such is the case with respect to “ShallRTC” but not “MayRTC”. The effects of “ShallRTC” are not significantly different from zero for the census years only estimates, but they are so for both interpolated estimates. “MayRTC”, on the other hand, reports very stable and statistically significant effects throughout, and the magnitudes are actually slightly larger for the census year only estimates than for the interpolated estimates. Weighting proportional to population size generally reduces standard errors for the treatments somewhat, suggesting that smaller cities display somewhat greater variability than large cities.

Conclusions

There are two important conclusions to be drawn from the present study, one methodological and the other substantive. The substantive conclusion to be drawn from the present study is that “may issue” RTC laws robustly and consistently reduce homicide rates by roughly 20 to 30%, whereas “shall issue” laws may conversely increase these same outcomes by a similar margin, although the stability and significance of the effects of the latter are a bit less clear presently (Tables 5 and 6vs. Tables 7 and 8). Moreover, RTC laws reduce incidents of interpersonal lethal violence, but only if the issuing authorities are allowed to exercise at least some discretion beyond the objective legal licensing criteria. When and where the issuing authorities are not allowed discretion, the effects seem to be as “right to carry” critics suggest—more people die (e.g., Ayers & Donohue, 2003; Ayers, 2003; Cook & Ludwig, 2003; Duggan, 2001; Ludiwg et al., 1998).

The methodological conclusion to be drawn from the present study is that future RTC research should further refine and conceptually account for the critical distinction between “shall issue” RTC laws and “may issue” RTC laws. This distinction is not only important to better understanding the effects of these laws, but it also may resolve the question of the robustness of the effects, a question to which the National Science Academy Report devotes a great deal of effort (Wellford et al., 2005, p. 139–151). Indeed, the previous studies that have employed similar esearch methodologies most similar to the present study but failed to distinguish “shall issue” types from “may issue” types (e.g., La Valle, 2007, 2010) reported the effects of these laws to be statistically non-existent.19

Finally, acceptance of the present methodology should not be interpreted to mean that the present study is necessarily superior to past RTC studies; the present study is merely a modest attempt to estimate RTC outcomes according to the recommendations issued by a National Academy Report (Wellford et al., 2005), and to distinguish “may issue” effects from “shall issue” effects. To be clear, the present conceptualizations and methodology are both open to discussion, as is the case for all published research.

Footnotes
1

See pages 15–18 under “Model Specification: Factorial Determinants of Homicide” for a complete review.

 
2

Sex ratio and age are commonly found in the homicide literature, but both are absent from the present study due to lack of association and insignificance throughout

 
3

The Science Academy Report (2005:121) “…concludes that, in light of (a) the sensitivity of the results to seemingly minor changes in model specification, (b) a lack of robustness of the results to the inclusion of more recent years of data, and (c) the imprecision of the results, it is impossible to draw strong conclusions from the existing literature on the causal impact of these laws”. In response, the present study (a) further refines the model specification over previous efforts (eg., La Valle, 2007; 2010), (b) extends the post intervention periods to the most recent data point presently possible—2006, and (c) combines, compares and evaluates the results of dual statistical estimates to better evaluate the stability and robustness of the effects.

 
4

The three counties from Oregon were combined into a single analytic unit.

 
5

The disparities between Ludwig’s results and Lott and Mustards may also be due to differences in sample size and length of the post intervention periods.

 
6

See Olson and Maltz (2001:753–55) for extensive justification for this approach.

 
7

There is some variability regarding these criteria.

 
8

Most previous discussions classify any RTC laws with “shall issue” language as a “shall issue” type regardless of the presence of subjective qualifying language.

 
9

We hold that ours is the most objective methodology possible in this particular regard.

 
10

We recognize that some will variously disagree with our RTC conceptualization methods, and may therefore reject the present study outright. But it should be noted that there is no single “authoritative” classification scheme presently available. For example, the Research Council (2005, p. 122) footnotes that “…Lott and Mustard (1997) classify North Dakota as having adopted such [RTC] laws prior to 1977, but Vernick and Hepburn (2003) code these states as adopting them in 1985. Likewise, Lott and Mustard (1997) classify Alabama and Connecticut as having right-to-carry laws prior to 1977, yet Vernick and Hepburn (2003) codes these states as not having right-to-carry laws.” The present study agrees that Alabama has a RTC law, but that it is a “may issue” type rather than a “shall issue” type, which also disagrees with the National Rifle Association evaluation of Alabama’s RTC law (NRA.org).

 
11

This approach is in part a response to Ayers and Donahue (2003) critical objection to “spline” models.

 
12

Total homicide rates and gun homicides rates NOT interpolated.

 
13

The major advantages of this approach are that it (a) automatically pre-standardizes the coefficients, it (b) reduces substantially the total number of parameter estimates, it (c) resolves collinearity problems, it (d) reports the reliability of the underlying construct, and (e) it allows for more refined and valid model specifications.

 
14

No combination of either of the two ethnic composition variables with any of the others could be justified theoretically or statistically, so each measures a different dimension of “ethnic composition”, respectively (see again Cao, Adams, & Jensen, 1997; Covington, 1999; Crutchfield, 1989).

 
15

Lott and Mustard (1997), Olson and Maltz (2001), Ludwig (1998), Plassman and Tideman (2001), Plassman and Whitley (2003) and Vernick and Hepburn (2003) all report that the effects of RTC laws vary considerably according to whether the measured outcomes are property crimes, violent crimes, gun related or non-gun related. In addition, it is the lethality of guns that concern the public, researchers and policy makers. For these reasons, the measured outcomes for the present study are homicide rates and gun homicides rates.

 
16

The “fixed effects” approach is due to the non-random sample, general linear models were chosen over general estimating equations due to better fit statistics, and the homogeneous auto-regressive covariance structure was chosen over the heterogeneous type due to stronger “rho” statistics.

 
17

A multi-wave panel design was originally planned as a supplement to the pooled estimates, but we found that the single-city samples were too small and too unstable to really believe the results. Moreover, there was very little within city variation of the controls and covariates, within city trends were extraordinarily high and therefore the significance values were likely invalid.

 
18

The non non-interpolated estimates include only 4 time periods total, and some of the jurisdictions included in the sample only enacted RTC laws within 2 or 3 years prior to 2006, therefore lagging would effectively eliminate at least a few post-intervention periods entirely from the analysis for the non-interpolated estimates, and shorten them to only a year-or-two for the interpolated estimates.

 
19

All four equations were estimated with “shall issue” and “May issue” RTC laws lumped together conceptually, and the results of these effects were not significantly different from zero for any of them.

 

Copyright information

© Southern Criminal Justice Association 2011