1. The 1988 poll's margin of error was 1.1 percent, while that of the 1996 poll was 2.2 percent.
2. In order to obtain the rate at which people in the general population owned guns, I weighted the respondents' answers to give less weight to groups that were overrepre-sented among voters compared to their share in the overall population, and to give greater weight to those groups that were underrepresented. Twenty-four categories of personal characteristics were used to compute these weightings: white males and females, and black males and females, aged 18—29; neither black nor white males and females 18—29; white males and females, and black males and females 30—44; neither black nor white males and females 30—44; white males and females, and black males and females 45—59; neither black nor white males and females 45-59; white males and females, and black males and females over 59; neither black nor white males and females over 59.
3. This argument has been made explicitly in the press many times. See, for example, Scott Baldauf, "As Crime Shrinks, Security Is Still Growth Industry," Christian Science Monitor, Oct. 2, 1996, p. 1.
276 / NOTES TO PAGES 36-40
4. Alix M. Freedman, "Tinier, Deadlier Pocket Pistols Are in Vogue," Wall Street Journal, Sept. 12, 1996, P. Bl.
5. The primary concern here is that letting people check those parts of a list that apply will result in fewer positive responses than asking people to answer individual questions about each item. As one way of checking the importance of this concern, I examined whether other questions that changed in a similar way between the two polls experienced a change in the same direction as that shown for gun ownership. The two questions that I looked at—regarding marriage and whether children less than 18 lived with the respondent—moved in the opposite direction. Relatively more people indicated these responses in the 1988 poll when the questions were presented in a list than did so when they were presented with separate questions about these characteristics. I have also done extensive research using other questions involving marriage and children under 18 living with the respondent that were part of a "check as many as apply" question. That research provides extremely strong evidence that these questions were answered consistently be-' tween 1988 and 1996. See John R. Lott, Jr. and Larry W. Kenny, "How Dramatically Did Women's Suffrage Change the Size and Scope of Government?" University of Chicago School of Law working paper (1997). The relative differences in gun ownership across groups is also consistent with recent work using other polls by Edward Glaeser and Spencer Glendon, "Who Owns Guns?" American Economic Review 88 (May 1998).
The empirical work that will be done later will allow us to adjust for the changes in the reported level of gun ownership that might result from the change in this question.
6. I appreciate Tom Smith's taking the time to talk to me about these issues on May 30, 1997.
7. Gun owners within each of the twenty-four categories listed in note 2 above may have particular characteristics that cause them to vote at rates that differ from the rates at which other people vote. One would hope that some of that difference would be accounted for in the detailed demographic characteristics, but there is a good chance that this may not occur. Several attempts were made to see how large this effect might be by asking, for example, whether gun owners were more or less likely not to have voted in previous elections. This question has also been broken down to account for those who are old enough to have voted previously. For 1988, the difference in gun ownership between those who were voting for the first time and those who had voted previously was 3 percent (23.2 percent of those voting for the first time and 26.2 percent of those who were not owned guns). Limiting this question to people who were 30 years of age or older produced an even smaller difference: 28.9 percent of first-time voters owned guns versus 27.5 percent of those who had voted previously. Similarly, for the question of whether voters in 1988 had also voted in 1984, the difference was also 3 percent (23 percent of those who did not vote in 1984 and 26.4 percent of those who did owned guns).
Because most people voted, a 13 percent increase in the proportion of the general population owning guns would require an even greater drop in gun ownership among those who didn't vote in order for gun ownership to have remained constant. For some groups, such as women, for whom gun ownership among voters increased by over 70 percent, the increase is so large and the percent of women voting so high that an 80 percent drop in gun ownership among nonvoting women would have been required for gun ownership among women to have remained constant.
8. Indeed, making this adjustment produces a number that is much closer to that found in other polls of the general population, such as the National Opinion Research Center's 1996 National Gun-Policy Survey, which finds that 42 percent of the general adult population owns guns.
9. The previous peak in murder rates occurred at the end of Prohibition in the early 1930s, with the peak of 9.7 murders per 100,000 people being reached in 1933. The 1996 murder rate of 7.3 murders per 100,000 people seems tame by comparison. Indeed many people, such as Milton Friedman, have argued that much of the change in murder rates
NOTES TO PAGES 43-49/277
over time has been driven by the country's war on drugs and its earlier war on alcohol. Even the gradual increase in murder rates leading up to the Nineteenth Amendment's adoption in 1991 corresponds with passage of individual state laws. Kansas, Maine, and North Dakota enacted prohibition laws between 1880 and 1890. Five states enacted prohibition in 1907-1909, followed by twelve more between 1912 and 1915 and another twelve between 1916 and 1918. Obviously, all this points to the importance of other factors in the murder rate, and that is part of the reason why I include a measure of drug prices in my estimates to explain why crime rates change over time. See Ernest H. Cherrington, The Evolution of Prohibition in the United States of America (Westerville, OH: Tern-Press, 1920); Edward B. Dunford, The History of the Temperance Movement (Washington, DC: Tern-Press, 1943); D. Leigh Colvin, Prohibition in the United States, (New York: George H. Doran, 1926); as well as state statutes (as a check).
10. While I will follow Cramer and Kopel's definition of what constitutes a "shall-issue" or a "do-issue" state (see "'Shall Issue': The New Wave of Concealed-Handgun Permit Laws," Tennessee Law Review 62 [Spring 1995]), one commentator has suggested that it is not appropriate to include Maine in these categories (Stephen P. Teret, "Critical Comments on a Paper by Lott and Mustard," School of Hygiene and Public Health, Johns Hopkins University, mimeo, Aug. 7, 1996). Neither defining Maine so that the "shall-issue" dummy equals zero nor removing Maine from the data set alters the findings shown in this book.
11. While the intent of the 1988 legislation in Virginia was clearly to institute a "shall-issue" law, the law was not equally implemented in all counties in the state. To deal with this problem, I reran the regressions reported in this paper with the "shall-issue" dummy equal to both 1 and 0 for Virginia.
12. I rely on Cramer and Kopel for this list of states. Some states, known as "do-issue" states, are also included in Cramer and Kopel's list of "shall-issue" states, though these authors argue that for all practical purposes these two groups of states are identical. See Cramer and Kopel, "New Wave of Concealed-Handgun Permit Laws," pp. 679—91.
13. The Oregon counties providing permit data were Benton, Clackamas, Columbia, Coos, Curry, Deschutes, Douglas, Gilliam, Hood River, Jackson, Jefferson, Josephine, Klamath, Lane, Lincoln, Linn, Malheur, Marion, Morrow, Multnomah, Polk, Tillamook, Umatilla, Washington and Yamhill.
14. In economics jargon I would say that I am interacting the sentence length with year-dummy variables.
15. These variables are referred to as county fixed-effects, where a separate dummy variable is set equal to 1 for each individual county.
16. See appendix 4 for the list and summary statistics.
17. For example, see James Q. Wilson and Richard J. Herrnstein, Crime and Human Nature (New York: Simon and Schuster, 1985), pp. 126-47.
18. However, the effect of an unusually large pe
rcentage of young males in the population may be mitigated because those most vulnerable to crime may be more likely to take actions to protect themselves. Depending upon how responsive victims are to these threats, the coefficient for a variable like the percent of young males in the population could be zero even when the group in question poses a large criminal threat.
19. Edward L. Glaeser and Bruce Sacerdote, "Why Is There More Crime in Cities?" Harvard University working paper, Nov. 14, 1995.
20. For a discussion of the relationship between income and crime, see John R. Lott, Jr., "A Transaction-Costs Explanation for Why the Poor Are More Likely to Commit Crime," Journal of Legal Studies 19 (Jan. 1990): 243-45.
21. A brief survey of the laws, excluding the changes in the rules regarding permits, reveals the following: Alabama made no significant changes in these laws during the period. Connecticut law gradually changed its wording from "criminal use" to "criminal possession" from 1986 to 1994. Florida has the most extensive description of penalties; the
278 / NOTES TO PAGES 49-51
same basic law (790.161) persists throughout the years. An additional law (790.07) appeared only in 1986. In Georgia, a law (16-11-106) that does not appear in the 1986 edition appears in the 1989 and 1994 editions. The law involves possession of a firearm during commission of a crime and specifies the associated penalties. Because this legal change might have occurred at the same time as the 1989 changes in the rules regarding permits, I used a Lexis search to check the legislative history of 16-11-106 and found that the laws were last changed in 1987, two years before the permit rules were changed (Official Code of Georgia, Annotated, at 16-11-106 [1996]). Idaho has made no significant changes over time. In Indiana and Maine no significant changes occurred in these laws during the period. In Mississippi, Law 97-37-1 talks explicitly about penalties. It appears in the 1986 version but not in the 1989 or the 1994 versions. Montana enacted some changes in punishments related to unauthorized carrying of concealed weapons, but no changes in the punishment for using a weapon in a crime. New Hampshire, North Dakota, Oregon, Pennsylvania, and Washington made no significant changes in these laws during period. In South Dakota, Law 22-14-13, which specifies penalties for commission of a felony while armed, appears in 1986 but not 1989. In Vermont, Section 4005, which outlines the penalties for carrying a gun when committing a felony, appears in 1986 but not in 1989 or 1994. Virginia and Washington made no significant changes in these laws during the period. West Virginia had Law 67-7-12 on the books in 1994, but not in the earlier versions. It involves punishment for endangerment with firearms. Removing Georgia from the sample, which was the only state that enacted changes in its gun laws near the year that the "shall-issue" law went into affect, eliminates the chance that the other changes in gun laws might affect my results and does not appreciably alter those results.
22. Thomas B. Marvelland Carlisle E. Moody, "The Impact of Enhanced Prison Terms for Felonies Committed with Guns," Criminology 33 (May 1995): 247, 258-61.
23. Marvell and Moody's findings (see note 22 above) show that the shortest time period between these sentencing enhancements and changes in concealed-weapon laws is seven years (Pennsylvania). Twenty-six states passed their enhancement laws prior to the beginning of my sample period, and only four states passed such laws after 1981. Maine, which implemented its concealed-handgun law in 1985, passed its sentencing-enhancement laws in 1971.
24. The states that had waiting periods prior to the beginning of the sample are Alabama, California, Connecticut, Illinois, Maryland, Minnesota, New Jersey, North Carolina, Pennsylvania, Rhode Island, South Dakota, Washington, and Wisconsin. The District of Columbia also had a waiting period prior to the beginning of my sample. The states that adopted this rule during the sample period are Hawaii, Indiana, Iowa, Missouri, Oregon, and Virginia.
CHAPTER FOUR
1. More precisely, it is the percentage of a one-standard-deviation change in the crime rate that can be explained by a one-standard-deviation change in the endogenous variable.
2. All the results are reported for the higher threshold required with a two-tailed t-test.
3. One possible concern with these initial results arises from my use of an aggregate public-policy variable (state right-to-carry laws) on county-level data. See Bruce C. Greenwald, "A General Analysis of the Bias in the Estimated Standard Errors of Least Squares Coefficients," Journal of Econometrics 22 (Aug. 1983): 323—38; and Brent R. Moulton, "An Illustration of a Pitfall in Estimating the Effects of Aggregate Variables on Micro Units," Review of Economics and Statistics 72 (1990): 334. Moulton writes, "If disturbances are correlated within the groupings that are used to merge aggregate with micro data, however, then even small levels of correlation can cause the standard errors from the ordinary
NOTES TO PAGES 51-54/279
least squares (OLS) to be seriously biased downward." Yet this should not really be a concern here because of my use of dummy variables for all the counties, which is equivalent to using state dummies as well as county dummies for all but one of the counties within each state. Using these dummy variables thus allows us to control for any disturbances that are correlated within any individual state. The regressions discussed in table 4.2 reestimate the specifications shown in table 4.1 but also include state dummies that are interacted with a time trend. This should thus not only control for any disturbances that are correlated with the states, but also for any disturbances that are correlated within a state over time. Finally, while right-to-carry laws are almost always statewide laws, there is one exception. Pennsylvania partially exempted its largest county (Philadelphia) from the law when it was passed in 1989, and it remained exempt from the law during the rest of the sample period. However, permits granted in the counties surrounding Philadelphia were valid for use in the city.
4. However, the increase in the number of property crimes is larger than the decrease in the number of robberies.
5. While I adopt the classifications used by Cramer and Kopel in "'Shall Issue': The New Wave of Concealed-Handgun Permit Laws," Tennessee Law Review 62 (Spring 1995), some are more convinced by other classifications of states (for example, see Doug Weil, "Response to John Lott's Study on the Impact of 'Carry-Concealed' Laws on Crime Rates," U.S. Newswire, Aug. 8, 1996; and Stephen P. Teret, "Critical Comments on a Paper by Lott and Mustard," School of Hygiene and Public Health, Johns Hopkins University, mimeo, Aug. 7, 1996). Setting the "shall-issue" dummy for Maine to zero and rerunning the regressions shown in table 4.1 results in the "shall-issue" coefficient equaling—3% for violent crimes, —8% for murder, -6% for rape, —4.5 for aggravated assault, —1% for robbery, 3% for property crimes, 8.1% for automobile theft, 0.4% for burglary, and 3% for larceny. Similarly, setting the "shall-issue" dummy for Virginia to zero results in the "shall-issue" coefficient equaling —4% for violent crimes, —9% for murder, -5% for rape, —5% for aggravated assault, —0.11% for robbery, 3% for property crimes, 9% for automobile theft, 2% for burglary, and 3% for larceny. As a final test, dropping both Maine and Virginia from the data set results in the "shall-issue" coefficient equaling —2% for violent crimes, —10% for murder, -6% for rape, —3% for aggravated assault, 0.6% for robbery, 3.6% for property crimes, 10% for automobile theft, 2% for burglary, and 4% for larceny.
6. This information is obtained from Mortality Detail Records provided by the U.S. Department of Health and Human Services.
7. This assumption is implausible for many reasons. One reason is that accidental handgun deaths occur in states without concealed-handgun laws.
8. Given the possible relationship between drug prices and crime, I reran the regressions in table 4.1 and included an additional variable for cocaine prices. One argument linking drug prices and crime is that if the demand for drugs is inelastic and if people commit crimes in order to finance their habits, higher drug prices might lead to increased levels of crime. Using the Drug Enforcement Administration's STRIDE data set from 1977 to 1992 (with the exceptions of 1988 and 1989
), Michael Grossman, Frank J. Chaloupka, and Charles C. Brown, ("The Demand for Cocaine by Young Adults: A Rational Addiction Approach," NBER working paper, July 1996), estimate the price of cocaine as a function of its purity, weight, year dummies, year dummies interacted with eight regional dummies, and individual city dummies. There are two problems with this measure of predicted prices: (1) it removes observations during a couple of important years during which changes were occurring in concealed-handgun laws, and (2) the predicted values that I obtained ignored the city-level observations. The reduced number of observations provides an important reason why I do not include this variable in the regressions shown in table 4. 1. However, the primary impact of including this new variable is to make the "shall-issue" coefficients in the violent-crime regressions even more negative and more
280 / NOTES TO PAGES 54-57
significant (for example, the coefficient for the violent-crime regression becomes -7.5%, -10% for the murder regression, -7.7% for rape, and -11% for aggravated assault, with all of them significant at more than the 0.01 level). Only for the burglary regression does the "shall-issue" coefficient change appreciably: it becomes negative and insignificant. The variable for drug prices itself is negatively related to murders and rapes and positively and significantly related, at least at the 0.01 level for a one-tailed t-test, to all the other categories of crime. I would like to thank Michael Grossman for providing me with the original regressions on drug prices from his paper.
9. In contrast, if we had instead inquired what difference it would make in crime rates if either all states or no states adopted right-to-carry concealed-handgun laws, the case of all states adopting concealed-handgun laws would have produced 2,000 fewer murders; 5,700 fewer rapes; 79,000 fewer aggravated assaults; and 14,900 fewer robberies. In contrast, property crimes would have risen by 336,410.
10. Ted R. Miller, Mark A. Cohen, and Brian Wiersema, Victim Costs and Consequences: A New Look (Washington, DC: National Institute of Justice, Feb. 1996).
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