More Guns Less Crime

by John R. Lott Jr

  Criticisms of the Original Study

  A second line of attack came from academic, quasi-academic, and gun-control advocacy groups concerning the competence with which the study was conducted. Many of these objections were dealt with somewhere in the original study, which admittedly is very long. Yet it should have been easy enough for critics—especially academics—to check.

  The attacks have been fairly harsh, especially by the standards of academic discourse. For example,

  "They highlight things that support their hypothesis while they ignore things contrary to their hypothesis," said Daniel Webster, an assistant professor at Johns Hopkins University Center for Gun Policy and Research.

  "We think the study falls far short of any reasonable standard of good social science research in making [their] case " said economist Daniel

  THE POLITICAL AND ACADEMIC DEBATE/129

  Nagin of Carnegie-Mellon University, who has analyzed Lott's data with colleague Dan Black. 17

  I have made the data I used available to all academics who have requested them, and so far professors at twenty-four universities have taken advantage of that. Of those who have made the effort to use the extensive data set, Dan Black and Daniel Nagin have been the only ones to publicly criticize the study.

  The response from some academics, particularly those at the Johns Hopkins Center for Gun Policy and Research, has been highly unusual in many ways. For instance, who has ever heard of academics mounting an attack on a scholarly study by engaging in a systematic letter-writing campaign to local newspapers around the country? 18 One letter from a citizen to the Springfield (Illinois) State Journal-Register noted, "Dear Editor: Golly, I'm impressed that the staff at Johns Hopkins University reads our local State Journal-Register. I wonder if they subscribe to it." 19

  The rest of this chapter briefly reviews the critiques and then provides my responses to their concerns. I discuss a number of issues below that represent criticisms raised in a variety of published or unpublished research papers as well as in the popular press:

  1 Is the scale of the effect realistic?

  Large reductions in violence are quite unlikely because they would be out of proportion to the small scale of the change in carrying firearms that the legislation produced. (Franklin Zimring and Gordon Hawkins, "Concealed-Handgun Permits: The Case of the Counterfeit Deterrent," The Responsive Community [Spring 1997]: 59, cited hereafter as Zimring and Hawkins, "Counterfeit Deterrent")

  In some states, like Pennsylvania, almost 5 percent of the population has concealed-handgun permits. In others, like Florida, the portion is about

  2 percent and growing quickly. The question here is whether these percentages of the population are sufficient to generate 8 percent reductions in murders or 5 percent reductions in rapes. One important point to take into account is that applicants for permits do not constitute a random sample of the population. Applicants are likely to be those most at risk. The relevant comparison is not between the percentage of the population being attacked and the percentage of the entire population holding permits, but between the percentage of the population most vulnerable to attack and the percentage of that population holding permits.

  Let us consider some numbers from the sample to see how believable

  these results are. The yearly murder rate for the average county is 5.65 murders per 100,000 people, that is, .00565 percent of the people in the average county are murdered each year. An 8 percent change in this murder rate amounts to a reduction of 0.0005 percent. Obviously, even if only 2 percent of the population have handgun permits, that 2 percent is a huge number relative to the 0.0005 percent reduction in the murder rate. Even the largest category of violent crimes, aggravated assault, involves 180 cases per 100,000 people in the average county per year (that is, 0.18 percent of the people are victims of this crime in the typical year). A 7 percent change in this number implies that the assault rate declines from 0.18 percent of the population to 0.167 percent of the population. Again, this 0.013 percent change in the assault rate is quite small compared to the observed changes in the number of concealed-handgun permits.

  Even if those who carry concealed handguns face exactly the same risk of being attacked as everyone else, a 2 percent increase in the portion of the population carrying concealed handguns seems comparable to the percentage-point reductions in crime. Bearing in mind that those carrying guns are most likely to be at risk, the drop in crime rates correlated with the presence of these guns even begins to seem relatively small. Assuming that just 2 percent of the population carries concealed handguns, the drop in the murder rate only requires that 0.025 percent of those with concealed-handgun permits successfully ward off a life-threatening attack to achieve the 0.0005 percent reduction in the murder rate. The analogous percentage for aggravated assaults is only 0.65 percent. In other words, if less than seven-tenths of one percent of those with concealed handguns successfully ward off an assault, that would account for the observed drop in the assault rate.

  2 The importance of "crime cycles"

  Crime rates tend to be cyclical with somewhat predictable declines following several years of increases... . Shall-issue laws, as well as a number of other measures intended to reduce crime, tend to be enacted during periods of rising crime. Therefore, the reductions in violent crime ... attribute^] to the implementation of shall-issue laws may be due to the variety of other crime-fighting measures, or to a commonly observed downward drift in crime levels towards some long-term average. (Daniel W. Webster, "The Claims That Right-to-Carry Laws Reduce Violent Crime Are Unsubstantiated " The Johns Hopkins Center for Gun Policy and Research, copy obtained March 6, 1997, p. 1; cited hereafter as Webster, "Claims")

  Despite claims to the contrary, the regressions do control for national and state crime trends in several different ways. At the national level, I

  THE POLITICAL AND ACADEMIC DEBATE/131

  use a separate variable for each year, a technique that allows me to account for the changes in average national crime rates from one year to another. Any national cycles in crime rates should be accounted for by this method. At the state level, some of the estimates use a separate time trend for each state, and the results with this method generally yielded even larger drops in violent-crime rates associated with nondiscretionary (shall-issue) laws.

  To illustrate that the results are not merely due to the "normal" ups and downs for crime, we can look again at the diagrams in chapter 4 showing crime patterns before and after the adoption of the nondiscretionary laws. The declines not only begin right when the concealed-handgun laws pass, but the crime rates end up well below their levels prior to the law. Even if laws to combat crime are passed when crime is rising, why would one believe that they happened to be passed right at the peak of any crime cycle?

  As to the concern that other changes in law enforcement may have been occurring at the same time, the estimates account for changes in other gun-control laws and changes in law enforcement as measured by arrest and conviction rates as well as by prison terms. No previous study of crime has attempted to control for as many different factors that might explain changes in the crime rate.

  3 Did I assume that there was an immediate and constant effect from these laws and that the effect should be the same everywhere?

  The "statistical models assumed: (1) an immediate and constant effect of shall-issue laws, and (2) similar effects across different states and counties." (Webster, "Claims," p. 2; see also Dan Black and Daniel Nagin, "Do 'Right-to-Carry' Laws Deter Violent Crime?" Journal of Legal Studies 27 [January 1998], p. 213.)

  One of the central arguments both in the original paper and in this book is that the size of the deterrent effect is related to the number of permits issued, and it takes many years before states reach their long-run level of permits. Again, the figures in chapter 4 illustrate this quite clearly.

  I did not expect the number of permits to change equally across either counties or states. A major reason for the larger eff
ect on crime in the more urban counties was that in rural areas, permit requests already were being approved; hence it was in urban areas that the number of permitted concealed handguns increased the most.

  A week later, in response to a column that I published in the Omaha World-Herald, 20 Mr. Webster modified this claim somewhat:

  Lott claims that his analysis did not assume an immediate and constant effect, but that is contrary to his published article, in which the vast majority of the statistical models assume such an effect. (Daniel W. Webster, "Concealed-Gun Research Flawed," Omaha World-Herald, March 12, 1997; emphasis added.)

  When one does research, it is most appropriate to take the simplest specifications first and then gradually make things more complicated. The simplest way of doing this is to examine the mean crime rates before and after the change in a law. Then one would examine the trends that existed before and after the law. This is the pattern that I followed in my earlier work, and I have followed the same pattern here. The bottom line should be, How did the different ways of examining the data affect the results? What occurs here is that (1) the average crime rate falls after the nondiscretionary concealed-handgun laws are adopted; (2) violent-crime rates were rising until these laws were adopted, and they fell dramatically after that; and (3) the magnitude of the drops, both across counties and states and over time, corresponds to the number of permits issued.

  4 When were these concealed-handgun laws adopted in different states?

  Lott and Mustard also use incorrect dates of shall-issue law implementation in their analyses. For example, they claim that Virginia adopted its

  shall-issue law in 1988 Some populous counties in Virginia continued

  to issue very few permits until 1995 (after the study period), when the state eliminated this discretion. Lott and Mustard identify 1985 as the year in which Maine liberalized its concealed-carry policy. It is unclear why they chose 1985 as the year of policy intervention, because the state changed its concealed-carry law in 1981, 1983, 1985, 1989, and 1991. (Webster, "Claims," p. 3; see also Daniel W Webster, "Concealed-Gun Research Flawed," Omaha World-Herald, March 12, 1997; cited hereafter as Webster, "Flawed.")

  I do think that Virginia's 1988 law clearly attempted to take away local discretion in issuing permits, and, indeed, all but three counties clearly complied with the intent of the law. However, to satisfy any skeptics, I examined whether reclassifying Virginia affected the results: it did not. The 1988 law read as follows:

  The court, after consulting the law-enforcement authorities of the county or city and receiving a report from the Central Criminal Records Exchange, shall issue such permit if the applicant is of good character, has demonstrated

  THE POLITICAL AND ACADEMIC DEBATE/133

  a need to carry such concealed weapon, which need may include but is not limited to lawful defense and security, is physically and mentally competent to carry such weapon, and is not prohibited by law from receiving, possessing, or transporting such weapon [emphasis added]. 21

  As with Virginia, I relied on a study by Clayton Cramer and David Kopel to determine when Maine changed its law to a nondiscretionary law. Maine enacted a series of changes in its law in 1981, 1983, 1985, and 1991. The 1985 law did not completely eliminate discretion, but it provided the foundation for what they then considered to be a switch to a de facto shall-issue regime, which was upheld in a number of important state court decisions. 22 The bottom line, however (again, as with Virginia), is that reclassifying Maine (or even eliminating it from the data set) does not change the results much.

  5 Should robbery be the crime most affected by the adoption of the nondiscretionary law?

  Shall-issue laws were adopted principally to deter predatory street crime, the most common example of which is robbery by a stranger. But [the] results indicate that shall-issue laws had little or no effect on robbery rates. Instead the strongest deterrent effects estimated were for rape, aggravated assault, and murder. (Webster, "Claims," p. 3)

  Is it credible that laws that allow citizens to carry guns in public appear to have almost no effect on robberies, most of which occur in public spaces, yet do reduce the number of rapes, most of which occur outside of public spaces within someone's home. (Jens Ludwig, speaking on Morning Edition, National Public Radio, 10:00 a.m. ET December 10, 1996.)

  I have two responses. First, as anyone who has carefully read this book will know, it is simply not true that the results show "little or no effect on robbery rates." Whether the effect was greater for robbery or other violent crimes depends on whether one simply compares the mean crime rates before and after the laws (in which case the effect is relatively small for robbery) or compares the slopes before and after the law (in which case the effect for robbery is the largest).

  Second, it is not clear that robbery should exhibit the largest impacts, primarily because the term robbery encompasses many crimes that are not street robberies. For instance, we do not expect bank or residential robberies to decrease; in fact, they could even rise. Allowing law-abiding citizens to carry concealed handguns makes street robberies more difficult,

  and thus may make other crimes like residential robbery relatively more attractive. Yet not only is it possible that these two different components of robbery could move in opposite directions, but to rank some of these different crimes, one requires information on how sensitive different types of criminals are to the increased threat.

  Making claims about what will happen to different types of violent crimes is much more difficult than predicting the relative differences between, say, crimes that involve no contact with victims and crimes that do. Even here, however, some of these questions cannot be settled a priori. For example, when violent crimes decline, more people may feel free to walk around in neighborhoods, which implies that they are more likely to observe the illegal actions of strangers. 23 Criminals who commit violent crimes are also likely to commit some property crimes, and anything that can make an area unattractive to them will reduce both types of crime.

  6 Do concealed-handgun laws cause criminals to substitute property crimes for rape?

  Lott and Mustard argue that criminals, in response to shall-issue laws, substitute property crimes unlikely to involve contact with victims. But their theory and findings do not comport with any credible criminological theory because theft is the motive for only a small fraction of the violent crimes for which Lott and Mustard find shall-issue effects. It is difficult to rationalize why a criminal would, for example, steal a car because he felt deterred from raping or assaulting someone. (Webster, "Claims," p. 4. See also Jens Ludwig, "Do Permissive Concealed-Carry Laws Reduce Violent Crime?" Georgetown University working paper, October 8, 1996, p. 19, hereafter cited as Ludwig, "Permissive Concealed-Carry Laws")

  No one believes that hard-core rapists who are committing their crimes only for sexual gratification will turn into auto thieves, though some thefts do also involve aggravated assault, rape, or murder. 24 Indeed, 16 percent of murders in Chicago from 1990 to 1995 occurred in the process of a robbery. 25 What is most likely to happen, however, is that robbers will try to obtain money by other means such as auto theft or larceny. Although it is not unusual for rape victims to be robbed, the decline in rape most likely reflects the would-be rapist's fear of being shot.

  I am also not completely clear on what Webster means when he says that "theft is the motive for only a small fraction of violent crimes," since robbery accounted for as much as 34 percent of all violent crimes committed during the sample between 1977 and 1992 (and this excludes robberies that were committed when other more serious crimes like murder or rape occurred in connection with the robbery).

  THE POLITICAL AND ACADEMIC DEBATE/135

  7 Comparing crime rates for two to three years before nondiscretionary laws go into effect with crime rates for two to three years after the passage of such laws

  If right-to-carry laws have an immediate, substantial impact on the crime rates, the coefficients on the right
-to-carry laws immediately after the enactment of the law should be substantially different from those immediately preceding the law's enactment. To test formally for the impact of right-to-carry laws, we see if the sum of the coefficients for two to three years prior to adoption is significantly different from the sum for two and three years following adoption.... Only in the murder equation do our findings agree with Lott and Mustard. In contrast to Lott and Mustard, we find evidence that robberies and larcenies are reduced when right-to-carry laws are passed and no evidence of an impact on rape and aggravated assaults. (Dan Black and Daniel Nagin, "Do 'Right-to-Carry' Laws Deter Violent Crime?" Carnegie-Mellon University working paper, October 16, 1996, p. 7)

  Instead of the approach used earlier in this book (a simple time trend and time trend squared for the number of years before and after the concealed-handgun laws) Black and Nagin use ten different variables to examine these trends. Separate variables were used for the first year after the law, the second year after the law, the third year after the law, the fourth year after the law, and five or more years after the law. Similarly, five different variables were used to measure the effects for the five years leading up to the adoption of the law. They then compare the average coefficient values for the variables measuring the effects two to three years before the law with the average effect for the variables two to three years after the law.

  A quick glance at figures 7.1 to 7.5, which plot their results, will explain their findings. Generally, the pattern is very similar to what we reported earlier. In addition, as crime is rising right up until the law is adopted and falling thereafter, it is not surprising that some values when the crime rate is going down are equal to those when it was going up. It is the slopes of the lines and not simply their levels that matter. But more generally, why choose to compare only two to three years before and after to look for changes created by the law. Why not use all the data available?