More Guns Less Crime (33 page)

During the Missouri campaign, many reporters called me up to comment about the "FBI numbers" on crime rates. 66 When I would point out that the claim was actually based on a report produced by Handgun Control, they said that they didn't know what to do with the conflicting claims. Editorials and news stories in the St. Louis Post-Dispatch and the Kansas City Star normally just accepted the Handgun Control assertion as established truth.

After repeatedly encountering this response from reporters, I started suggesting to reporters that they ask some local academic (a statistician, criminologist, or economist) to evaluate the two conflicting claims. One reporter with the St. Louis Post-Dispatch, Kim Bell, expressed the concern that they might run into a professor with a preconceived bias and that would make the test unfair. I told her that I was willing to take that risk, but that if she were concerned about that problem, she could always approach a few different academics. Others who refused to take me up on this challenge included Bill Freivogel, deputy editor at the Post-Dispatch, and Rich Hood, an editor at the Kansas City Star. Rather, their newspapers simply presented Handgun Control's claims as fact.

Criticisms of the Book

Some reviewers clearly have not even bothered to read my book, or at least it didn't matter to them whether they read it. A review in the British Journal of Criminology claimed that "there is nothing in Lott's study to con-

nect this more general information to the specific county-based data on the issuing of concealed-carry permits," "Lott is dealing with a time frame entirely prior to the introduction of the non-discretionary concealed-carry laws in most of the states which now have them," and "he has preoccupied himself exclusively with 'good guns' owned by 'good people.'" 67 Another book review, in the New England Journal of Medicine, starts off by falsely claiming that I "approvingly" quote Archie Bunker's suggestion to stop airplane hijacking by arming "all the passengers." 68

As of this writing (September 1999), Handgun Control's Web site still continues to assert the same "major criticisms" of my research—"where are the robbery effects?" "auto theft as a substitute for rape," "Lott fails to account for other initiatives—including other gun control laws," "Lott fails to account for cyclical changes in crime rates"—and the same claims about misclassifying state laws. 69 Ironically, they also continue citing the McDowall et. al. (1995) study that we discussed in chapter 2, which examined a total of only five counties picked from three states, attempted to account for no other factors that might be changing over the same period of time, and examined only murders with guns. 70

Time magazine reported that "Other critics raise questions about whether Lott massaged the numbers. One arcane quarrel: for statistical purposes, Lott dropped from his study sample any counties that had no reported murders or assaults for a given year." 71 It also said that "the book does not account for fluctuating factors like poverty levels and policing techniques." After the story on my book ran, I called up the reporter, Romesh Ratnesar, and said that I knew that he had read the book carefully, so I was surprised that he would write these claims as if they were true. I, as well as critics like Black and Nagin, had looked at the evidence once arrest rates were excluded so as to include those counties with zero arrest rates. What was particularly disappointing was that I had spent the time to obtain all the data that were available. The county-level data were used for all the years and for all the counties for which they were available, both when I did the original paper and when I wrote the book. As to the other claim, I had measures of poverty and policing techniques like the broken-window strategy included.

While I appreciated that the Time magazine piece was published, claims that "the book does not account" for these factors are clearly wrong. Ratnesar agreed that these issues were dealt with in the book, but that his role was not to serve as a "referee" between the two sides. His job was to report what the claims were. 72

I keep on being amazed at the absolute faith that so many news media people place in the gun-control organizations and the "facts" issued by them. Take another example: Molly Ivins, a syndicated columnist, as-

serted that "[Lott] himself admits, he didn't look at any other causative factors—no other variables, as they say." 73 She also argued that "Lott's study supposedly showed that when 10 Western states passed 'right-to-carry' laws between 1985 and 1992, they had less violent crime" and that "according to the author's research, getting rid of black women older than 40 would do more to stop murder than anything else we could try." Syndicated columnist Tom Teepen wrote a very similar column a year earlier in which he also claimed that this book "failed to consider other anti-crime variables in making its cause-and-effect claims, a fundamental gaffe." 74

I did get a chance to talk with Mr. Teepen, and he told me that he wrote his review without even reading the book. He apparently relied on conversations that he had with people at Handgun Control and the Violence Policy Center. When I talked to Cynthia Tucker, an editor at the Atlanta Journal-Constitution, where Mr. Teepen is based, about having a letter responding to the charges Mr. Teepen made, she found it "unbelievable" that he would have written the review without first looking at the book. She grudgingly said that if it were true, they would publish as a response a short letter, but that she would have to check into it first. Needless to say, the newspaper published my letter the following Sunday. 75 In contrast, unfortunately, Ms. Ivins never returned my telephone calls or responded to my E-mail messages and never corrected her claims. 76

Undoubtedly, some of the claims constitute simple mistakes, but more than a few reflect columnists and others being too quick to accept whatever gun-control groups tell them. I will spare the reader the long list of other false claims reported in the press. 77 Yet, obviously, many people, particularly those with gun-control organizations, continually make statements that they know are false—safe in the knowledge that only a tiny fraction of readers or listeners ever check the assertions. Unfortunately, the gun-control organizations risk losing significant credibility only with the few who read the book. 78

Other critiques by academics and the media—some old, some new— require more in-depth discussions. The rest of this section reviews the critiques and then provides my responses.

1 How do we know that these findings are not a result of the normal ups and downs in crime rates?

The central problem is that crime moves in waves, yet Lott's analysis does not include variables that can explain these cycles. (David Hemenway, "Book Review of More Guns, Less Crime? New England Journal ofMedicine, December 31, 1998)

Jens Ludwig, assistant professor of public policy at Georgetown University, argued that Lott's data don't prove "anything about what laws do to crime." He noted that crime rates, including homicide, are cyclical: They rise and fall every five to 10 years or so in response to forces that are not well understood. Ludwig suggested that this pattern explains the apparent effectiveness of concealed weapons laws. Imagine, he said, a state where the murder cycle is on the upswing and approaching its peak and public concern is correspondingly high. Then a particularly ghastly mass shooting occurs. Panicked legislators respond by passing a law that allows equally panicked citizens to carry concealed weapons. A year or two later, the murder rate goes down, as Lott's study found. (Richard Morin, "Guns and Gun Massacres: A Contrary View," Washington Post, May 30, 1999, p. B5)

Lott's variables are not good predictors of crime waves. Nor does he provide for any effect of history in the way he models crime. For example, the year 1982 could as well follow 1991 as 1981 in his analyses. (David Hemenway, "More Guns, Less Crime," New England Journal of Medicine, May 20, 1999)

Even my most determined critics concede one point: violent-crime rates fell at the point in time that the right-to-carry laws went into effect. The real question is: Why did the crime rates fall? Do these laws simply happen to get passed right when crime rates hit their peaks? Why don't we observe this coincidence of timing for other gun-control laws?

It is logically possible that such coincidental timing could take place. But there is more evidence besides decreases in crime after right-to-carry laws are adopted. First, the size of the drop is closely related to the number of permits issued (as indicated in the first edition and confirmed by the additional data shown here). Second, the new evidence presented here goes even further: it is not just the number of permits, but also the type of people who obtain permits that is important. For example, high fees discourage the poor, the very people who are most vulnerable to crime, from getting permits. Third, if it is merely coincidental timing, why do violent-crime rates start rising in adjacent counties in states without right-to-carry laws exactly when states which have adopted right-to-carry laws are experiencing a drop in violent crime?

Finally, as the period of time studied gets progressively longer, the results are less likely to be due to crime cycles, since any possible crime "cycles" involve crime not only going down but also "up." If crime happened to hit a peak, say, every ten years, and right-to-carry laws tended to be passed right at the peak, then the reported effect of the law would spuriously show a negative impact right after the enactment. However,

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five years after that an equally large positive spurious effect on crime would have to show up. Instead, my results reveal permanent reductions in crime that only become larger with time, as more people acquire concealed-carry permits.

Furthermore, my study accounted for possible crime cycles in many ways: individual year variables accounted for average national changes in crime rates, and different approaches in chapter 4 controlled for individual state and county time trends and did not take away the effects of concealed carry. To the contrary, they resulted in similar or even stronger estimates for the deterrence effect. Other estimates used robbery or burglary rates to help account for any left-out factors in explaining other crime rates. Since crime rates generally tend to move together, this method also allows one to detect individual county trends. In updating the book, I have included estimates that account for the separate average year-to-year changes in five different regions in the country. Despite all these additional controls the deterrence effect continues to show up strongly.

It is simply false to claim, "nor does he provide for any effect of history," as I have variables that account for "changes" in crime rates from previous years. I have variables that measure explicitly the number of years that the law has been in effect as well as the number of years until it goes into effect. In addition, I have used individual state linear time trends that explicitly allow crime rates to change systematically over time.

Earlier discussions in chapter 7 on crime cycles (pp. 130—31) and causality (pp. 152—54) also explain why these concerns are misplaced.

2 Does it make sense to control for nonlinear time trends for each state?

The results suggest that the Lott and Mustard model, which includes only a single national trend, does not adequately capture local time trends in crime rates. To test for this possibility, we generalized the Lott and Mustard model to include state-specific trends in an effort to control for these unobserved factors. ... we report the results for models with a quadratic time trend. The only significant impact estimate is for assaults, and its sign is positive, not negative. (Dan Black and Dan Nagin, "Do Right-to-Carry Laws Deter Violent Crime?" Journal ofLegal Studies, January 1998, p. 218)

Much more was controlled for than "a single national trend" in my study (e.g., as just mentioned above, state and county trends as well as other crime rates). While it is reasonable to include individual linear state trends or nonlinear trends for regions, including nonlinear trends for in-

dividual states makes no sense. The approach by Black and Nagin is particularly noteworthy because it is the one case in which an academic study has claimed that a statistically significant, even if small, increase in any type of violent crime (aggravated assault) occurs after the law.

Consider a hypothetical case in which the crime rate for each and every state follows the pattern that Black and Nagin found in their earlier paper and that I showed in this book (discussed in chapter 7, pp. 136-37): crime rates were rising up until the law went into effect and falling thereafter. Allowing a separate quadratic time trend for each state results in the time trend picking up both the upward path before the law and the downward path thereafter. If the different state crime patterns all peaked in the year in which their state law went into effect, the state-specific quadratic trends would account for all the impact of the law. A variable measuring the average crime rates before and after the law would then no longer reflect whether the law raised or lowered the crime rate. 79 This is analogous to the "dubious variable" problem discussed earlier. If enough state-specific trends are included, there will be nothing left for the other variables to explain.

If shall-issue laws deter crime, we would expect crime rates to rise until the law was passed and then to rise more slowly or to fall. The effect should increase over time as more permits are issued and more criminals adjust to the increased risks that they face. But the quadratic specification used by Black and Nagin replicates that pattern, state by state. Their results show not that the effect from the quadratic curve is insignificant, but that the deviation of the law's effect from a quadratic curve over time is generally insignificant.

To see this more clearly, take the hypothetical case illustrated in figure 9.15, in which a state faced rising crime rates. 80 The figure shows imaginary data for crime in a state that passed its shall-issue law in 1991. (The dots in the figure display what the crime rate was in different years.) The pattern would clearly support the hypothesis that concealed-handgun laws deter violent crime, but the pattern can easily be fitted with a quadratic curve, as demonstrated with the curved line. There is no systematic drop left over for any measure of the right-to-carry law to detect— in terms of the figure, the difference between the dots and the curved line shows no particular pattern.

Phrased differently, the deterrence hypothesis implies a state-specific time pattern in crime rates (because different states did or did not pass shall-issue laws, or passed them at different dates). All Black and Nagin have shown is that they can fit such a state-specific pattern with a state-specific quadratic time trend, and do this well enough that the residuals no longer show a pattern.

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Year

83 85 87 89 91 93 95 97 Right-to-carry law passes in 1991

Figure 9.15. Fitting a nonlinear trend to individual states

3 Should one expect an immediate and constant effect from right-to-carry laws with the same effect everywhere?

While he includes a chapter that contains replies to his critics, unfortunately he doesn't directly respond to the key Black and Nagin finding that formal statistical tests reject his methods. The closest he gets to addressing this point is to acknowledge "the more serious possibility is that some other factor may have caused both the reduction in crime rates and the passage of the law to occur at the same time," but then goes on to say that he has "presented over a thousand [statistical model] specifications" that reveal "an extremely consistent pattern" that right-to-carry laws reduce crime. Another view would be that a thousand versions of a demonstrably invalid analytical approach produce boxes full of invalid results. (Jens Lud-wig, "Guns and Numbers," Washington Monthly, June 1998, p. 51) 81

We applied a number of specification tests suggested by James J. Heckman and V. Joseph Hotz. The results are available from us on request. The specifics of the findings, however, are less important than the overall conclusion that is implied. The results show that commonly the model either overestimates or underestimates the crime rate of adopting states in the years prior to adoption. (Dan Black and Dan Nagin, "Do Right-to-Carry Laws Deter Violent Crimel" Journal of Legal Studies, January 1998, p. 218)

Black and Nagin actually spent only a few brief sentences on this issue at the very end of their paper. Nevertheless, I did respond to this general point in the original book. Their test is based upon the claim that I believe "that [right-to-carry] laws have an impact on crime rates that is constant over time." 82 True, when one looks at the simple before-and-after average crime rates, as in the first test presented in table 4.1 and

Crime rate before law

Crime rate after law

-5 -4

-10 12 3 4 5

Years before and after implementation of the law

Figure 9.16. What was the crime pattern being assumed in the simple test provided in table 4.1?

a corresponding table in my original work with Mustard, this was the assumption that was being made. 83 Figure 9.16 illustrates the crime pattern assumed by that test. But I emphasized that looking at the before-and-after averages was not a very good way to test the impact of the right-to-carry laws (e.g., see p. 90), and I presented better, more complicated specifications which showed even larger benefits from these laws. Black and Nagin's test confirms the very criticisms that I was making of these initial simplifying assumptions.

Looking at the before-and-after averages merely provides a simplified starting point. If criminals respond to the risk of meeting a potential victim who is carrying a concealed handgun, the deterrent effect of a concealed-handgun law should be related to the number of concealed handguns being carried and that should rise gradually over time. It was precisely because of these concerns that I included a variable for the number of years since the law had been in effect. As consistently demonstrated in figure 1 in my original paper as well as the figures in this book (e.g., pp. 77—79), these estimated time trends confirm that crime rates were rising before the law went into effect and falling afterward, with the effect increasing as more years went by.

As already discussed in the book, I did not expect the impact to be the same across all states, for obviously all states cannot be expected to issue permits at the same rate (see the response to point 3 on pp. 131—32). Indeed, this is one of the reasons why I examined whether the drops in crime rates were greatest in urban, high-population areas.

On this issue David Friedman, a professor at the University of Santa Clara Law School, wrote that "The simplifying assumptions used in one

of the regressions reported in the Lott and Mustard paper (Table 3) are not true—something that should be obvious to anyone who has read Lott and Mustard's original article, which included a variety of other regressions designed to deal with the complications assumed away in that one. Black and Nagin simply applied tests of the specification to demonstrate that they were not true." 84 Similar points have also been raised in academic reviews of the book: "Another tactic was to criticize one part of the research by raising issues that Lott actually raised and addressed in another part of the study. Those criticisms that were not uninformed or misleading were generally irrelevant since taking them into account did not change his empirical results. Nonetheless, they were widely cited by an unquestioning press." 85

4 Can changes in illegal drug use explain the results?

Even though Lott's fixed effects regressions will correct for some of the unobserved differences between the two groups of states [shall-issue and non-shall-issue states], we worry in particular that the crack induced crime jump in the mid-1980s in the states that did not pass shall issue laws may account for the apparent crime-reducing effects of the concealed-handgun laws. The omission of crack-related explanatory variables may have spuriously correlated lower crime with the passage of shall issue laws instead of correctly relating higher crime to the introduction of crack. The adoption of shall issue laws by six states in the 1980s may be associated with an unexpected crime rate increase in states that did not pass the laws rather than a concealed-gun-induced decrease in state that did. Two testable conclusions flow from our crack hypothesis: 1) Lott's results may not be robust to changes in specification that more fully capture differences in states that adopt or shun shall issue laws and 2) Lott's results may become weaker as additional years of data are added (because crack-related crime seems to have been declining sharply, giving the nonadopt-ing states a relatively better crime performance in the last five years). (Ian Ayres and John J. Donohue III, "Nondiscretionary Concealed Weapons Laws: A Case Study of Statistics, Standards of Proof, and Public Policy," American Law and Economics Review 1, nos. 1—2 [Fall 1999]: 464—65)

Their concern over cocaine- or crack-induced crime is surely a legitimate one, and it must be examined for the research to be convincing. Indeed, if the accessibility of cocaine or crack were primarily a problem in non-right-to-carry areas, they might experience a relative increase in crime, particularly for murder. Using the simplest approach—of using variables to account for national changes in crime between years—would not detect the differences in time trends then between shall-issue and non-

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shall-issue states. Still, the original tests in this book did address this problem in many different ways.

While it is difficult to directly measure the violence-inducing influence of cocaine or crack, I do attempt to measure directly the relative accessibility of cocaine in different markets. For example, the book and the original paper reported that including price data for cocaine (pp. 279—80, n. 8) did not alter the results. Using yearly county-level pricing data also has the advantage of detecting cost and not demand differences between counties, thus measuring the differences in availability across counties. 86 The simplest regressions did use only national year dummy variables, but other attempts were made to account for differences in time trends by including either individual state or county trends. Ayres and Donohue argue that the differences in time trends between states with right-to-carry laws and those without such laws are really due to the crack cocaine market. If the differences in trends that Ayres and Donohue describe actually exist, these state or county trends (particularly the county-level ones) should account for this. However, including these trends actually strengthens the results, which is the opposite of what Ayres and Donohue predict.

The spillover effects on neighboring counties strongly undermine their critique. Earlier we examined the crime rates for counties within either fifty or one hundred miles of each other on either side of a state border (the reported results are based on counties whose county centers are within fifty miles of each other). Neighboring counties without right-to-carry laws directly on the other side of the border experienced an increase in violent crime precisely when the counties adopting the law were experiencing a drop. But that is not all. The size of the spillover is larger if the neighboring counties are closely matched to each other in population density. In other words, criminals in more urban areas (as measured by population density) are more likely to move across the border if the neighboring county is also urban. Ayres and Donohue argue that different parts of the country may have experienced different impacts from the crack epidemic. Yet if you have two urban counties next to each other, how can the Ayres and Donohue discussion explain why one urban county would face a crime increase from drugs when the neighboring urban county is experiencing a drop? Such an isolation would be particularly surprising given that these counties are known to be closely tied to each other in terms of criminals moving between them.