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2016 The Short-Term Deterrent Effect of Execution on Homicides in the United States, 1979-1998 Moonki Hong
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COLLEGE OF CRIMINOLOGY AND CRIMINAL JUSTICE
THE SHORT-TERM DETERRENT EFFECT OF EXECUTION ON HOMICIDES
IN THE UNITED STATES, 1979 - 1998
By
MOONKI HONG
A Dissertation submitted to the College of Criminology and Criminal Justice in partial fulfillment of the requirements for the degree of Doctor of Philosophy
2016 Moonki Hong defended this dissertation on April 14, 2016. The members of the supervisory committee were:
Gary D. Kleck Professor Directing Dissertation
David W. Rasmussen University Representative
William D. Bales Committee Member
Theodore G. Chiricos Committee Member
The Graduate School has verified and approved the above-named committee members, and certifies that the dissertation has been approved in accordance with university requirements.
ii
This dissertation is dedicated to my parents, Sungkwan Hong and Kyongja Kim, who were always there praying for me. I am very glad to know that they have been able to see me complete this undertaking, as their kindness and much loving encouragement made it possible.
iii ACKNOWLEDGMENTS
I could not have completed this dissertation without the support from many people. Thus, I would like to express my sincere appreciation to all of those who have contributed to my efforts over the past years. First and foremost, I would like to extend my sincerest gratitude and appreciation to my major professor, Gary Kleck, for the advice, understanding and considerable tolerance he has demonstrated throughout this research. His guidance and knowledge have been invaluable to my successful completion of the doctoral program. Over the years and the distance, he never failed to give my work and me his full attention. Dr. Kleck displayed great patience and allowed me to work at my own pace while always being there when I needed him. Dr. Kleck’s compassion and commitment to his students and his desire for them to succeed will remain with me throughout my life. Without his generous support and intellectual guidance, I could not have finished this dissertation. I thank you from the bottom of my heart. I am indebted equally my other dissertation committee members, Drs. David Rasmussen, William Bales, and Theodore Chiricos, whose support, advice and feedback have been of great benefit in the completion of this dissertation. It was an honor to have them serve on my committee. Special thanks go to Dr. Nancy Marcus, the Dean of the Graduate School, and Dr. Thomas Bloomberg, the Dean of the College of Criminology and Criminal Justice for their unqualified support and assistance in allowing me to undertake this work. My thanks go out to the College of Criminology and Criminal Justice at Florida State University for the education they have provided me. I consider myself blessed to have studied and worked there with my professors and fellow classmates. I would like to thank Dr. SuHo Lee, an associate professor in the Department of Criminal Justice and Sociology at Cameron University. Dr. Lee was the best mentor while I was working at Cameron University. Dr. Lee always provided me with the best advice and support. Finally, my parents, Sungkwan Hong and Kyongja Kim, and my little brother, Wangmun Hong, have been constant sources of support and encouragement. I owe an unpayable debt to my parents in particular, who have offered me unwavering support as I pursued my studies. Without this, I might not have found myself at Florida State University, nor had the courage to engage in
iv this task and see it through. I am especially grateful that my parents are alive to witness the completion of this dissertation and hope that I will use what I have learned to live up to their expectations.
v TABLE OF CONTENTS
List of Tables ...... ix List of Figures ...... x Abstract ...... xi
1. INTRODUCTION ...... 1
Historical Background: The Use of the Death Penalty in the United States ...... 2 Policy Implication Issues ...... 4 Theoretical Issues ...... 7 Statement of the Problem ...... 9 Summary ...... 10
2. THEORY ...... 11
Deterrence Theory ...... 11 General Overview ...... 11 Definition ...... 13 Types of Deterrence ...... 13 The Simultaneous Relationship between Executions and Homicide Rates ...... 16 Other Possible Preventive Mechanism for Punishment ...... 17 The Brutalization Effect of Executions on Homicides ...... 18 Full Rational Choice and Limited Rational Choice Models of Crime and Deterrence ...... 19 Full Rational Choice Model of Crime and Deterrence ...... 19 Limited Rational Choice (Constricted Rational Choice) Model of Crime and Deterrence ...... 21 Threat Communication as Proxies for Perceptions of Execution Risk ...... 22 The Effects on Homicides of Factors Other than the Death Penalty ...... 24 Other Criminal Justice Factors...... 24 Non-Criminal Justice Factors ...... 24
3. LITERATURE REVIEW...... 26
Summary of Findings from Previous Studies ...... 26 The Dependent Variable ...... 31 Measures of the Prevalence or Risk of Capital Punishment ...... 34 Measures of Execution Risk ...... 36 Temporal Unit of Analysis ...... 38 News Media Publicity on Executions ...... 39 Control Variables ...... 40 Deterrence Variables ...... 40 Economic Variables ...... 42 Social and Demographic Variables ...... 43 Temporal Variables ...... 43
vi Other Violent and Property Crime ...... 44 Research Designs ...... 45 Unit of Analysis ...... 49 Temporal Unit of Analysis...... 50 Geographical Unit of Analysis...... 51 Homicide Data Sources ...... 53 Summary ...... 55
4. RESEARCH METHODOLOGY ...... 57
Research Design ...... 57 Research Data Sources ...... 58 Analytical Model of Daily Homicide Counts ...... 64 Variables ...... 65 Dependent Variable ...... 65 Main Independent Variable of Interest - Occurrence of Executions and Execution Publicity ...... 66 Control Variables ...... 70 Daily Estimates of State Population and Prison Population ...... 70 Temporal Control Variables ...... 71 Geographical Control Variables ...... 73 Research Hypotheses ...... 73 Estimation Models ...... 74
5. FINDINGS ...... 76
Trends in Daily News Coverage of Executions ...... 76 Multivariate Statistics...... 89 Total State Resident Population Variable ...... 89 Geographical (State) Control Variables ...... 90 Temporal Control Variables ...... 90 The Execution Variables ...... 91 Newspaper and Television Variables ...... 97 Non-Capital Punishment Variables...... 98 Supplementary Analyses for the Test of Sensitivity ...... 101
6. CONCLUSIONS ...... 119
A Summary of Empirical Findings ...... 119 Theoretical Implications...... 121 Policy Implications ...... 123 Limitation of the Study ...... 123 Recommendations for Future Research ...... 125 Conclusion ...... 126
References ...... 127
vii Biographical Sketch ...... 140
viii LIST OF TABLES
1 Overdispersion Test ...... 79
2 Comparative Counts of Mortality Detail File and Federal Bureau of Investigation Data: 1979- 1998...... 80
3 Summary of Counts of Homicide and Execution Data: 1979-1998...... 82
4 Descriptive Statistics ...... 85
5 The Extreme Homicide Counts for State-Days between January 1, 1979 and December 31, 1998...... 89
6 Negative Binomial Regression Models...... 92
7 Average Number of Days between Execution Dates by States ...... 97
8 The Sum of the Coefficient Values for 4-Week Period Surrounding Executions ...... 99
9 Negative Binomial Regression Models with the only "E" Variable...... 102
10 Negative Binomial Regression Models with the only 29-Day Dummy Variable ...... 106
11 Negative Binomial Regression Models with the only 15-Day Dummy Variable ...... 109
12 Negative Binomial Regression Models w/o Overlaps of 4-Week Periods of Executions .....114
ix LIST OF FIGURES
1 Number of In-State Newspaper Stories about Executions ...... 77
2 Number of National Television Stories about Executions...... 78
3 Histogram ...... 79
4 Mortality Detail File Data versus FBI Data on Homicide Trends in the United States, 1979- 1998...... 81
5 The Estimated Coefficient Graph for the 4-Week Period Surrounding Executions ...... 101
x ABSTRACT
While a very few death penalty studies find that the death penalty has the deterrent effect on homicides, the majority of the studies do not find. These contrasting and inconclusive findings raise an important question as to why the death penalty has little or no deterrent effect on homicides. As Phillips and Hensley (1984) pointed out, failure to find solid evidence of the deterrent effect may occur for one of two reasons: (1) either a deterrent effect can theoretically exist, but it does not actually exist, or (2) the methods used to find the deterrent effect are not sophisticated enough to reveal it. Theoretically, the deterrent effect of the death penalty could be achieved quickly and last only for a very short period of time (Andenaes, 1952; Phillips and Hensley, 1984). It is plausible that the deterrent effects of executions become strongest when the number of newspaper and television coverage of execution reaches its peak one day before and after an execution. However, as several researchers have repeatedly suggested that most of the past studies have employed annual and monthly homicide data (Donohue and Wolfers, 2005; Hjalmarsson, 2009, 2012; Katz, Levitt, and Shustorovich, 2003). In short, the main methodological limitation of the previous studies is that use of annually aggregated crime data may miss any deterrent effect in studies of the death penalty on homicides that are short-lived, that the number of killings deterred is too small to be detected excessively long temporal units such as years or months. The primary goals of this research were (1) to test whether an execution reduce murders on given day in the given state, (2) to assess whether an publicized execution has a deterrent effect on homicides on the given day in the given state, and (3) to determine whether the results of the analyses 1 and 2 remain consistent with temporal, regional, demographic and non-capital punishment variations. Data are collected from the Mortality Detail Files including the exact dates of homicides from January 1, 1979 through December 31, 2006. This study reveals a statistically significant deterrent effect of executions on homicides on the day of an execution. Some remote significant deterrent effects of execution on the days 5 and 6 afterward could not be interpreted as genuine deterrent effects because this pattern of the deterrent effects has nothing to do with the patterns of newspaper and television coverage of executions. However, this study find no evidence indicative of the deterrent effects of publicized execution on homicides. In addition, this study finds no evidence of a brutalization effect of executions on homicides.
xi In summary, the evidence suggests that executions do cause the homicide rates to drop, but only to a very small degree. It appears that, in the aggregate, the small number of executions carried out in a typical year in the United States has very little impact on the recent declines in the number of homicides. The robustness tests confirm the earlier findings, leading to the overall conclusion that executions do affect the behavior of prospective killers, but only for a very brief period of time in a modest way.
xii CHAPTER 1
INTRODUCTION
Whether the death penalty has a deterrent effect on homicides has been tested empirically and debated extensively for years in the United States (Baldus and Cole, 1975; Bowers and Pierce, 1975; Cameron, 1994; Donohue and Wolfers, 2005; Ehrlich, 1975, 1977; Fagan, 2005; Fagan, Ziming, and Geller, 2006). The vast majority of empirical studies, using different research methods, have produced mixed findings, but concluded that the death penalty has little or no deterrent effect on homicide (Albert, 1999; Avio, 1979; Bailey, 1977, 1979a, 1979b, 1980, 1990; Bailey and Peterson, 1989; Black and Orsage, 1978; Bowers and Pierce, 1975; Boyes and McPheters, 1977; Decker and Kohfeld, 1990, 1988, 1987; Donohue and Wolfers, 2005; Fagan, Zimring, and Geller, 2006; Forst, 1977; Fox, 1977; Fox and Radelet, 1990; Grogger, 1990; Hjalmarsson, 2009; Katz, Levitt, and Shustorovich, 2003; King, 1978; Kleck, 1979; Marvell and Moody, 1999; McFarland, 1983; Passell, 1975; Passell and Taylor, 1977; Peterson and Bailey, 1988, 1991; Sesnowitz and McKee, 1977; Sorenson, Wrinkle, Brewer, and Marquart, 1999; Stolzenberg and D’Alessio, 2004). More recently, in a meta-analysis of published studies, Yang and Lester (2008) continued to produce similarly inconclusive and contradictory findings: while cross-sectional studies found no evidence of the deterrent effect, time-series and panel studies found considerable evidence for it. Overall evidence from later body of longitudinal research led the scholars to conclude that the death penalty has a statistically significant deterrent effect on homicide. Nevertheless, at least until recently, there is a general consensus among scholars that the death penalty has no deterrent effect on homicide (Cameron, 1994; Donohue and Wolfers, 2005). These empirical findings raise important questions as to why it is that the longitudinal research reveals a deterrent effect of the death penalty, while the cross-sectional research reveals no such effect. More generally, why do some studies find a deterrent effect, while other studies fail to find the deterrent effect? As Phillips and Hensley (1984) pointed out, failure to find solid evidence of the deterrent effect may occur for one of two reasons: (1) either a deterrent effect can
1 theoretically exist, but it does not actually exist, or (2) the methods used to find the deterrent effect are not sophisticated enough to reveal it. Theoretically, it is perfectly plausible that perceptions of the risk of legal punishment would discourage prospective offenders from committing crimes (Zimring and Hawkins, 1973). However, perception of punishment risk is somewhat unstable, because experience with crime and punishment is likely to affect perceptions (Paternoster, 1987). Consequently, it is possible that the deterrent effect of individual punishment events, such as executions, could be achieved quickly and last only for a couple of days or for a very short period of time (Andenaes, 1952; Phillips and Hensley, 1984). If this is so, methodological differences may explain why most of the existing studies to date have generated no conclusive evidence on the deterrent effect of the death penalty. Most of the past studies have employed official crime data, for long time periods such as years (Hjalmarsson, 2009). Use of annually aggregated crime data may miss any deterrent effect in studies of the death penalty on homicide that are short-lived, that the number of killings deterred is too small to be detected excessively long temporal units such as years (Hjalmarsson, 2012; Land, Teske, and Zheng, 2012). Historical Background: The Use of the Death Penalty in the United States The history of capital punishment in North America can be divided into three distinct periods: (1) the “Pre-Moratorium Period” spanning almost 360 years from 1608 to 1967, starting with colonial America and ending with the late 1960s; (2) the “Moratorium Period,” 1968-1976, when the death penalty was not used because of doubts about its constitutionality; and (3) the “Post-Moratorium Period” beginning in 1977, one year after the Supreme Court of the United States made a series of decisions confirming that the U.S. Constitution allowed the death penalty in cases of murder and continuing to the present (For details, see Gregg v. Georgia, 1976; Jurek v. Texas, 1975; Proffitt v. Florida, 1976; Woodson v. North Carolina, 1976; and Roberts v. Louisiana, 1976). The distinction to be made between the later two periods rests in large part upon the major historical fact that no executions were carried out in any state for the nine years (1968 through 1976) between the other two periods.1 The first execution marking the beginning
1 This is referred to as the Moratorium Period. After Louis Jose Monge was hanged for murder at the Colorado State Prison on June 2, 1967, executions in the United States came to a temporary end until 1972. The United States Supreme Court’s 1972 decision in the case of Furman v. Georgia stated that the death penalty, as
2 of the Post-Moratorium Period occurred on January 17, 1977 when Gary Gilmore was executed by firing squad in Utah (Bowers, 1974; Paternoster, Brame, and Bacon, 2008). Fundamental changes to death penalty laws and practices, which took place gradually over the Pre-Moratorium Period were completed during the moratorium period. For example, death penalty statutes in the United States have narrowed the range of capital offenses for which the death penalty can be imposed. Before the Moratorium Period, capital punishment was not limited to murder but also was applied in cases of robbery, burglary, arson, and rape, among other crimes. But currently, the death penalty is imposed exclusively for first-degree murder (Bowers, 1974; The Death Penalty Information Center, 2015; Espy and Smykla, 2004). In practice, implementation of the death penalty exhibits a clear regional variation among the states. The North accounted for the highest percentage of U.S. executions from colonial times until the 1930s, but the South has carried out most of the nation’s executions from that time until now (Blomberg and Lucken, 2010; Bowers, 1974; Paternoster, Brame, and Bacon, 2008). After the Moratorium, executions were to be carried out under state law rather than county charter, and executions were no longer carried out in public. Executions are an extremely rare event in the United States. For example, the National Judicial Reporting Program indicated that among persons convicted of murder or non-negligent manslaughter in 2006, only 2% were sentenced to death, 23% were sentenced to life in prison, and 75% were sentenced to a probation or a prison and jail sentence (Rosenmerkel, Durose, and Farole, Jr., 2009). The cumulative number of executions represents just 16 % of all death sentences from 1977 through 2010 (The Death Penalty Information Center, 2015). Also, the annual number of executions went up sharply in the 1990s, but began to drop after peaking at 98 in 1999, and has declined since then (The Death Penalty Information Center, 2015). This trend
administered in most states, violated the 8th Amendment’s ban on cruel and unusual punishment and the 14th Amendment’s right to due process. In order to preserve laws authorizing capital punishment, all death penalty states had to revise their state criminal codes to restrict jury discretion in the application of the death penalty in accordance with the guided discretion required by the ruling in Furman v. Georgia decision. In all 35 retentionist states that passed new death penalty legislation to comply with the Supreme Court’s rulings between 1972 and 1976, penalty jurors had to follow strict federal death penalty guidelines when they choose a death sentence rather than a prison sentence for some forms of murder. As a result, the death penalty was reinstated as one of the sentencing options for capital murder in most states after late 1976.
3 has a significant implication for the present research: the number of homicides each execution might realistically be expected to deter is only a tiny proportion of the total homicides. The rarity of executions may help explain why most studies conclude that the death penalty is no deterrent to murder. Let us generously assume that one execution can prevent ten future homicides. The Bureau of Justice Statistics reports that the United States carried out 39 executions in 2013 (Snell, 2014). Thus, no more than 390 lives might have been saved by all executions in 2013. This estimated figure would be a very small proportion of all U.S. murders in 2013. Official crime statistics from the Federal Bureau of Investigation ([FBI], 2015) report 13,483 homicides in 2013. Executions thus would be responsible for a roughly three percent decrease in homicides over one year period. Because the number of executions is so small relative to the number of homicides, the deterrent effect of capital punishment, even if such an effect actually exists, would be very hard to detect, if one analyzed time units as large as years. On the other hand, if deterrent effects were concentrated in the days immediately before and after executions, these effects would be considerably more detectable when analyzing smaller time units, like days, because the number of “deterred” homicides could be far larger relative to the number otherwise expected for such a short period. Therefore, when trying to detect the deterrent effect of the death penalty on homicides, it is better to use the smaller time units of analysis.
Policy Implication Issues In much of the U.S., a hard line stance has been adopted by politicians and lawmakers to keep the homicide rates down. Some death penalty states have actively used the death penalty rather than imprisonment to punish murderers. Deterrence theory, which posits that more severe punishment will deter more criminal behavior (Gibbs, 1975), is the leading instrumentalist rationale for punitive homicide policies in retentionist states. Deterrence theory assumes that criminals fear capital punishment more than other punishments, such as life in prison without parole, and therefore executing murderers will reduce the number of homicides. Thus, for the crime control policy makers in the death penalty states, the relative effectiveness of different types of punishment seems to provide a sufficient basis for continuing the death penalty. Although enforcing the death penalty is much more expensive than keeping death- eligible murderers locked up in prison for life, the effect of execution on homicide rates is not as straightforward as expected (Harries and Cheatwood, 1997). In response to a wide gap between the expected and the actual impact of tough penal policies, some scholars who favor punitive
4 policies have attempted to explain why tough criminal justice policies do not work. Among these explanations, one approach is particularly worth mentioning: political influence. The issue of political influence in the field of deterrence has received little sustained attention. This silence in itself may reflect broader ambivalence about whether execution has a deterrent effect. Austin (2003) argues that crime control policies in the United States are impaired by overdependence on a wide range of nonscientific factors that include particular political agendas, political ideologies and political parties. He also argues that the particular interest of an incumbent political power group on the issue of crime and punishment often leads to the claim that increasing punishments would reduce crimes within a very short time. The Republican and Democratic parties and governments all are eager for quick solutions to reduce the costs of dealing with criminals, so they are favorably disposed toward implementing more punitive crime control policies because they believe that more severe punishment options would reduce crimes quickly. However, their approaches to crime prevention have turned out to be problematic. Politically driven policies can cause damage to society because many such crime control policies are not supported by sound empirical evidence. A causal relationship between criminal justice polices and crime rates has often simply been assumed to be true without rigorous scientific testing. When the U.S. Supreme Court considered the reinstatement of the death penalty in the mid-1970s, for example, it did not appeal to scientific evidence to show whether the death penalty had a deterrent effect on homicides. Ehrlich’s empirical study published in 1975 was extensively cited one year later in the U.S. Supreme Court’s rulings in both Fowler v. North Carolina and Gregg v. Georgia (1976). In the Fowler case, the Solicitor General presented Ehrlich’s empirical evidence to the Court and cited it to support the position that the death penalty functions as a significantly greater deterrent than less severe punishment options. In the Gregg case, by contrast, Justice Marshall’s dissenting opinion cited several empirical studies pointing out numerous methodological flaws in Ehrlich’s work. However, neither opinions for or against the death penalty relied on scientific evidence on deterrence. Justice Stewart’s statement of the Supreme Court’s ruling in the Gregg case rejected the scientific evidence on the grounds that no convincing empirical evidence either supports or refutes the view that capital punishment deters murderers (For details, see Gregg v. Georgia, 1976).
5 Crime control efforts traditionally have been directed at choosing the best method of decreasing crime rates. To make such choices intelligently, decision makers need credible, balanced information about the relative effectiveness of different punishment options. Accordingly, the present research will contribute to contemporary crime control policy in two ways. First, this study’s findings about the death penalty’s effect on homicides will be useful information to federal and state crime control policy makers. Because death penalty trials, when compared to non-capital ones, are obliged by state and federal law to have a longer and more complex judicial process, and because death row inmates in prison are treated differently from other inmates, the death penalty in the criminal justice system is much more expensive than alternative non-capital punishment options (Bedau, 1998; The Death Penalty Information Center, 2015). Thus, it is no wonder that policy makers want to know whether executions deter homicides. If the current study does not provide evidence supporting the effectiveness of the death penalty as a deterrent, then crime control policy makers should take into account the benefits and risks of capital punishment and consider eliminating the death penalty from the list of possible punishment options in the American penal system. On the other hand, if this study shows a reliable deterrent effect from the death penalty, policy makers could revise the death penalty process so as to maximize its deterrent effect. On the other hand, the current research might provide a rationale for saving the lives of prisoners currently sentenced to death. In the American penal system, capital punishment is the severest punishment option: It punishes the most violent offenders by taking their lives. Nevertheless, for some, the use of the death penalty could be justified under the notion of general deterrence, as the life of one guilty person executed in the present is exchanged for saving the lives of innocent people in the future (Bowers, 1974; Miethe and Lu, 2005; Paternoster, Brame, and Bacon, 2008; Zimring, 2004). However, if this study does not find support for a deterrent effect of the death penalty in reducing homicides, policy makers should consider whether the death penalty takes human life without good reason. In conclusion, the results of this study will have the potential to provide more credible empirical evidence on death penalty deterrence, because the research will employ more appropriate, up-to-date and sophisticated data and research design to estimate the impact of the death penalty on homicide rates. Furthermore, if it turns out that the death penalty does not
6 reduce homicide, this could encourage its elimination, which could save many millions of dollars in tax money, which could be redirected to more productive endeavors. Theoretical Issues The death penalty may have some deterrent value. Homicides might be deterred if executions increased the perception among prospective killers that homicidal actions can lead to an execution (Zimring and Hawkins, 1973). However, any one execution may deliver a deterrent message only to a small number of people who are likely to commit a murder in the near future (Cook, 1980; Kleck, Sever, Li, and Gertz, 2005). For example, consider the case of Aileen Wuornos, who, in one state, over the course of two years, killed seven men who she claimed had raped or attempted to rape her while she was working as a prostitute. Although she argued that all of the homicides were committed in self-defense, she was convicted and sentenced to death for six homicides. When her execution was imminent, many stories about her appeared in the national press because she was a convicted serial killer. During the relatively short time period when her story was in the news, the threat of execution may have affected other prospective offenders, but only a select few, such as other prostitutes. Thus, the deterrent effect of the death penalty may be minimal, and possibly confined to a small subset of potential killers. Homicides can also be prevented in other ways that do not involve deterrence (Andenaes, 1952; Bowers, 1974; Gibbs, 1975; Paternoster, Brame, and Bacon, 2008; Zimring and Hawkins, 1973). For example, imprisonment may prevent future murders by depriving known killers of the opportunity to commit further murders. As Kleck (1979) pointed out, most homicide offenders are likely to have a prior arrest record of violent crime and to be incarcerated in prison for violent crimes or murder prior to the commission of the homicide. Alternatively, murders could be prevented by strengthening moral inhibitions against murder and other violence. To disentangle the deterrent effect of executions on homicides from the effects of other preventive mechanisms of punishment, a framework is needed to simultaneously analyze the effects of preventive mechanisms on murders. A few scholars have provided some useful hints about how to accomplish this. For example, Andenaes (1952) pointed out that a deterrent effect can be achieved very quickly, whereas a moralizing effect takes longer. Likewise, using the smallest temporal unit of analysis, such as days, can help distinguish the deterrent effect from either incapacitative or moralizing effects. The deterrent effect of execution could be far stronger
7 on days close to the execution date, whereas neither prison population sizes nor the morality of the population much from day to day. In contrast to claims of a negative effect of the death penalty on homicides, some scholars posit that the death penalty has a “brutalization effect” that serves to encourage, rather than discourage, homicide (Bowers and Pierce, 1975; Thompson, 1997, 1999). The rationale behind the brutalization effect is that prospective criminals identify with the government and excuse their homicidal behaviors as justified because the government, engages in killing for purportedly legitimate reasons. In other words, prospective murderers consider the death penalty to be “legalized homicide,” which they see as lending legitimacy to their own actions (Mandery, 2005; Thompson, 1997, 1999). Because the brutalization effect of the death penalty on homicides is considered contrary to economic theory, it has been often ignored by economists. Nevertheless, the brutalization effect has frequently been discussed in empirical studies conducted by criminologists (Bullock, 1991; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; Graves, 1956; Stolzenberg and D’Alessio, 2004; Thompson, 1997, 1999). It is also possible that the negative relationship between the use of the death penalty and homicides is spurious, due to the confounding influence of omitted variables that have a causal effect on both variables. Some antecedent variables may have a positive effect on one variable and a negative effect on the other one. For instance, suppose that a community is extremely conservative in its attitude towards criminals or deviant behavior. When the population in a given area at a given time strongly disapproves of crime, this will discourage crime through informal social control mechanisms like verbal expressions of disapproval, termination of social associations with offenders, and so on. This higher level of disapproval can, however, also generate more support for legal punishment – demands for more prison facilities, harsher sentences without parole, longer prison sentences, and so on. Consequently, assessing the relationship between use of the death penalty and homicides is fraught with difficulty due to the influence of spurious omitted variables. Causal order is another potential problem that a positive association between the number or rate of executions and the homicide rate may reflect an effect of homicide rates on use of the death penalty rather than the brutalizing effects of the death penalty on homicide rates. This could occur either because a large number of murders results in more people being sentenced to
8 death, or because increased murder rates increase popular support for harsher sentences, such as the death penalty. It is important to note that the levels of social disapproval of crime are not likely to change enough from day to day to have any measurable effect on the number of homicides. Likewise, it is impossible for demographical, social, and technological changes to have a noticeable effect on changes in the number of homicides from one day to the next. Thus, research examining daily homicide counts has advantages in separating deterrent effects of executions from the effects of other factors that influence homicide. Statement of the Problem Over the past decades, questions have been raised about the deterrent effect of the death penalty on murder: Does the death penalty deter homicides? How long does the deterrent effect of the death penalty last? If it does, how many homicides might be deterred by the application of the death penalty? Under what conditions would the impact of the death penalty be the greatest? Or, does the death penalty actually increase homicides? These questions have not been satisfactorily answered, because the studies reported in the past few decades have yielded inconclusive and sometimes conflicting results. In an extensive overview and synthesis of more than 100 identified and relevant studies, clear-cut evidence on the deterrent effect of the death penalty was found only in studies with panel and time-series research designs (Yang and Lester, 2008). Yet, it has been found that the results of recent econometric panel studies supporting a deterrent effect of execution on homicides are not robust enough to rule out alternative explanations (Donohue and Wolfers, 2005). One reason sometimes given for the mixed results is the fact that only a few earlier studies employed the most appropriate data needed to address specific research questions (Dann, 1935; Donohue and Wolfers, 2005; Graves, 1956; Grogger, 1990; Hjalmarsson, 2009; Katz, Levitt, and Shustorovich, 2003; Phillips, 1980; Phillips and Hensley, 1984; Stack, 1995; Savitz, 1968). For example, Hjalmarsson (2009) pointed out that most of past studies have employed temporary aggregated data. Donohue and Wolfers (2005) argued that the effects of the death penalty are not large enough to be detected when analyzing annual homicide data. Katz, Levitt, and Shustorovich (2003) have pointed out that the amount of homicide rate variation deterred by executions may be too small to be detected, even if the death penalty has a substantial deterrent effect. Thus, one major methodological flaw in most prior studies was the use of homicide
9 counts for long time periods such as years or months. Even if executions deterred some killers, the effect might be hard to detect using such unsuitably long temporal time periods, because the number of homicide prevented by one or two executions in a given year is likely to be a very small proportion of the total number of homicides committed across the full one-year period. To reliably estimate whether the death penalty has a deterrent effect, it is helpful if the smallest temporal unit of analysis is analyzed, to allow researchers to detect any short-term fluctuations in homicide counts that may occur immediately before or after an execution. Although a few studies conducted during the past decade have employed daily homicide data, most of them have bear limited by their study of short time periods and limited geographical areas. Hence, employing a national sample and a longer sample period is likely to provide a more reliable estimate of any short-term effect of the death penalty on homicides. Summary As the brief overview of the history of capital punishment shows, the United States has seen a steady decline in executions, first from its peak in the 1930s, and then its post-moratorium peak of 98 in 1998. The infrequency of executions may make it hard to detect any deterrent effect because the aggregate impact for large areas like states is so small relative to their homicide totals. This problem is further aggregated when researchers use a longer temporal unit of analysis such as years or months. The methods of the previous studies may simply be too crude to detect any effect. Thus, the findings to date against on the deterrent effect of capital punishment on homicides should be interpreted with caution, because all but handful of the previous studies have been based on annual and monthly data. Therefore, the current study aims to (1) overcome the methodological limitations of past studies, (2) test the causal effect of the death penalty on homicides with improved methodologies, and (3) provide a theoretical explanation for any effects detected. In addition, this study is intended to produce practical findings that may be useful in influencing on policy makers. The next three chapters will present relevant theoretical explanations, a literature review, and the research methodologies and design of this dissertation research.
10 CHAPTER 2
THEORY
This chapter reviews the main theoretical issues relevant to the deterrent effect of capital punishment on homicides. Although many theoretical mechanisms are proposed to explain how legal punishment reduces crime, general deterrence theory is the most widely applied mechanism in the death penalty research. In contrast, the brutalization mechanism is used to explain why capital punishment increases homicides. The chapter also will address the ways that prospective offenders perceive the risks of the death penalty, as well as possible factors other than the death penalty that could conceivably influence homicides. Deterrence Theory General Overview An economic approach to crime and punishment, such as the Ehrlich paradigm, forms the rational criminal argument and its influence is found in the classical school of criminology.2 Implicit in deterrence theory that was popular among crime control advocates in the 1970s is the expected utility principle in the rational choice model (RCM), which assumes that people are utility maximizers who can consider all costs and benefits accruing to them from a particular course of action and make an optimal choice that maximizes benefits and minimizes costs (Kubrin, Stucky, and Krohn, 2008; Lilly, Cullen, and Ball, 2010). When the rational choice model is applied to deterrence doctrine, potential criminals have full knowledge of the costs and benefits of legitimate versus illegitimate opportunities and soon decide to behave in a rational way as they decide whether or not to engage in illegitimate behavior. Accordingly, prospective offenders will be more likely to offend only if they consider that the commission of illegitimate behaviors yields more productive and beneficial results than the commission of legitimate behaviors (Becker, 1968). For deterrence theory to be effective, its fundamental requirement is
2 Gary S. Becker’s (1968) seminal paper, “Crime and Punishment: An Economic Approach,” was the theoretical groundwork for Ehrlich’s (1975) empirical research on capital punishment and its replication studies. Becker (1968) argued that most sociological theories of crime causation were based on an incorrect assumption that all criminals were fundamentally irrational, deviant, or abnormal.
11 that potential offenders must be optimal utility producers who have solid knowledge about all the expenses associated with legitimate versus illegitimate behaviors and acknowledge that crimes committed will be of no benefit to themselves. Nevertheless, many may question the underlying assumption in the rational choice model that people are complete rational actors who can calculate the likely costs and benefits of an action, without being influenced by his/her own knowledge, state of mind, or ability (Blumstein, Cohen, and Nagin, 1978; Cook, 1980). In reality, conformed people, as well as prospective criminals, do not satisfy the fundamental assumption of the rational choice model, which lacks a necessary element for deterrence theory to be effective. Even those who conform to society frequently tend to act against their own interests. For example, people tend to prefer simple problem solving or decision making techniques that may produce nonoptimal outcomes. Following Simon (1955), Cook (1980) pointed out that human beings often make inconsistent or irrational decisions because they have imperfect information about the world they live in. Human beings often employ experience-based techniques, such as rule of thumbs, educated guess, intuitive judgment, or common sense when they must make decisions. In addition, even criminals deviate from being rational calculators because many are alcoholics or drug addicts and have poor anger management skills. At the time of their offense, many of these offenders may have an intellectual disability, suffer from a mental disorder, or lash out impulsively because they cannot control their anger if provoked. In addition, most active criminals have little knowledge about levels of criminal punishment until they are faced with their own sentences in criminal court. In reconsidering the expected utility principle of rational choice model, it can be suggested that people do not always have to be fully informed or perfectly rational utility maximizers when they must choose one option out of many desirable choices. Because we live in overwhelmingly complicated and interdependent societies, many aspects of daily life are beyond human capacity to completely predict or understand. When they are faced with simple social, cultural, political, or economic problems, people spend days in trying to figure out what factors are wrong and why. Therefore, much of everyday life processes gets so complicated that people often do not make the best choice because of their limited rational capacity to comprehend.
12 Definition Gibbs (1975: 2) defined deterrence as “the omission of an act as a response to the perceived risk and fear of punishment for contrary behavior.” Within the definition of deterrence, the word “omission” can represent either of two possibilities: (1) prospective offenders may be entirely deterred from committing crimes for fear of legal punishment; or (2) they may curtail or restrict their criminal activities (Stafford and Deibert, 2007). Deterrence can also be understood in terms of the pleasure and pain associated with a certain type of crime. People commit crimes to obtain emotional benefits, such as pleasure or enjoyment, as well as material gains, such as money or properties, to prevent crime, then, the pains of legal punishments must outweigh these pleasures, thereby dissuading prospective offenders from offending in the future. Therefore, deterrence may be expressed in one simple proposition: if the criminal justice system responds to a type of crime with great degrees of actual certainty, celerity, and severity of legal punishment, then such a punitive sanction will discourage or impede the rate of that crime. Certainty refers to the probability of getting caught, convicted, and punished if found guilty. The greater the probability that crime prompts punishment, the greater the certainty of punishment. Celerity refers to the swiftness of detection, apprehension, impartial trial process, and punishment for a crime. Severity refers to the harshness with which punishment is applied for commission of the crime. The harsher the punishment, the greater the severity of punishment. Deterrence cannot occur without prospective offenders’ perceptions of punishment risk (Gibbs, 1975; Kleck, Sever, Li, and Gertz, 2005; Spelman, 1994; Zimring and Hawkins, 1973). For example, prospective offenders do not refrain from committing criminal acts unless they perceive the actual risk of criminal punishment, such as “death sentence,” “three strikes, you’re out,” or “truth in sentencing” policies. The core proposition of deterrence theory can be summarized thusly: “the greater the perceived certainty, severity, and swiftness of legal punishment, the lower the crime rate will be” (e.g., Kleck, Sever, Li, and Gertz, 2005: 625 - 626). Types of Deterrence The types of deterrent effects depend on the degree to which crime will be deterred through legal punishment, the relative effectiveness of two comparable legal punishments in reducing crime rates, and those who will suffer pain or deprivation inflicted by legal punishment. There are four basic types of deterrence: partial, marginal, specific, and general (Gibbs, 1975;
13 Zimring and Hawkins, 1973). Partial deterrence denotes a situation in which the threat of legal punishment has some deterrent value, although the punishment threats do not completely deter crime. Consider the typical example of two drivers who are traveling at 80 miles per hour in a 60 mile per hour zone in a local jurisdiction. In response to a notice that monetary fines for speeding have become tougher in recent years, the first driver may reduce his or her speed to 70 miles per hour and the second driver may also reduce his or her speed to 55 miles per hour. While the first driver exceeded the speed limit by 10 miles per hour, the second driver was below the speed limit by 5 miles per hour. Although the first driver is driving slow but still exceeding the legal speed limit, it may be said that he or she has been partially deterred. In contrast, it can be said that the second driver has been completely deterred because he or she, who initially was in full compliance with the legal speed limit, now is below it. Marginal deterrence refers to the comparison of the relative effectiveness of different types of punishments. As Zimring and Hawkins (1973) pointed out, the main task of the marginal deterrent effect is to discover whether a more severe punishment could more effectively deter crime. The marginal deterrent effect can be applied to both general and specific deterrents. For example, if DUI drivers punished with mandatory jail sentences had lower recidivism rates than those punished with monetary fines, the jail sentences would be considered to have a stronger marginal deterrent effect as a specific deterrent for driving under the influence. The debate over capital punishment usually revolves around the marginal deterrent effect: whether the death penalty has more deterrent effect on murder than the alternative punishment of life imprisonment without possibility of parole. The question of whether prospective offenders may have prior experience with legal punishment before contemplating offenses can explain a similarity between specific and general deterrence. Specific deterrence occurs when punished offenders will be less likely to repeat the same criminal acts after being punished for certain illegitimate acts because they fear being punished again for the same acts; general deterrence occurs when prospective offenders refrain from committing crimes because are aware that others have been punished for an illegal act and they fear receiving the same punishment as the offenders. Specific and general deterrence both assume that past experiences of being punished, either directly or indirectly, may impact future decision making among those who contemplate illegal acts. Therefore, deterrence theory
14 illustrates that if either specific or general deterrent effects are to be achieved, the target audience must be aware of the increased risks of being caught and punished (Zimring and Hawkins, 1973). The distinction between specific and general deterrence is widely recognized and commonly used to classify different types of deterrence studies (Cook, 1980; Nagin, 1978; Zimring and Hawkins, 1973). Specific deterrence occurs if an offender refrains from committing additional crimes in the future as a result of his or her own experience of being legally punished in the past, and enhanced fear of being punished in the future. Recidivism is used to measure the specific deterrent effect of punishment. For example, a short-term prison sentence may produce specific deterrent effect in that the sentence in prison will cause an inmate to suffer unpleasant experiences in prison and discourage further criminal activity by intensifying his fear of being punished against the future. In contrast, general deterrence occurs when potential offenders refrain from committing crimes because they are aware that others have been punished for committing crimes. For example, the general deterrent effect occurs when the execution of convicted murderer deters other prospective offenders from committing murders. Geographical or temporal comparisons of crime rates are typically used to measure the general deterrent effect of punishment. General deterrence is potentially more influential than specific deterrence from a crime control perspective in that it can deter more prospective offenders.3 While general deterrence could prevent a large number of potential offenders from committing offenses, specific deterrence can affect only the small number of offenders who were punished (Kleck, Sever, Li, and Gertz, 2005). From a general deterrence prospective, crime rates might be higher if criminal punishment failed not only to deter punished offenders from committing further offenses, but also failed to prevent other potential offenders in the general public from committing crimes. If general deterrence works perfectly, therefore, crime control policy would be a very economical method to reduce crime rates because punishment of one criminal would set an example and thus would prevent many other prospective offenders from committing crimes (Andenaes, 1974). General deterrent effects should be strongest when legal threats are communicated to many. Prospective offenders may hear about the possible legal punishment in a variety of ways, such as the news media, visible presence of law enforcement, and personal experience and
3 Andenaes (1966: p. 955) argued in the same vein, “General prevention is more concerned with the psychology of those obedient to the law than with the psychology of criminals.”
15 observation (Cook, 1980; Zimring and Hawkins, 1973). While these communication channels are unable to deliver complete information about possible criminal punishment, these channels offer the greatest opportunities to remind prospective criminals that punishment is a real possibility. Based on this rationale, a few prior studies have measured some lag and lead effects of executions (Grogger, 1990; Phillips and Hensley, 1984; Phillips, 1980). As the number of news stories covered by the news media increases prior to the execution day, people will talk about incoming execution and perceive their risk of executions. In other words, the deterrent effect could actually occur before the actual execution event because of the news coverage of execution. Therefore, the deterrent effect should be strongest when the number of newspaper and television stories about executions reaches its peak. The Simultaneous Relationship between Executions and Homicide Rates Homicide rates and capital punishment may simultaneously influence each other. Generally, deterrence theory proposes that increases in actual certainty, severity, or swiftness of legal punishment causes increases in perceived certainty, severity, or swiftness of punishment, which leads to decreases in criminal activity (Gibbs, 1975). Such a theoretical framework predicts a negative causal relationship between current perceptions of execution risk and future homicidal behavior - if people perceive a stronger risk of execution, they will be less likely to engage in homicides. It is, however, also possible that higher homicide rates may reduce the probability of execution. According to the National Academy of Sciences (NAS) (2012), a continuing upward trend in homicides may contribute to increased court workloads for homicide cases, with the result that fewer resources can be devoted per homicide case in gaining convictions. Accordingly, there would be an observed negative association between homicide rates and death sentencing rates due to the overloading of court resources, rather than deterrence. On other hand, a continuing upward trend in homicides would lead to the misleading impression of a brutalization effect. When homicide rates grow steadily, public concern about violence could intensify and juries in the criminal court might be more likely to impose death sentences rather than life sentences. Accordingly, there would be an observed positive association between homicide rates and death sentencing rates that might be mistaken for a brutalization effect. Thus, it is important to recognize that the causal effect of executions on homicide rates needs to be separated from a reverse causal effect of homicide rates on execution frequency when the deterrent effect of executions on homicides. However, many previous empirical studies
16 failed to address causal order between executions and homicide rates. Accordingly, some scholars have argued that a longitudinal design, such as a panel design, is better for estimating the deterrent effect (Nagin, 1999). Other Possible Preventive Mechanisms for Punishment As Gibbs (1975: 57) discussed, deterrence is one of 10 possible explanations why legal punishment may prevent crimes. In contrast to deterrence mechanism, which postulates that the threat of punishment will cause prospective offenders to refrain from committing a crime even if they contemplate it, nine other preventive mechanisms operate to prevent crimes in different ways, including incapacitation,4 punitive surveillance,5 enculturation,6 reformation,7 normative validation,8 retribution,9 stigmatization,10 normative insulation,11 and habituation.12 As Nagin (1978b) argued, general deterrence is often intertwined with these nine preventive mechanisms. In finding the observed negative relationship between the death penalty and homicide rates,
4 As Gibbs (1975: p. 58) defines, “some punishments diminish or remove opportunities for certain types of crime.” Accordingly, prospective offender will be deprived of an opportunity to commit crimes against society usually by being locked up, or by being made incapable of doing something harm. To keep repeated criminals out of society, the incapacitative mechanism of punishment operates on the understanding that the criminal justice system increases sentence severity for all offenders convicted of a particular offense, such as the “Truth in Sentencing,” “Three Strikes and You’re Out” laws, and other habitual offender laws. However, it should be kept in mind that incapacitation differs from deterrence in that it may neither change people’s willingness nor desire to refrain from criminal acts, not alter future criminal behavior. 5 Probation or parole is punishment when it is perceived by the client as discomforting (Gibbs, 1975: 63). 6 Respect for and socialization for norms enforceable by laws are furthered by instances where violators are punished (Gibbs, 1975: 68). 7 This preventive mechanism originates in the Christian view that everyone should follow the law and be punished if they fail to obey it. The ultimate purpose of punishment in the Bible is to turn criminals into law-abiding people through repentance, reconciliation, and changing life for the better. Therefore, a criminal refrains from criminal acts after punishment, and does not even contemplate committing the acts (Gibbs, 1975: 72). 8 Negative evaluations of illegal acts are maintained or intensified by legal sanctions for those acts (Gibbs, 1975: 80). 9 To the extent that victims demand retribution, punishment of crime is at the same time vengeance and a means to control vengeance (Gibbs, 1975: 82). This means that if offenders infringe on rights of victims by choosing to commit illegal acts, they deserve to be punished. The basic notion of retribution is to punish all offenders who violate the same norm equally. In contrast to deterrence and rehabilitation mechanisms, which aim to discourage prospective offenders from committing future crimes, retribution mechanism aim to punish offenders for what they have done in the past. 10 Anticipation of stigma may deter the typical citizen more than the punishment itself (Gibbs, 1975: 84). 11 Assuming that the influence of the offender in some cases would have involved more definitions favorable to crime for the offender’s associates, removal of the offender reduces crimes (Gibbs, 1975: 87). 12 Habitual conformity may develop from conformity that was initially affected by threatened punishment (Gibbs, 1975: 89).
17 Stack (1998, 1990) argued that this might result from normative validation13 of capital punishment, rather than general deterrence. It should be kept in mind that other punishments besides executions can affect homicide rates. The National Academy of Sciences (NAS) (2012) argued that existing death penalty studies did not tell us much about whether there is a deterrent effect of the death penalty, because of their failure to control for noncapital punishment variables such as prison sentence length. Reviewing previous death penalty studies, the NAS found that the same states that have more executions also have larger prison population rates and longer prison sentences. Thus, analysts must control for measures of noncapital punishment in order to rule out the possibility that larger prison populations or longer prison sentences actually reduce homicide rates, rather than executions. The Brutalization Effect of Executions on Homicides In contrast to the theoretical predictions of deterrence theory, some past studies have found a counterdeterrent, or brutalization effect of the death penalty (Bailey, 1983; Bowers and Pierce, 1980; Cochran, Chamlin, and Seth, 1994; Decker and Kohfeld, 1990; King, 1978; Phillips, 1980; Thompson, 1997). Thus, some scholars argue that executions may increase rather than decrease the number of murders. In the capital punishment literature, it should not be overlooked that executions may affect the overall levels of homicide in the contrasting way of the theory: the brutalization argument, which suggests that executions encourage prospective murderers to commit murder, as well as the deterrence argument (Bowers and Pierce, 1980; Cochran, Chamlin, and Seth, 1994; Thompson, 1997). There are several reasons why executions could stimulate more homicide than they deter. First, executions may contribute to creating a climate of brutal violence and set an example of state killing for private citizens to follow. More than 200 years ago, Cesare Beccaria argued in his 1764 treatise: “the death penalty cannot be useful, because of the example of barbarity it gives men” (Paolucci, 1975: 50). For Beccaria, “It seems to be absurd that the laws, which are an expression of the public will, which detest and punish homicide, should themselves commit it, and that to deter citizens from murders they order a public one” (Paolucci, 1975: 55). Accordingly, Beccaria believed that executions would not be effective in reducing the number of
13 Gibbs (1975: 79) points out that punishment reduces crime through normative validation theory. A publicized execution may reduce homicide because prospective murderers think that homicide is unacceptable behavior. The deterrence and normative validation explanations may work to reduce homicide at once.
18 murders because they would encourage the idea that some murders could be considered justified, just like state-sponsored killings. Andenaes (1966) argued that capital punishment exerts two contrasting effects at the same time: it attempts to remind society that life is the highest human value, to be respected and protected, while the execution of perpetrators undercuts the value of respect for life. Finally, executions may serve to inspire a potential killer to adopt alternative identification process, different from the one implied by the deterrence theory (Bowers and Pierce, 1980). For example, the deterrent effect occurs when prospective killers identify with killers who were executed. In contrast, brutalization is likely to occur when the prospective killer identifies someone who has offended him with the killer who was executed, the prospective killers will identify themselves with the state as executioner. Under these circumstances, executions may reinforce the belief that lethal vengeance is justified. Bowers and Pierce (1980: 482 - 483) offered a number of ways that a would-be murderer could identify with some party other than the executed killer.14 Cochran, Chamlin, and Seth (1994) argued that capital punishment produces both deterrent and brutalization effects on homicide at the same time, which prevents some types of homicide while encouraging others. These authors asserted that executions in Oklahoma produced a brutalization effect on stranger homicides. They attributed it to the possibility that state-sponsored execution exercises a dehumanizing effect on the populace by sending the message that killing can be legitimized. Likewise, Thompson (1997) argued that Arizona’s first executions in more than 29 years produced a brutalization effect on some types of homicides and pointed out that imitation and identification may serve to produce a brutalization effect. Full Rational Choice and Limited Rational Choice Models of Crime and Deterrence Full Rational Choice Model of Crime and Deterrence In its simplest form, the rational choice model (RCM) generates easy and testable predictions and clear implications for crime control policy (i.e., Becker, 1968; Ehrlich, 1973). Though it has been used to explain economic behavior, it also has been applied to explain and
14 The homicidal act of the person executed; the right of a person to kill someone who has wronged the potential murderer; the excitement of committing a murder or engaging in criminal activity in which a murder might occur that could lead to execution; the stimulation of a life being taken; a feeling of guilt or suicide that would be resolved by execution; a chance for publicity and the opportunity to air feelings, views; and, an act to imitate.
19 predict all or most kinds of criminal behavior.15 Based on the neoclassical economics principle of the maximization of utility that humans make choices in a deliberate way to maximize their happiness or utility and minimize their costs, the rational choice model can be expressed in the simple proposition: people will choose the option with highest expected utility among alternative courses of action prior to making decisions. In other words, the rational choice model (RCM) stipulates that people consider all possible legitimate and illegitimate alternatives to achieve goals, estimate the costs and benefits of each alternative, and assign different weights to each cost or benefit with their relative values and probability estimates, which lead to calculate the sum of the weighted costs and benefits of the best course of action (Kleck, in press: pp. 2 - 3). Under the rational choice perspective, the decision with the highest expected utility is most likely to produce optimal results. As in the expected utility theory, or the sum of the weighted costs and benefits of a choice, there are two contrasting forms of the theory, depending on the degree to which the actual probabilities of legal punishment are accurately known by decision makers: objective expected utility theory and subjective expected utility theory. The subjective expected utility theory is based on the assumption that people hold a variety of possibly erroneous ideas about the actual probabilities of likely consequences of a given choice: the objective expected utility theory assumes that people have accurate knowledge about the consequence (Kleck, in press). The rational choice model (RCM) of criminal behavior has many criticisms. There are severe limits on information regarding legal punishment; people do not consistently decide in accordance with the principle of expected utility maximization; instrumental rationality does not apply in the presence of strong moral norms; people do not necessarily make separate decisions about whether to commit individual crimes; people do not decide in social isolation; nonmaterial costs and benefits may matter more than material ones; people are driven by emotion, much of it genetically determined; and, punishment can encourage crime as well as discourage it (Kleck, in press: pp. 13-25). While most of these criticisms are invalid, irreconcilable, and weakly arguable, a few are developed with logically strong and solid foundation. For example, Kleck (in press: pp.
15 The rational choice model can take a variety of forms, from the “economic approach” to crime of economist Gary Becker (1968) in the simplest one to alternative ones, including the “calculus of pleasures and pain” of utilitarian philosopher Jeremy Bentham (1789), the “rational choice” and “situational crime prevention” perspectives of criminologists Cornish and Clarke (1985), and the “routine activities theory” of sociologists Cohen and Felson (1979).
20 6 - 25) devoted several pages to clearing misleading ideas away and listed a number of strongly arguable criticisms.16 The process by which decisions with the highest expected utility are formed does not necessarily produce optimal results. This could occur if people select a seemingly best alternative when they possess limited, or inaccurate information about expected costs and benefits of alternative courses of action, and consider only a fraction of what information they do possess (Kleck, in press). Thus, lack of accurate, complete, and up-to-date information on likely costs and benefits of alternative courses of action produces a lack of correspondence between actual and perceived levels of punishment. In sum, the rational choice model has ignored the process by which perceptions of risk are formed and the possibility that actual level of punishment risk may have no or little impact on those perceptions. Limited Rational Choice (Constricted Rational Choice) Model of Crime and Deterrence The alternative to the full rational choice model is the constricted rational choice model (CRCM), by which humans take account of only a fraction of all the costs and benefits associated with their legitimate and illegitimate decisions, and the contingencies enumerated are slightly related to decisions as to whether and how often they commit a crime17 (Kleck, in press). The core of the constricted rational choice approach can be applied equally to average offenders and normal people who present themselves as highly rational and reasonable decision makers. Given that it is an extremely rare situation when people possess a large amount of accurate information about the costs and benefits of all general and specific crimes, prospective offenders obviously have very limited information on the contingencies of committing a crime, and much of the information the offenders use is inaccurate and outdated (Kleck, in press).
16 For example, strongly arguable criticisms include: there are severe limits on information regarding legal punishment; people do not consistently decide in accordance with the principle of expected utility maximization; instrumental rationality does not apply in the presence of strong moral norms; people do not necessarily make separate decisions about whether to commit individual crimes; people do not decide in social isolation; nonmaterial costs and benefits may matter more than material ones; people are driven by emotion, much of it genetically determined; punishment can encourage crime as well as discourage it; and, what kinds of human behaviors do accord with the rational choice model? (Kleck, in press: pp. 13-25) 17 The term “constricted rationality” may be confused with the term “limited rationality.” While the term “constricted rationality” used in Simon’s work (1957) represents the extreme degree to which rational choice has a very limited use to understand humans’ behavior, the term “limited rationality” used in Cook’s work (1980) reflects an exceptional situation in which human’s behavior deviates from the predictions made by the rational choice model (Kleck, in press: p. 45).
21 Economists committed to the traditional utility maximization model view potential criminals as people who make exhaustive and complex calculations leading to an optional choice, but other scholars view them as people who make a few simplified assessments of their alternative courses of action and make decisions that can be far short of optimal (Cook, 1980). As Cook (1980) pointed out, “the existence of a strong deterrent effect does not require that potential criminals be fully informed or fully rational in their crime decision.” Cook (1980) advocated a limited rationality model of decision making that recognized limitations on people’s capacity to acquire and process information. People tend to economize on this scarce capacity by adopting rules of thumb, or “standing decisions,” which eliminate the need to analyze every decision anew. Even a person whose judgment is impaired by emotion or inebriation may still be guided by his or her personal standing decisions, which in turn may reflect a concern with the threat of punishment that was developed on previous occasions. An increase in the threat of punishment may have the effect of persuading more people to adopt such standing rules, thus inhibiting them from acting “on impulse” when an attractive crime opportunity arises. Threat Communication as Proxies for Perceptions of Execution Risk As the National Academy of Sciences (2012) pointed out, one of the main reasons why previous death penalty studies have failed to provide clear evidence of whether capital punishment has a deterrent effect on homicide rates is that researchers have failed to directly measure prospective murderers’ perceptions of the risk of execution. Many researchers accept without reservation the assumption that aggregate-level perceptions of the risk of punishment will be closely related to actual risks (Cook, 1980). Many researchers, especially economists, have preferred macro-level research to individual-level research, and question the validity of responses to questions used in the survey research that measure the individual-level perceptions of the risks of legal punishment (Kleck, in press). In addition, without conducting empirical test of the assumption, prior death penalty studies have presumed that individuals contemplating homicide actually perceive the risk of execution on the basis of the subjective probabilities of arrest, conviction, and execution (NAS, 2012). Consequently, researchers have employed measures of actual execution risk, such as observable frequencies of arrest, conviction, and execution, as proxies for perceptions of execution risk. Thus, researchers only indirectly test the deterrence proposition that capital punishment deters homicides, inferring it from negative associations between aggregate levels of capital punishment and homicide rates (Kleck, in press).
22 Prior research, however, has indicated that perceptions of the risk of legal punishment have little relationship with actual levels of risk. Thus, the latter cannot serve as proxies for the former. An alternative method is therefore needed to indirectly measure variation in the perception of execution risk. Cook (1980: 222 - 226) discussed a variety of communication channels by which information on the threat of capital punishment is communicated to prospective offenders, including the news media,18 visible presence of enforcers,19 personal experience and observation,20 prospective offenders’ own experiences,21 and rumors and gossip from potential criminal associates.22 However, the poor quality of information about punishment transmitted through these communication channels makes it unlikely that prospective offenders will accurately perceive the certainty, severity, or swiftness of punishment (Kleck, Sever, Li, and Gertz, 2005). Indirect measurement of perceptions of execution risk could be achieved by measuring volume of information flowing through the most reliable channel of communication. Although information on the threat of execution may be transmitted to prospective murderers over many communication channels, few of the flows of information could be empirically measured in the macro-level death penalty studies. It is possible, however, to measure the amount of news coverage dedicated to executions. Perceptions of execution risk should be higher when there are more news stories about executions. Researchers have suggested that the deterrent effect of punishment is greater when punishment events receive much more extensive news media attention than usual punishment events (Jacoby, Bronson, Wilczak, Mack, Suter, Xu, and Rosenmerkel, 2008; Kleck, Sever, Li, and Gertz, 2005). Therefore, news stories about executions
18 Information on the risks of criminal justice activities is transmitted by the media. For example, prospective offenders update their estimates of the risks, primarily through news reporting of legislative actions, newsworthy crimes and criminal court cases, introduction of news programs and policies, etc. (Cook, 1980: 222). 19 If the police are seen frequently in an area, potential criminals may be persuaded that there is a high likelihood of arrest in that area because of presumed fast police response and the chance that they will happen on the scene while the crime is in progress (Cook, 1980: 223-224). 20 Active criminals accumulate personal experience during the course of their criminal careers; this experience surely has a powerful effect on perceptions of criminal justice system effectiveness among the group that is of greatest importance in the crime picture (Cook, 1980: 224). 21 Potential criminals make judgments on the basis of direct observation of the extent of criminal activity in the area: if “everyone” is doing it, it must pay (Cook, 1980: 226). 22 Rumors concerning police and judicial activities circulate and at times have considerable potency (Cook, 1980: 226).
23 from newspapers and television networks can be used to indirectly measure prospective murderers’ perceptions of risk of execution. The Effects on Homicides of Factors Other Than the Death Penalty States with and without capital punishment are not equivalent in respect to the factors that may influence homicide rates (Gibbs, 1975). So, estimate of the deterrent effect of the death penalty can be contaminated by estimates of other factors on homicides. Homicides may be affected by other possible social, economic, political, or criminal justice factors, as well as the use of the death penalty. Hence, other factors that could conceivably influence homicides jointly with capital punishment should be addressed. Other Criminal Justice Factors Prospective criminals’ perceptions of the effectiveness of the criminal justice system may be significantly influenced by knowledge that they develop through their own experiences with criminal justice activities (Cook, 1980). Thus, each arrest, court appearance, and sentence may send a deterrent message to the relatively few potential offenders who experience or know about them. Some studies have found that more police presence or activity increases the probabilities of detection and apprehension, and therefore reduce crime levels (Mocan and Gittings, 2003; Nagin, 2013). Adding more police officers could improve arrest rates and therefore lower crime. Since the probability of arrest for murder may be correlated with the use of capital punishment, one needs to distinguish the deterrent effect of police presence and activity from the deterrent effect of executions (NAS, 2012). The deterrent effect of executions may also be confused with the incapacitative effect of imprisonment (Nagin, 2013; NAS, 2012; Klein, Lawrence R., Brian E. Forst, and Victor Filitov, 1978). Imprisonment may reduce crime by physically incapacitating active offenders in jail and prison and denying the offenders the ability to commit crimes, including homicides. States that incarcerate more criminals should experience greater incapacitative effects. If states with larger prison populations have a higher number of executions, the size of the prison population must be controlled in order to isolate the deterrent effect of capital punishment. Non-Criminal Justice Factors It is widely acknowledged that many extralegal conditions, as well as the deterrent properties of legal punishment, can affect crime rates (Gibbs, 1975; Zimring and Hawkins,
24 1973). There are times and places where there are more people who are vulnerable to being murdered. For example, prospective serial killers tend to target vulnerable victims in deserted public places where are parking lots, dark city streets, university campuses, school playgrounds, rural roads, and so forth (Norris, 1988). Greater time spent being alone in the public places may increase vulnerability of an individual to murder. However, the present study in fact does not take a supply of vulnerable victims into account because it does not vary to any significant degree from one day to the next and because there is not any measurement at all for it.
25 CHAPTER 3
LITERATURE REVIEW
The National Academy of Science concludes that the existing literature does not tell us much of anything about whether there is the deterrent effect of the death penalty on homicides (Nagin and Pepper, 2012). One main reason of the conclusion lies in the failure to control for noncapital punishment variable such as prison sentence length. The same states that have more executions also have longer prison sentences, and it might be these longer sentences that actually affect homicide rates, rather than executions. Another reason is that existing research fails to directly measure perceptions of execution risk. This chapter presents a comprehensive and critical review of the existing empirical literature, published in economics, sociology, and criminology journals, that specifically examines the deterrent effect of the death penalty on murder rates in the United States. In order to provide background and rationale for the methodologies that will be used to conduct this research, this literature review identifies the significant methodological flaws of previous studies. This chapter consists of a summary of previous studies’ results, followed by sections addressing six specific topics: independent variable of primary interest, dependent variables, other explanatory variables, units of analysis, research design, and data sources. Summary of Findings from Previous Studies The deterrent effect of the death penalty on homicide rates has been the subject of long- standing academic debate since the mid-1910s. Until economist Isaac Ehrlich published his groundbreaking research in 1975, most of the early death penalty studies (1919-1974) had provided no empirical support for the argument that the death penalty has a general deterrent effect on murder rates. Some studies reported a statistically insignificant negative association between murder and use of the death penalty (Bye, 1919; Sellin, 1967a, 1967b; Reckless, 1969; Vold, 1932, 1952), whereas other studies reported a positive association, suggesting a brutalization effect rather than a deterrent effect (Bailey 1974, 1975; Dann, 1935; Graves, 1956; Savitz, 1959). Given that the findings were generally inconsistent with the deterrence hypothesis, it is not surprising that most researchers concluded that the deterrent effect of the death penalty
26 does not in fact exist. However, this conclusion should be interpreted with caution because the results from these early studies were derived from very simple comparative analyses. For instance, one early death penalty study compared homicide rates in neighboring states that had many similarities but differing legal stances on the death penalty (Sellin, 1959). To analyze homicide rates from 1920 to 1955 among neighboring states, two death penalty states (such as Indiana and Ohio) were compared to one life imprisonment state (such as Michigan). Other studies compared homicide rates in states that retained the death penalty and states that had abolished the death penalty (Sellin, 1967a, 1967b; Bailey 1974, 1975). Another common approach was to compare homicide rates in the same jurisdiction before and after an execution was carried out or a highly publicized death sentence was imposed (Dann, 1935; Graves, 1956; Savitz, 1959). Studying five highly publicized executions occurring in Philadelphia, Dann (1935) compared the number of homicides occurring during the 60 days before the execution to the number of homicides occurring during the 60 days afterwards. Savitz (1959), on the other hand, compared the number of homicides occurring eight weeks before and eight weeks after four highly publicized death sentences imposed in Philadelphia. In addition, Graves (1956) used homicide rates between 1946 and 1954 for the three largest counties in California to compare the daily homicide counts during two time periods: 74 weeks during which executions occurred, and 116 control weeks when no executions occurred. From a statistical standpoint, matching culturally similar states or contiguous time periods in a city or state can only be a partially effective way to hold social and economic variables constant (Passell, 1975). However, many of these early death penalty studies were quite inadequately designed (Ehrlich, 1975; Grogger, 1990). Only limited efforts were made to control for a set of demographic, cultural, and socioeconomic variables that could affect homicide rates, independent of the death penalty (Sellin 1959). This unsophisticated statistical methodology failed to distinguish the effect of capital punishment on homicide from the effects of other variables. Further, most researchers did not distinguish actual use of capital punishment from the mere presence of a death penalty statute (Sellin, 1967; Bailey, 1974, 1975). Also, the sample sizes of these studies were all too small to produce stable results (Passell, 1975). Finally, early studies failed to take account of the possibility that higher homicide rates might cause states to pass or retain the death penalty, or to execute more murderers (Ehrlich, 1975). This positive effect could obscure any negative effect of the death penalty on homicide rates.
27 A major breakthrough in the study of the death penalty occurred in 1975 when Isaac Ehrlich used multiple regression analysis to overcome some of the methodological weaknesses inherent in the earlier comparative studies. Ehrlich’s (1975) approach employed execution risk (i.e., the conditional probability of execution given conviction) as the main independent variable of interest to measure the extent to which executions were carried out in a given state. Moreover, Ehrlich controlled for additional explanatory variables that night affect homicide rates, such as deterrence variables (e.g., the probability of apprehension and the conditional probability of conviction) and demographic and socioeconomic variables (e.g., estimated per capita income, the proportion of the population in the age group 14 to 24, the unemployment rate, and the labor force participation rate). Ehrlich used annual time-series data for the United States in 1933-1969 (N=36). Ehrlich also used two-stage least-squares methods to model the possible two-way relationship between execution risk and homicide rates found that “an additional execution per year for the period of 1933-69 resulted, on average, in 7 or 8 fewer murders” (p. 414) and concluded that execution exerts a deterrent effect on some prospective offenders who contemplate homicide. This result was replicated in Ehrlich’s alternative methodological approach, which used cross-sectional data from 1940 and 1950 and included a larger number of observations (N=45 in 1940 and N=46 in 1950) than his 1975 research (N=36). This study (Ehrlich, 1977) controlled for some possible confounding variables, such as other violent crimes and the severity of prison sentences. Ehrlich’s second study confirmed his original (1975) conclusion that execution risk deters homicide. Moreover, Ehrlich’s 1975 time-series finding was also replicated by some other researchers who tested his econometric model using foreign data or slightly different time periods and model specifications applied to the U.S. data (e.g., Cloninger, 1977; Layson, 1983, 1985, 1986; Wolpin, 1978; Yunker, 1976). For example, two studies used time-series data collected in Canada, England, and Wales because information about the length of prison sentence was available in these data; such information was not available in the U.S. data (Layson, 1983; Wolpin, 1978). Two other studies used U.S. vital statistics homicide data because they provided a more accurate and appropriate measure of homicides than the Federal Bureau of Investigation’s (FBI’s) Uniform Crime Report (UCR) data used in Ehrlich’s research (Bowers and Pierce, 1980; Layson, 1985). Also, in a study using the 1933-1971 national time-series data to examine the relationship between U.S. homicide rates as the dependent variable and
28 unemployment rates and executions rates as the only independent variables, Yunker (1976) found a deterrent effect much stronger than Ehrlich’s. Although recognized and cited frequently for a time, Ehrlich’s original work and a few colleagues’ similar studies fell out of favor when advanced statistical methodologies and panel data become available for use. A large number of replication studies challenged Ehrlich’s results on methodological grounds, such as his choice of time periods for analysis, his use of the FBI’s UCR data, and his uncritical use of regression methods (Bowers and Pierce, 1975; Hoenack and Weiler, 1980; Passell, 1975; Kleck, 1979; Passell and Taylor, 1977). For example, some researchers excluded the post-1962 (1962-1969) sample periods from Ehrlich’s original work because there was virtually no variation in execution risk during this period (Avio, 1979; Bechdolt, 1977; Bowers and Pierce, 1975; Klein, Forst, and Filatov, 1978; Passell and Taylor, 1977; Wolpin, 1978). These researchers overwhelmingly failed to find evidence of a deterrent effect of executions on homicide and concluded that Ehrlich’s 1975 finding had been significantly influenced by the excluded sample period. Other researchers found that Ehrlich’s results changed when analysts controlled for additional independent variables that were omitted from his original model. For example, mandatory death sentences and length of sentence (Avio, 1979, 1988; McKee and Sesnowitz, 1977), propensity to commit crime (Klein, Forst, and Filatov, 1978; McKee and Sesnowitz, 1977), and gun ownership (Kleck, 1979) were found to have effects on homicide, and controlling these variables caused the deterrent effect of executions on homicide to vanish. Cameron (1994) reviewed a number of death penalty studies published after Ehrlich reported his widely cited but controversial findings in 1975 and 1977. Ehrlich’s work and studies that tried to replicate it were criticized for methodological limitations, such as omitted relevant variables, inclusion of irrelevant variables, measurement error, insufficient temporal variation in the sample, and inappropriate sample periods. Interestingly, Cameron noted that Ehrlich had ignored the possibility that executions may have a brutalization effect on murderers, because economists believed that the evidence in support of the brutalization effect was the result of model misspecification. Cameron cited two empirical findings in support of the brutalization effect to lend credence to his argument (Bowers, Pierce, and McDevitt, 1984; Phillips, 1980). He also argued that time-series design is better than cross-sectional design because executions may
29 show only a short-run deterrent effect. He noted that neither pooled cross-section/time-series data nor panel data had been used (Cameron, 1994). In addition, a few death penalty researchers have examined the impact on homicide of the reintroduction of executions in a few states after the moratorium period (Cochran and Chamlin, 2000; Cochran, Chamlin, & Seth, 1994; McFarland, 1983; Thompson, 1997, 1999). It should be noted that these executions’ impact might have been artificially high because executions at this time naturally attracted extensive media attention. However, depending on the subtypes of homicide, the studies reported either mixed findings (Cochran and Chamlin, 2000; Land, Teske, and Zheng, 2012; McFarland, 1983; Thompson, 1999) or brutalization findings (Cochran, Chamlin, & Seth, 1994; Thompson, 1997). Several studies have examined the relationship between the amount of publicity given to executions and the homicide rate by analyzing television coverage of executions, newspaper coverage, or both. These studies have produced mixed findings. Although some studies have found that publicity has a statistically significant deterrent effect (Phillips, 1980; Phillips and Hensley, 1984; Stack, 1990, 1995, 1998), other studies have found either no deterrent effect or a brutalization effect (Bailey, 1990, 1998; Bailey and Peterson, 1989; Bullock, 1991; Hjalmarsson, 2009; King, 1978; Peterson and Bailey, 1991; Stolzenberg and D’Alessio, 2004). Recently, economists and law professors have tested for death penalty effects using panel data (Albert, 1999; Cloninger, 1992; Dezhbakhsh and Shepherd, 2006; Dezhbakhsh, Rubin, and Shustorovich, 2003; Ehrlich and Liu, 1999; Ekelund, Jackson, Ressler, and Tollison, 2006; Fagan, Zimring, and Geller, 2006; Katz, Levitt, and Shustorovich, 2003; Lester, 1979; Liu, 2004; Mocan and Gittings, 2003; Peterson and Bailey, 1988; Shepherd, 2004, 200; Zimmerman, 2004, 2006). With different temporal and geographic units of analysis, sets of control variables, and sample periods, some panel studies obtained results indicating deterrent effects (Cloninger, 1992; Dezhbakhsh and Shepherd, 2006; Dezhbakhsh, Rubin, and Shustorovich, 2003; Ehrlich and Liu, 1999; Lester, 1979; Liu, 2004; Mocan and Gittings, 2003; Shepherd, 2004; Zimmerman, 2004). In their reanalysis of recent panel studies (e.g., Dezhbakhsh and Shepherd, 2006; Katz, Levitt, and Shustorovich, 2003; Mocan and Gittings, 2003), Donohue and Wolfers (2005) repeatedly refuted findings in support of the deterrent effect of executions. Nevertheless, Donohue and Wolfers acknowledged that executions may have an effect on homicide, although they were uncertain about whether it is a deterrent effect or a brutalization effect. They pointed
30 out that this uncertainty arises because the effect of executions on homicide rates is too small to be detected with data on years or other long periods of the sort that have been used so far in published studies. This implies that future research should rely on the smallest possible temporal data to determine whether a deterrent effect exists and to examine how it varies in different situations. Yang and Lester’s 2008 comprehensive meta-analysis leads to a more systematic conclusion than Cameron’s (1994) and Donohue and Wolfers’ (2005) reviews of the empirical research on the deterrent effect of capital punishment on homicide. Yang and Lester used meta- analysis to summarize the results of 104 studies published in peer-reviewed journals. They investigated effects within five types of designs (cross-sectional, time-series, panel, single execution, and publicized execution studies) and found that three mean effect sizes were statistically significant. The significant mean effect sizes were -0.115 for all combined studies, - 0.155 for time-series studies, and -0.133 for panel studies, while the mean effect sizes were not significant for the other two designs. Thus, these findings show that the evidence in support of the deterrent effect of executions on homicide is strongest in the time-series and panel studies. This pattern of evidence is consistent with Bowers and Cole’s (1975) review of Sellin’s and Ehrlich’s studies: although previous studies examined the causal relationship between capital punishment and murder rates, different statistical methods led to different conclusions. The Dependent Variable This section reviews a variety of measures of the dependent variable that have been used in previous studies: (1) general (total) homicide rate (the number of murders and non-negligent manslaughters per 100,000 population), (2) felony murder rate, (3) disaggregated subtypes forms of homicide rates, and (4) a more age-specific general murder rates (the number of murders and non-negligent manslaughters per 100,000 population 16 years and older). Most previous studies have exclusively used general (total) homicide rate as the dependent variable (Albert, 1999; Avio, 1979, 1988; Bailey, 1975, 1976, 1977, 1979a, 1979b, 1979c, 1980, 1984, 1990; Bailey and Peterson, 1989; Black and Orsagh, 1978; Bowers and Pierce, 1975). It has long been acknowledged both theoretically and practically that the appropriate measure of the dependent variable may affect any homicides, not just capital homicides legally defined as punishable by death. In compliance with Van den Haag’s (1969) definition of deterrence as a “preconscious, general response to a severe but not necessarily
31 specifically and explicitly apprehended or calculated threat” (p. 146), some scholars have placed considerable weight on the assumption that deterrence does not necessarily require any conscious, rational consideration of possible punishments by prospective offenders (Kleck, 1979; Kovandzic, Vieraitis, and Boots, 2009; Stolzenberg and D’Alessio, 2004). If prospective killers do not consciously distinguish capital murders from other homicides, this provides a theoretical rationale for combining capital and noncapital homicides under one homicide category to estimate the deterrent effect of capital punishment. Furthermore, it seems reasonable to model the link in prospective offenders’ minds between the ultimate legal sanction for capital murder and the homicidal act rather than between the ultimate legal sanction and any particular arbitrary legal subtype of homicide (Kleck, 1979; Stolzenberg and D’Alessio, 2004). Some scholars have also argued that the effect of formal legal punishment may be so subtle that other possible general preventive effects could not be explicitly separated from a deterrent effect (Andenaes, 1952, 1966, 1974; Durkheim, 1933; Gibbs, 1975, 1978; Hart, 1961, 1968; Hawkins, 1971; Zimring and Hawkins, 1973), and that all legal subtypes of homicides should therefore be grouped together into a single measure of the dependent variable. For example, it is possible that, in addition to serving as a deterrent, capital punishment might serve the educative, moralizing, and normative validation purposes that promote respect for human life and dignity, leading to a decrease in the homicides rate. With this premise in mind, Peterson and Bailey (1988) argued that the appropriate measure of the dependent variable should not be limited only to homicides likely to be deterred by capital punishment. Likewise, Stack (1998) insisted that the dependent variable should include all types of homicide, because the “death-dip” phenomenon (a decline in homicide after an execution) might be due to the normative validation effect, independent of a fear of capital punishment. For practical reasons, the general (total) homicide rate has been employed as the best proxy for the dependent variable because many death penalty studies have relied heavily on the FBI’s UCR statistics or mortality statistics from the U.S. Department of Health and Human Services (Peterson and Bailey, 1991). The most apparent limitation of the UCR is that murders, manslaughter, and negligent homicides are grouped into a single homicide category, making it impossible to separate homicides that are punishable by death from other homicides. As Dezhbakhsh, Rubin, and Shepherd (2003) pointed out, any attempts to single out death-eligible homicides may require a close examination of each reported homicide to produce a balanced,
32 unbiased judgment as to whether that case can be labelled a capital or non-capital homicides. Such extensive data scrutiny is vulnerable to measurement errors and biased subjective judgment. Moreover, some researchers have argued that homicides are in a generally constant ratio to total homicides so that the deterrent effect of the death penalty on homicide will not be obscured by the insensitivity of general homicide rates (Bailey, 1974; Ehrlich, 1975; Peterson and Bailey, 1988; Stolzenberg and D’Alessio, 2004). For the purposes of estimating the deterrent effect of capital punishment, the general homicide rate is a valid and reliable measure of capital homicide, even though research in this area may be hampered by the UCR’s reporting and recording procedures. In contrast, some social scientists have argued that the appropriate dependent variable in a study of the deterrent effect of capital punishment should be restricted to first degree homicides or capital homicides, which could be punishable by death. For example, because a core assumption of classical deterrence theory is that deterrence requires a conscious and rational calculation of expected risks and benefits, Glaser (1977) argued that homicides that can be classified as non-capital cases should be excluded. Likewise, Fagan, Zimring, and Geller (2006) argued that many of the previous studies are flawed because the measure of the dependent variables includes both capital-eligible and non-capital-eligible homicides. According to the statutory definition of capital-eligible homicides, not all capital-eligible cases will actually be tried as such. In other words, the use of inclusive measures in the previous studies does not accurately reflect the fact that only a small proportion of all murders, capital-eligible or death- eligible, is actually punishable by death (Hjalmarsson, 2009). In addition, some researchers have maintained that prior studies’ null findings for the deterrent effect of capital punishment on homicide rates may be attributed to the simple aggregation of homicide offenses in the UCR system (Bailey, 1983; Cochran, Chamlin, and Seth, 1994; Peterson and Bailey, 1991). For this reason, very few studies have used capital (death-eligible) homicide rates as the dependent variable (Bailey, 1974; Dann 1935; Fagan, Zimring, and Geller, 2006; Hjalmarsson, 2009; Peterson and Bailey, 1991; Savitz, 1958; Shepherd, 2004; Sorensen, Wrinkle, Brewer, and Marquart, 1999). A few studies have employed a wide variety of legal subtypes of homicide, in order to further measure two possible contradictory effects of capital punishment (Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; Land, Teske, and Zheng, 2012; Thomson, 1997, 1999).
33 The basic premise behind these studies is the assumption that capital punishment may generate both deterrent and a brutalization effects at the same time. For example, the felony murders of nonstrangers, which typically involve some planning, may significantly decrease after an execution, whereas the argument-based murders of strangers, which are typically more spontaneous, may significantly increase during the same time period. The methods used in these studies disaggregate homicides into narrow data subtypes and explain differences in homicide rates or counts by focusing on situational characteristics unique to the homicide subtypes involved. The availability of detailed homicide data sets allows researchers to study the different effects of capital punishment on narrow categories of homicide. Prior studies using UCR data have ignored the possibility that the measure of the dependent variable tends to be confounded by excessive heterogeneity in the official homicide category (Bailey, 1983; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; Peterson and Bailey, 1991). However, this problem has been partially overcome by the FBI’s development of incident-based Supplementary Homicide Report (SHR) data, which enables researchers to disaggregate homicides by situational factors into narrow subcategories of homicides. However, the process of disaggregating homicides can lead to reduced data quality, inaccurate and incomplete category coding, and unstable statistical results (Marvell and Moody, 1999). Finally, a very few studies have analyzed the various subtypes of homicides by the victims’ demographic characteristics. For example, Grogger (1990) investigated homicide rates not only in the total population but also in demographic subpopulations, including whites, nonwhites, white males, and nonwhite males. Measures of the Prevalence or Risk of Capital Punishment This section summarizes a wide variety of the measures of the primary independent variable of interest that have been used in the previous studies: (1) probability of execution, (2) presence of the death penalty statute, (3) frequency of execution, (4) count of executions, (5) the occurrence of a single execution event, and (6) the occurrence of publicized executions. Many studies, mainly performed by economists and using monthly or annual data, have employed a variety of measures of the probability that an offender would be executed (Kleck, 1979; Kovandzic, Vieraitis, and Boots, 2009; Layson, 1983, 1985; Liu, 2004; McAleer and Veall, 1989; Merriman, 1988; Mocan and Gittings, 2003; Passell, 1975; Passell and Taylor,
34 1977; Shepherd, 2004, 2005; Veall, 1992; Wolpin, 1978; Yunker, 2001; Zimmerman, 2004, 2006). These studies have followed Ehrlich-style measures of execution risk. Ehrlich (1975) employed three different measures of the conditional probability of execution to reflect the execution risk: (1) the ratio of the number of executions in the current year t to the number of convictions for murder and non-negligent manslaughter in the same time period, (2) the ratio of the number of executions in the next year t+1 to the number of convictions at the current year t, and (3) the ratio of the number of executions at the current year t to the number of convictions in the previous year in the previous year t-1. Some researchers used a slightly different kind of denominator in their measures of execution risk that reflect average elapsed time between sentencing and execution. For example, taking into account that the average length of time the between conviction and execution during the middle decades of the 20th century was approximately one year, many early studies measured the probability of execution as the number of executions at year t divided by the number of convictions for murder and non-negligent manslaughter in the previous year t-1 (Kleck, 1979; Kovandzic, Vieraitis, and Boots, 2009). In recent years, the average length of time between death sentence and execution has risen to approximately six years, so some recent panel studies have used a longer mean lag time between death sentence and execution (Dezhbakhsh, Rubin, and Shepherd, 2003; Kovandzic, Vieraitis, and Boots, 2009; Mocan and Gittings, 2003; Shepherd, 2005; Zimmerman, 2004). Accordingly, these studies measured the probability of execution as the number of executions at year t divided by the estimated number of persons convicted of murder or non-negligent manslaughter at year t-6. This conditional probability of execution seems to assume that potential murderers will estimate the likelihood of being executed based on the execution of inmates at the current year t who had been sentenced six years earlier (Kovandzic, Vieraitis, and Boots, 2009). Earlier points in a time series must be dropped when using these lagged execution variables, which reduces sample size. Therefore, some researchers also use an un-lagged probability of execution to prevent data loss (Shepherd, 2004; Zimmerman, 2004). There are still other variations in measures of the probability of execution. Some scholars (Mocan and Gittings, 2003; Shepherd, 2004) have measured the subjective probability of execution as the number of executions per death row inmate by using the number of persons convicted of murder and non-negligent manslaughters rather than the number of convictions in
35 the denominator (Mocan and Gittings, 2003; Shepherd, 2004). For example, Mocan and Gittings (2003) measured the subjective probability of execution as the number of executions per number of death row inmates. Following Mocan and Gittings (2003), Shepherd (2004) employed the probability of execution, defined as a 12-month moving average of the number of executions divided by a 12-month moving average of the number of people on death row. The time between death row sentencing and execution reflects 12 months. Shepherd (2004, p. 297) argued that prospective murderers are likely to estimate their probabilities of being executed based on a “cheaper informational proxy,” such as the rate at which convicted murders are sentenced to death row and executed over the past few months. Measures of Execution Risk Shepherd (2005) included the length of time after executions were carried out when constructing a comprehensive set of measures of the subjective probability of execution. She measured forward-looking and backward-looking expectations by using the number of executions at year t divided by the number of death sentences in year t-6 and the number of executions at year t+6 divided by the number of death sentences in year t. In the same study, Shepherd used a six-year moving average with the sum of executions during the six-year period (t+2, t+1, t, t-1, t-2, and t-3) divided by sum of death sentences during the preceding six-year period (t-4, t-5, t-6, t-7, t-8, and t-9). Alternatively, some researchers have pointed out that Ehrlich’s subjective probability of execution and its variants were too complex to precisely reflect the way in which potential murderers perceive the threat of capital punishment (Black and Orsagh, 1978; Boyes and McPheters, 1977). Because prospective murderers anticipate only one of two consequences of their criminal involvement, involving either a prison sentence or the death penalty, the subjective probability of execution needs to be much simpler than the Ehrlich-style subjective probability of execution (Black and Orsagh, 1978; Boyes and McPheters, 1977). Accordingly, several studies have measured the subjective probability of execution as the number of executions divided by the number of reported murders or non-negligent manslaughters in the same year (Albert, 1999; Black and Orsagh, 1978; Boyes and McPheters, 1977). Because the frequency or number of executions is generally considered to be a more theoretically appropriate measure of execution risk than the conditional probabilities of execution, the most widely used measure of the main independent variable has been the
36 frequency of executions (Bailey, 1983, 1984, 1990, 1998; Bailey and Peterson, 1989; Bechdolt, 1977; Bowers and Pierce, 1980; Decker and Kohfeld, 1987, 1988, 1990; Dezhbakhsh and Shepherd, 2006; Ekelund, Jackson, Ressler, and Tollison, 2006; Fagan, Zimring, and Geller, 2006; Fox, 1977; Kleck, 1979; Kovandzic, Vieraitis, and Boots, 2009; Layson, 1985; Marvell and Moody, 1999; Peterson and Bailey, 1988. 1991; Sesnowitz and McKee, 1977; Shepherd, 2004; Sorensen, Wrinkle, Brewer, and Marquart, 1999; Stolzenberg and D’Alessio, 2004). Instead of the unwarranted assumption associated with the conditional probability of execution risk – that people’s perceptions of the threat of capital punishment derive from a conscious, rational calculation of the exact number of murders relative to the actual number of executions – the frequency of execution is based on the assumption that prospective offenders would have very limited knowledge about the actual number of homicides in their neighborhoods and the actual severity of punishments (Kleck, Sever, Li, and Gertz, 2005; Stolzenberg and D’Alessio, 2004). It is reasonable to assume that prospective offenders’ quality of information is poor, because they form their own probabilities of arrest, conviction, and execution mainly based on information obtained through their friends, relatives, and acquaintances (Shepherd, 2004). Drawing on the given assumption, it is reasonable to believe that capital punishment would deter murder simply by reminding prospective offenders of the state’s willingness to use capital punishment (Kleck, 1979, p. 896). As Kovandzic, Vieraitis, and Boots (2009) argued, increases in the number of executions may cause an increase in potential murderers’ perception of execution risk. Thus, the frequency of executions may indicate not only the actual number of inmates who are executed by a given state, but also the total number of times that potential murderers update their perception of execution risk, leading them to conclude that the perceived risk of execution would be greater when executions are most frequent. However, based on their finding that the effect of additional executions depends on the population size and is not systematically significant, Donohue and Wolfers (2005) argued that the frequency of execution does not reflect real execution risk. Nonetheless, some scholars have still argued that the frequency of executions is a reasonably solid indicator of execution risk (Dezhbakhsh and Shepherd, 2006; Kovandzic, Vieraitis, and Boots, 2009). Capital punishment studies have generally indicated the mere presence of the death penalty statute in a state by entering a binary dummy variable that takes the value of 1 when the state retained the death penalty law and 0 otherwise (Albert, 1999; Bailey, 1973, 1975, 1976,
37 1983, 1984; Bailey and Peterson, 1989; Chressanthis, 1989; Dezhbakhsh, Rubin, and Shepherd, 2003; Dezhbakhsh and Shepherd, 2006; Ehrlich, 1977; Ehrlich and Liu, 1999; Ekelund, Jackson, Ressler, and Tollison, 2006; Fagan, Zimring, and Geller, 2006; McAleer and Veall, 1989; Mocan and Gittings, 2003; Passell, 1975; Peterson and Bailey, 1988, 1991; Phillips and Hensley, 1984; Stack, 1995; Veall, 1992; Zimmerman, 2006). To date, the mere existence of the death penalty statute is still in use for a variety of reasons. The dummy variable approach assumes that the deterrent effect of the mere presence of the death penalty statute is not systematically stronger when actual probabilities of execution are high, instead assuming that the existence of the death penalty law has a direct impact on the homicide rate, independent of the probability of execution (Kovandzic, Vieraitis, and Boots, 2009). In contrast, Zimmerman (2004) argued that the deterrent effect of capital punishment occurs only when executions are actually carried out. Therefore, studies that intend to measure the pure deterrent effect of capital punishment on homicides should incorporate the existence of the death penalty law into the regression model. The existence of the death penalty law often has been used in both cross-sectional and panel studies, but it has not been used as much in time-series studies. For example, time-series studies have often failed to differentiate between retentionist and abolitionist states because they analyzed data on the entire United States. Thus, previous time-series studies that measured actual probabilities of execution effectively assumed that all U.S. states are retentionist. This is misleading, because the actual probabilities of execution are zero in abolitionist states. Temporal Unit of Analysis Most previous death penalty studies have employed annual or monthly homicide data, very few researchers have used execution counts for short periods of time to overcome the problems associated with highly aggregated data (Graves, 1967; Grogger, 1990; Hjalmarsson, 2009; Savitz, 1958). As Phillips and Hensley (1984) suggested, the failure to find consistent deterrent effects in previous studies might be caused by the analysis of highly aggregated data. In other words, the deterrent effect of the death penalty exists over a relatively short period of time. Phillips and Hensley (1984) thus proposed a return to the earlier tradition of analyzing daily data to detect short-term decreases in homicides following the occurrence of highly publicized death sentences and executions.
38 News Media Publicity on Executions A few studies have examined the deterrent effect of a first post-Moratorium execution event on homicide rates (Bailey, 1998; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; Lester, 1979; McFarland, 1983; Thomson, 1997, 1999). It is assumed that the first post-Moratorium death sentence and execution in each state might have had a particularly strong deterrent effect among prospective murderers because the number of broadcasts or published reports about these sentences and executions was significantly higher than for subsequent death sentences and executions. Although some executions are newsworthy, many executions receive little media coverage, as demonstrated by Jocoby, Bronson, Wilczak, Mack, Suter, Xu, and Rosenmerkel (2008). Their study found that the first post-Moratorium execution in a state received greater-than-average press attention due to the historical nature of the event. Therefore, it would be reasonable to assume that first post-Moratorium execution events used in these studies might receive much more extensive print and electronic media coverage than any subsequent execution event. However, one cannot necessarily generalize the findings of these studies to other places and times, because the studies were restricted to one geographic area and one time period. For capital punishment to have its deterrent effect, the threat of punishment should be communicated to the target population who contemplates murder. Prospective murderers base their estimates of execution risk more on information gathered from the mass media (newspapers, magazines, radio, and television) than on statistical facts regarding homicides and executions in any given state (Yunker, 2001). The deterrent effect of capital punishment may depend on the amount of publicity given to an execution, so more publicity means greater deterrent effect (Phillips, 1980). Nevertheless, most previous studies have ignored the effect of execution publicity on homicides (Stack, 1995). To overcome this shortcoming, some researchers have employed publicized executions as the main independent variable of interest, based at both the national level (Bailey, 1990; Bailey and Peterson, 1989; Peterson and Bailey, 1991; Phillips, 1980; Phillips and Hensley, 1984; Stack, 1987, 1995) and the local level (Bailey, 1998; Dann, 1935; Hjalmarsson, 2009; King, 1978; Savitz, 1958; Stack, 1990, 1998; Stolzenberg and D’Alessio, 2004). Depending on the availability of data sources, some studies have examined the relationship between the amount of newspaper coverage devoted to executions and the homicide
39 rate (Bailey, 1998; Bailey and Peterson, 1989; Dann, 1935; Hjalmarsson, 2009; King, 1978; Phillips, 1980; Phillips and Hensley, 1984; Savitz, 1958; Stack, 1987, 1990, 1998; Stolzenberg and D’Alessio, 2004). Others have examined the relationship between the amount of national network television exposure given to executions and the homicide rate (Bailey, 1990; Peterson and Bailey, 1991; Stack, 1995). Recently, one study examined the effects of newspaper and television news coverage of executions by using three metropolitan city newspapers in Texas and one local television network in Dallas (Hjalmarsson, 2009). Control Variables This section summarizes a wide variety of control variables used in previous studies, including (1) deterrence, (2) economic, (3) social and demographic, (4) temporal, and (5) other violent and property crimes. Because so many variables that correlate with execution also correlate with homicide rates, it is important both to incorporate a wide variety of explanatory control variables into a mathematical equation and to employ sophisticated statistical methods if one hopes to isolate the effect of executions on homicide rates (Fagan, Zimring, and Geller, 2005). As Ehrlich’s 1975 research and its follow-up studies have failed to include a complete set of relevant control variables (Baldus and Cole, 1975; Cameron, 1994; Forst, 1976; Kleck, 1979; Klein, Forst, and Filatov, 1978; Peterson and Bailey, 1988), it is possible that important variables have been excluded or that irrelevant variables have been included (Baldus and Cole, 1975; Cochran and Chamlin, 2000; Peterson and Bailey, 1988) Deterrence Variables Certainty of apprehension, conviction, and imprisonment for homicide may have a significant negative effect on homicide. Further, the degree to which a jurisdiction imposes noncapital punishment is likely to be positively correlated with its use of capital punishment. Given this, many previous studies have attempted to disentangle the deterrence effect of execution on homicide from the independent effects of potential confounding deterrent variables. To this end, some previous studies have employed an extensive variety of measures of deterrence variables other than the death penalty, including arrest, conviction, and imprisonment risks. Following Ehrlich’s subjective probability of execution given conviction for homicide, many economic studies necessarily employed arrest and conviction rates for murder and non- negligent homicide (Avio, 1979, 1988; Boyes and McPheters, 1977; Cover and Thistle, 1988; Dezhbakhsh, Rubin, and Shepherd, 2003; Ehrlich, 1975; Ehrlich and Liu, 1999; Hoenack and
40 Weiler, 1980; Layson, 1983, 1985; Liu, 2004; McAleer and Veall, 1989; Merriman, 1988; Mocan and Gittings, 2003; Passell, 1975; Passell and Taylor, 1977; Shepherd, 2004, 2005; Veall, 1992; Zimmerman, 2004). Although these studies employed measures of the conditional probability of execution that were different from Ehrlich’s measure, they also controlled for arrest and conviction rates. When data sources have been unavailable, some researchers have used proxies for the arrest and conviction rates, as these proxy variables may affect the arrest and conviction rates. Like the death penalty, imprisonment can have a significant deterrent effect on homicides (Kleck, 1979; Marvell and Moody, 1999). Unlike the deterrent effect of the death penalty, the incapacitative effect of imprisonment on homicide operates simply because imprisonment prevents prisoners from committing homicides. As Kleck (1979) pointed out, inmates whose life histories include frequent violent behavior in the past are more likely to commit interpersonal acts of violence in the future. Therefore, homicide offenders could be characterized as a person who could have been served a prison term for any of the previous felony convictions before committing homicide after released. For this reason, some studies have controlled for the incapacitative effect of imprisonment on homicide rates. For example, some studies have controlled for the imprisonment rate for murder (Bailey, 1983; Black and Orsagh, 1978; Boyes and McPheters, 1977; Fagan, Zimring, and Geller, 2005 [felony crime rates]; Passell, 1975; Sorensen, Wrinkle, Brewer, and Marquart, 1999), the number of persons in custody of state correctional authorities divided by adult population, multiplied by 1,000 (Katz, Levitt, and Shustorovich, 2003; Kleck, 1979; Marvell and Moody, 1999; Mocan and Gittings, 2003; Zimmerman, 2004), the number of persons in custody of state correctional authorities divided by total number of violent crimes (Katz, Levitt, and Shustorovich, 2003; Mocan and Gittings, 2003), the mean number of months served in state prison for homicide and nonnegligent manslaughter (Avio, 1979; Black and Orsagh, 1978; Ehrlich and Liu, 1999; Forst, 1976; Veall, 1992), and the mean or median number of months spent in prison by convicted murderers released in a given year (Leamer, 1983; Liu, 2004; Passell, 1975). In addition, some researchers have used prison death, defined as the number of prison deaths other than execution divided by number of adult state prisoners, multiplied by 1,000 as a proxy for harsh prison conditions (Katz, Levitt, and Shustorovich, 2003; Mocan and Gittings,
41 2003). These researchers maintained that knowledge of poor prison conditions among potential homicide offenders is likely to be accurate via personal direct experience or indirect information from their acquaintances, leading poor prison conditions to have a greater deterrent effect. Other researchers have used indirect measures of prison sentence lengths, including “Three Strikes” legislation, truth-in-sentencing legislation, and sentencing guidelines, because these policies generally result in longer prison stays (Shepherd, 2004). In some of these studies, a previously significant deterrent effect of the death penalty on homicide rates disappeared when any of the proxy variables for imprisonment was incorporated into the model (Avio, 1979, 1988; McKee and Sesnowitz, 1977). Economic Variables Research has demonstrated that homicides are correlated statistically and negatively with economic prosperity (Albert, 1999; Bechdolt, 1977; Boyes and McPheters, 1977; Dezhbakhsh, Rubin, and Shepherd, 2003; Kleck, 1979; Marvell and Moody, 1999; Mocan and Gittings, 2003; Shepherd, 2005). Increases in legitimate full-time, well-paid job opportunities and wages appear to influence a prospective offender’s decision to engage in deviant and criminal acts, which can lead to a decrease in the crime rate. Previous studies have employed many different types of economic variables, especially labor force participation, unemployment, and real per capita income. Death penalty studies explored the relationship between the percentage of the civilian population in the labor force and the homicide rate (Albert, 1999; Bowers and Pierce, 1975; Cover and Thistle, 1988; Decker and Kohfeld, 1987; Ehrlich, 1975; Ehrlich and Liu, 1999; Forst, 1976; Fox and Radelet, 1989; Layson, 1986, 1985; Leamer, 1983; Merriman, 1988; Passell and Taylor, 1977; and Veall, 1992). The relationship between unemployment rates and homicide rates has been addressed in studies conducted (Albert, 1998; Avio, 1988, 1979; Bailey, 1978, 1979, 1980, 1984, 1990, 1998; Bailey and Peterson, 1989; Bechdolt, Jr., 1977; Bowers and Pierce, 1975; Cover and Thistle, 1988; Decker and Kohfeld, 1988; Ehrlich, 1975; Dezhbakhsh and Shepherd, 2006; Ehrlich and Liu, 1999; Ekelund, Jr., Jackson, Ressler, and Tollison, 2006; Fox and Radelet, 1989; Layson, 1983, 1985; Leamer, 1983; Marvell and Moody, 1999; Merriman, 1988; Mocan and Gittings, 2003; Passell and Taylor, 1977; Peterson and Bailey, 1988, 1991; Sesnowitz and McKee, 1977; Shepherd, 2004; Sorensen, Wrinkle, Brewer, and Marquart, 1999; Veall, 1992; Wolpin, 1978; and Zimmerman, 2006, 2004). Researchers have investigated the relationship between per capita
42 personal income and homicide rates (Albert, 1998; Avio, 1988, 1979; Bechdolt, Jr., 1977; Bowers and Pierce, 1975; Chressanthis, 1989; Cover and Thistle, 1988; Dezhbakhsh and Shepherd, 2006; Dezhbakhsh, Rubin, and Shepherd, 2003; Ehrlich, 1975; Fox and Radelet, 1989; Katz, Levitt, and Shustorovich, 2003; Layson, 1985, 1986; Marvell and Moody, 1999; Mocan and Gittings, 2003; Passell and Taylor, 1977; Shepherd, 2004, 2005; and Zimmerman, 2006). Social and Demographic Variables To minimize inaccuracy in the estimations of the deterrent effect of the death penalty on homicides, many social scientists have employed social and demographic variables (Forst, 1976; Peterson and Bailey, 1988). For example, age, race, sex, education level, population density and size, and family stability (among other variables) have been studied to determine which factors influence both execution rates and homicide rates at the same time and thus tend to distort the estimated deterrent effect of executions on homicides. Although Ehrlich and his colleagues (including Layson) have argued that the increase in the number of homicides could be attributed to the abolition of the death penalty, some researchers have insisted that their findings in support of the deterrent effect have been attributable to the omission of important social and demographic variables from the homicide models (Klein, Forst, and Filatov, 1978; Kleck, 1979; Dezhbakhsh, Rubin, and Shepherd, 2003). For example, Kleck (1979) noted that increasing the availability of firearms could increase homicide and other violent crime rates, because use of guns in attacks increase the likelihood of death. Likewise, some researchers have employed National Rifle Association (NRA) membership rates as a proxy for the gun ownership rate (Dezhbakhsh, Rubin, and Shepherd, 2003; Shepherd, 2005). Temporal Variables Scholars have noted a number of temporal patterns of homicide and execution (Bailey, 1983; Bowers and Pierce, 1980; Hjalmarsson, 2009; Phillips and Hensley, 1984; Sorensen, Wrinkle, Brewer, and Marquart, 1999; Stack 1995, 1998). For example, homicide rates are generally higher during the summer months and in December, presumably because people are less subject the controlling effects of work or school during these months than in the remainder of the year. Moreover, homicides occur more frequently during weekends and on national holidays. In contrast, the most common day for executions is Wednesday, and they typically are not carried out on weekends (Grogger, 1990; Hjalmarsson, 2009).
43 Most longitudinal studies have controlled for an extensive set of temporal variables. For example, some studies using annual and monthly homicide data have included dummy variables for years and months as controls (Bailey, 1983, 1990, 1998; Bowers and Pierce, 1980; Peterson and Bailey, 1991; Sorensen, Wrinkle, Brewer, and Marquart, 1999; Stack, 1998). Other studies employing weekly and daily murder data have included dummy variables for days of the week and major public holidays, such as New Year’s Day, Memorial Day, Independence Day, Labor Day, Thanksgiving Day, and Christmas, as well as month and year dummies (Phillips and Hensley, 1984; Stack, 1995). However, a few economic studies employing daily homicide data have not taken into account the effect of public holidays on homicide (Grogger, 1990; Hjalmarsson, 2009). Given that a sudden or traumatic event or disaster can raise the number of murders, some studies have accounted for the impact of events such as the 1995 Oklahoma City bombing (Mocan and Gittings, 2003), the Second World War from 1942 to 1945 (Avio, 1979, 1988; Layson, 1983; Marvell and Moody, 1999; Wolpin, 1978), and the crack cocaine epidemic from 1985 to 1991 (Marvell and Moody, 1999). In addition, some researchers included time variables for other reasons. For example, Sorensen, Wrinkle, Brewer, and Marquart (1999) employed the 1997 dummy variable because Texas executed a record number of 37 capital murderers in 1997. Ehrlich (1975) included a linear time trend variable to reflect changes in homicide rates accompanied by the development of medical technology. Likewise, Layson (1983) used the time trend variable to work as a proxy for other omitted variables. Other Violent and Property Crimes Homicide is often a byproduct of other violent crimes (Dezhbakhsh, Rubin, and Shepherd, 2003; Ehrlich, 1975). A significant number of murders occur in conjunction with assault, battery, robbery, and other violent crimes. Accordingly, an increase in other violent crimes may lead to a greater number of homicides. Given this, some previous studies have included other violent crimes as explanatory control variables in their equations. For example, some studies have employed both aggravated assault and robbery rates (Dezhbakhsh, Rubin, and Shepherd, 2003; Zimmerman, 2004, 2006), whereas other studies have employed just robbery rates (Fagan, Zimring, and Geller, 2005; Kleck, 1979). In at least one study, the apparent deterrent effect of the death penalty disappeared when aggravated assaults and robbery variables were included (Klein, Forst, and Filatov, 1977).
44 Research Designs Overall, research on the death penalty’s deterrence effect has seen a definite trend away from simple correlational and cross-sectional research designs towards more sophisticated time- series and panel studies. For example, many recent researchers used panel design to offset the inherent methodological weaknesses of cross-sectional and time-series studies. Others have used natural experimental designs, because some of the first executions carried out in a given state after a moratorium has ended may show more of a deterrent effect. Therefore, this section provides a review of five major types of research designs that have been used extensively in previous studies: (1) matching (or comparative), (2) cross-sectional, (3) time-series, (4) natural experimental, and (5) panel or pooled time-series cross-sectional designs. The comparative advantages and disadvantages of each design type will be explored and discussed. Matching design has been employed to identify a cluster of neighboring states sharing as many similarities as possible, except for the legal statute of capital punishment (Sellin, 1959). One strength of the matching design is that it allows researchers to control for the short- and long-term impacts of historical, cultural, and regional factors that may not be recognized (Peterson and Bailey, 1988). However, matching (comparative) studies also have drawbacks. The matching design cannot control for all possible variables other than the death penalty statute that might influence the homicide rates, because it is always possible that a relevant variable has been overlooked by the researchers (Baldus and Cole, 1975; Klein, Forst, and Filatov, 1978; Peterson and Bailey, 1988). Furthermore, the matching design makes it difficult to separate the direct and reverse causal effects between the death penalty and homicide rates (Klein et al., 1978). In addition, it is possible that the researcher’s subjective value judgments could affect the selection of contiguous states to compare (Klein et al., 1978). Moreover, the matching approach cannot be applied within the South because this region has no retentionist or abolitionist states to be compared. Therefore, multivariate techniques, such as cross-sectional or time-series designs, are necessary to overcome many of the shortcomings of the matching technique used in earlier studies. Multivariate cross-sectional designs have been employed to minimize some of the limitations that arise with time-series design (Bailey, 1973, 1975, 1976, 1977, 1980; Baldus and Cole, 1975; Bechdolt, 1977; Black and Orsagh, 1978; Boyes and McPheters, 1977; Brumm and Cloninger, 1996; Cloninger, 1977, 1987; Ehrlich, 1977; Forst, 1977; McAleer and Veall, 1989;
45 Passell, 1975; Peterson and Bailey, 1988; Veall, 1992; Yunker, 2001). This design studies differences in homicide, executions risk and control variable for areas, such as states, counties, or cities. The use of these smaller, subnational units enables researchers to avoid the mistaken assumption that all states authorized the death penalty during the study period and allow them to distinguish abolitionist states from de facto abolitionist states (Avio, 1979). In addition, the cross-sectional design includes potentially important control variables that may not be available in time-series design. For example, a variable measuring the incapacitative effect, such as the average term of imprisonment for persons convicted of murder and not executed, was unavailable in Ehrlich’s (1975) time-series study (Ehrlich, 1977; Forst, 1976). Despite these advantages, the cross-sectional design also has a specific drawback: It fails to adequately establish the direction of the causal relationship between the use of the death penalty and the homicide rate. Because cross-sectional design relies on data collected at one fixed point in time, it is impossible to distinguish the deterrent effect of the use of the death penalty on the level of homicide from the effect of the homicide rate on the use of the death penalty. Most death penalty studies using cross-sectional data have focused only on the deterrent effect of the death penalty on homicide, failing to rule out the reverse effect of homicide on the use of the death penalty (Ehrlich, 1975; Kleck, 1979; Peterson and Bailey, 1988; Shepherd, 2005). Researchers have disagreed about whether the level of homicide decreases or increases the prevalence of the death penalty. Some scholars (Peterson and Bailey, 1988) have argued that a higher level of homicide may lead to less use of capital punishment, whereas others maintained that a higher level of homicide may contribute to greater use of capital punishment due to increased public demands for harsher punishment of murderers. As a result, ignoring the possibility of reverse causation could lead to biased results that underestimate, overestimate, or reverse the impact of death penalty on homicides. Another shortcoming of the cross-sectional design is due to the fact that most cross- sectional studies rely on annual or monthly temporal data. Given that the deterrent effect of the death penalty on homicide may persist only for a relatively short period of time after executions, the cross-sectional design may fail to detect a relatively small and short-lived deterrent effect of the death penalty on homicide.
46 Many previous studies have employed time-series design to address the shortcomings inherent in matching or cross-sectional designs (i.e., Bowers and Pierce, 1975, 1980; Ehrlich, 1975; Land, Teske, and Zheng, 2009; Phillips, 1980; Phillips and Hensley, 1984; Stolzenberg and D’Alessio, 2004; Yunker, 2001). The time-series approach is better able to identify a direction of the causal relationship between the use of death penalty and the homicide level (Ehrlich, 1975; Kleck, 1979). The use of the death penalty may influence the homicide rate, or the homicide rate may influence the use of death penalty. Under cross-sectional design, a negative effect of executions on homicide may be concealed by a positive effect of homicides on executions (Baldus and Cole, 1975; Ehrlich, 1975). For example, a high murder rate may generate an increase in the levels of execution. Thus, using a time-series approach to identify the causal relationship between the use of death penalty and the homicide rate can provide better evidence for or against the true deterrent effect of death penalty. The time-series design also suffers from several weaknesses. Some studies employing time-series data have exhibited a serious aggregation problem, which occurs when all lower- level cases are merged into a single higher-level unit of analysis and represented as one group (Albert, 1999; Baldus and Cole, 1975). Because all discrete areas, such as states, counties, or cities, are aggregated into a single nation as a whole in time-series studies, it has been difficult for such studies to measure the extent to which a change in the prevalence of the death penalty is associated with a change in homicide rates in individual states. For example, even though the nation’s homicide rate may be lower when execution rates are higher, it is possible that the lower homicide rates prevail in states where execution rate are lower. Both time-series and cross-sectional designs have in common the fact that they generally use relatively few observations. This leads to larger standard errors of coefficients, making it harder to reject the null hypothesis or make strong statistical conclusions. Because many death penalty studies to date have employed monthly or annually aggregated crime data, they generally have utilized small sample sizes. For example, consider two different studies intended to investigate the deterrent effect of the death penalty: One study employs a national time-series data set for the nation as a whole (N=1) over a 50-year period (N=50) (1950-2000), and the other uses a state-level, cross-sectional data set for the 50 states (N=50) for a single year, 2000 (N=1). Either study relies on just 50 observations.
47 Acknowledging that both time-series and cross-sectional designs are necessarily imperfect methods for testing the deterrent effect of the death penalty, several researchers and the National Academy of Sciences panels have called for new research designs using more disaggregated data and, ideally, a panel design (Avio, 1998; Cameron, 1994; Chamlin, Grasmick, Bursik, and Cochran, 1992; Dezhbakhsh, Rubin, and Shepherd, 2003; Greenberg and Kessler, 1982; Hoenack and Weiler, 1980; Zimring and Hawkins, 1973). Recently, many death penalty studies have employed more disaggregated units of analysis and panel designs, analyzing each U.S. county or each of the 50 states, for a series of months or years (Albert, 1999; Cloninger, 1992; Dezhbakhsh and Shepherd, 2006; Dezhbakhsh, Rubin, and Shepherd, 2003; Donohue and Wolfers, 2005; Ehrlich and Liu, 1999; Ekelund, Jackson, Ressler, and Tollison, 2006; Fagan, Zimring, and Geller, 2006; Katz, Levitt, and Shustorovich, 2003; Liu, 2004; Mocan and Gittings, 2003; Peterson and Bailey, 1988; Shepherd, 2004, 2005; Zimmerman, 2004, 2006). Panel design has some advantages over both time-series and cross-sectional designs (Dezhbakhsh, Rubin, and Shepherd, 2003; Mocan and Gittings, 2003; Shepherd, 2004; Zimmerman, 2004). The first advantage is that the number of observations is larger than in time- series or cross-sectional designs. For example, consider one panel study that examines the deterrent effect of the death penalty on homicide rates for the 50 states over a 50-year period (1950-2000). The maximum number of observations would be 2,500 state-years (50*50=2,500). Therefore, panel design permits more precise estimates of coefficients and a greater ability to reject the null hypothesis than the other designs (Shepherd, 2005). Second, panel design allows the analyst to test for lagged effects of executions using lags of differing length. Researchers also have noted frequent disagreements about the lag structure between death sentence and execution (Kovandzic, Vieraitis, and Boots, 2009). In addition, Chamlin, Grasmick, Bursik, and Cochran (1992) suggested that the panel approach is well suited to the task of disentangling the lagged reciprocal relationship between the level of sanctions and the level of crime using data that contain information for a large number of jurisdictions spanning multiple points in time. Finally, several economists have pointed out that panel design is a useful tool to overcome the omitted variable problem (Dezbakhsh, Rubin, and Shepherd, 2003; Shepherd. 2004; Zimmerman, 2004). The panel design enables researchers to control for unseen state- specific or year-specific heterogeneity by using area dummies and temporal dummies. Therefore,
48 as Zimmerman (2004) pointed out, panel design is likely to eliminate the influence of a large number of unobservable geographic and temporal factors. Some researchers have employed a natural experimental design based on the existence of a set of the first executions in each state either after the nation-wide end of the moratorium in 1976 or after the reinstatement of the death penalty in previously abolitionist states (Bailey, 1998; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; Lester, 1979; McFarland, 1983; Thomson, 1997, 1999). Because these were precedent-setting executions in the given states, they naturally received greater-than-average media coverage, possibly raising public awareness about the risk of capital punishment. Studies researching such historical executions may be able to detect deterrent effects that would be diluted in studies of large number of executions, most of which had little or no unique deterrent effect. In contrast, one disadvantage of the natural experimental design is that a pattern of findings across these studies might not be generalizable any larger population of settings, because these studies were limited to only one state and to a particular time period. Additionally, the executions included may have had unusually large deterrent effects precisely because these studies received an exceptional amount of media attention, since they were the first in the state where the executions were carried out. Broadcast and newspaper coverage of first executions declined as the number of executions increased (Jocoby, Bronson, Wilczak, Mack, Suter, Xu, and Rosenmerkel, 2008; McFarland, 1983). In sum, it is difficult to draw generalizable causal inferences from studies employing natural experimental design. Further, scholars using this design generally had little, if any ability to control for changing social conditions of the research settings. For example, McFarland (1983) found that the murder rate decreased by a statistically significantly amount just after the execution of Gary Gilmore in 1977, but he attributed the decrease in the murder rate to the unusually severe winter weather, rather than the execution. Unit of Analysis This section addresses the kinds of temporal and geographic units of analysis that have been employed in previous studies of the deterrent effect of the death penalty. Selecting the most appropriate temporal and geographic units of analysis is a perennially important issue in the field of research on the death penalty’s deterrence effect. Although previous studies have made extensive use of highly aggregated temporal and/or geographic units of analysis, some previous
49 studies have suggested that a much more disaggregated temporal and/or geographic unit of analysis should be used in future studies. The geographic and temporal units of analysis in past research have often been chosen based solely on the availability of data. Although many earlier death penalty studies used the year as the temporal unit of analysis and the nation as the geographic unit of analysis, many recent studies conduct temporal analysis at the monthly or weekly level and geographic analysis at the state, county, or city level. Temporal Unit of Analysis Most death penalty studies have relied on the year as the unit of analysis (i.e., Bowers and Pierce, 1975; Dezhbakhsh and Shepherd, 2006; Dezhbakhsh, Rubin, and Shepherd, 2003; Ehrlich, 1975, 1977; Fagan, Zimring, and Geller, 2006; Katz, Levitt, and Shustorovich, 2003; Kleck, 1979; Mocan and Gittings, 2003; Shepherd, 2005; Yunker, 2001; Zimmerman, 2004, 2006). Early time-series and cross-sectional studies typically employed the year as the unit of analysis because the only data sets available to researchers were geographically and temporally aggregated. Even recent panel studies still commonly use the year as the temporal unit of analysis, although geographic data are disaggregated to much smaller units of analysis, such as the state or the county (Dezhbakhsh, Rubin, and Shepherd, 2003; Katz, Levitt, and Shustorovich, 2003; Mocan and Gittings, 2003; Zimmerman, 2004). Although panel design increases the number of observations compared to the early studies, using the year as the unit of analysis may be inappropriate for detecting the deterrent effect of the death penalty on homicide, if the number of homicides deterred by executions is too small to be detected in annual data (Hjalmarsson, 2009, 2012; Land, Teske, and Zheng, 2012). Although Lester (1979) suggested that the deterrent effect of a given execution lasted for approximately one year, many scholars argued that the deterrent effect of the death penalty on homicide can disappear within three or four days of an execution (Andenaes, 1952; Nagin, 1998; Phillips and Hensley, 1984). Thus, it would not be surprising to find that evidence consistent with the deterrence hypothesis has not been detected by death penalty studies employing the year as the temporal unit of analysis (Grogger, 1990; Hjalmarsson, 2009, 2012; Phillips, 1980; Phillips and Hensley, 1984). When the incident-based SHRs became available in 1982, it made possible a number of studies that used the month as the unit of analysis (Bailey, 1983, 1990; Bailey and Peterson, 1989; Bowers and Pierce, 1980; Cloninger and Marchesini, 2001; King, 1978; Peterson and
50 Bailey, 1987; Shepherd, 2004; Sorenson, Wrinkle, Brewer, and Marquart, 1999; Stack, 1987, 1990, 1998; Stolzenberg and D’Alessio, 2004; Thomson, 1997, 1999). Because a smaller temporal unit of analysis can overcome the aggregation problems stemming from a larger temporal unit of analysis, the use of monthly data has gained popularity in studies attempting to measure the deterrent effect more precisely. For example, monthly fluctuations in homicide rates are far more variable than year-to-year shifts, so monthly data can enable researchers to observe brief fluctuations in homicide rates that are unobservable when using annual data (Shepherd, 2004). In addition, prospective murderers receive new information about crime and punishment every time they hear about an execution. Thus, it seems reasonable to assume that prospective murderers are likely to update their beliefs about the probability of being executed at least once a month rather than once a year (Shepherd, 2004). Nevertheless, as several scholars have pointed out, because the deterrent effect of an execution may last only for a few days immediately before and after an execution and is likely to be observable in daily data, even the month may be too long a time unit for death penalty studies (Andenaes, 1952; Grogger, 1990; Hjalmarsson, 2009; Nagin, 1998; Phillips, 1980; Phillips and Hensley, 1984). Only a few studies have employed a shorter temporal unit of analysis, such as the week (Bailey, 1998; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; McFarland, 1983; Phillips, 1980). Most studies employing the week as the temporal unit of analysis have focused solely on the deterrent effect of a single first post-Moratorium execution on the homicide rate (Bailey, 1998; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; McFarland, 1983), and therefore cannot provide aver generalizable results. Because the unique deterrent effect of the death penalty on homicide rates may disappear within days after an execution, the deterrent effect is most likely to be detected if studies employ the smallest possible temporal unit of analysis. A very few studies have done so, using very short time periods, such as the day, as the unit of analysis (Grogger, 1990; Hjalmarsson, 2009; Phillips and Hensley, 1984; Stack, 1995). According to Grogger (1990), a short-term deterrent effect would be detected if the average number of daily homicides decreased during the period immediately before or immediately after an execution rather than during more remote periods. Geographic Unit of Analysis Many time-series studies have used the nation as the unit of analysis (i.e., Bowers and Pierce, 1975; Ehrlich, 1975; Phillips and Hensley, 1984; Yunker, 2001). The key limitation of
51 these studies is that they are subject to the spatial aggregation problem, which occurs when state- level homicide and execution variables are computed on a national basis. State-level variations in executions and homicides are ignored in national-level studies. The existence of a statistically significant relationship between the death penalty and homicide rates at a smaller geographic unit of analysis may be undetectable when a more aggregated unit of analysis is used. For example, national-level studies are unable to distinguish death-penalty states from non-death- penalty states. As Peterson and Bailey (1991) suggested, it is necessary to use the state as the geographic unit of analysis to detect regional differences, because the vast majority of executions have taken place in southern states, meaning that the residents in southern retentionist states are more affected by the risk of execution than residents of other retentionist or abolitionist states. Because appropriate UCR data on arrests, convictions, and executions are readily available on a smaller geographic scale, such by state, many cross-sectional and panel studies have employed the state as the geographic unit of analysis (i.e., Dezhbakhsh and Shepherd, 2006; Ehrlich, 1977; Fagan, Zimring, and Geller, 2006; Forst, 1977; Grogger, 1990; Katz, Levitt, and Shustorovich, 2003; Shepherd, 2004; Yunker, 2001; Zimmerman, 2004, 2006). Many death penalty studies have attempted to use data aggregated to the state level, mainly because capital punishment laws are enacted at the state level and only state courts can impose death sentences (Zimmerman, 2004, 2006; Dezhbakhsh and Shepherd, 2005). Furthermore, using the state as the geographic unit of analysis is the only way to measure differences in the presence of the death penalty laws and the actual number of executions within a given state; this is simply not possible when using the nation as the unit of analysis. A small set of studies have used a smaller geographic unit of analysis, such as the county (Dezhbakhsh, Rubin, and Shepherd, 2003; Fagan, Zimring, and Geller, 2006; Shepherd, 2005; Stack, 1998). Like studies employing state-level panel data, most studies using counties do so to estimate any deterrent effect more precisely. Some scholars have argued that county-level panel data allows researchers to avoid statistical problems associated with more aggregated geographic units of analysis, such as aggregation bias and omitted variable bias (Dezhbakhsh, Rubin, and Shepherd, 2003; Shepherd, 2005). For example, county-level data may enable researchers to capture the demographic, economic, and jurisdictional differences among all U.S. counties while reducing aggregation bias. Likewise, researchers may control for unobserved heterogeneity across counties, thus avoiding the bias that arises from the correlation between county-specific
52 effects and judicial and law enforcement variables. For example, as Shepherd (2005) pointed out, a change in the murder rate may be caused by county trends in crime rates, attitudes toward crime, or the criminal justice system. In addition, county-level panel data provide a larger number of observations than state-level panel data, increasing degrees of freedom and variability and reducing the effects of collinearity among other independent variables. However, Zimmerman (2004) raised questions about the use of county-level panel data from a statistical perspective. At the county level of jurisdiction, no real distinctions can be made in the number of people who are sentenced to death and executed, because capital punishment laws are enacted only at the state level (by the courts and at the state-level legislature). Furthermore, county-level panel data contain a larger number of zero-value observations than state-level panel data, which increases the possibility that the results will be biased. A very small number of studies have employed the city as the geographic unit of analysis (Bailey, 1983; Brumm and Cloninger, 1996; Hjalmarsson, 2009; Stolzenberg and D’Alessio, 2004; Thomson, 1997). Some researchers chose to use city-level data because murder rates are generally much higher in large metropolitan areas of a given state than in other areas (Bailey, 1983; Thompson, 1997) or because homicide rates tend to increase or decrease only in the city where the executed offender was convicted or where the execution is publicized (Hjalmarsson, 2009). A few studies have used city-level data because information regarding changes in execution risk is more likely to be disseminated quickly in a smaller geographic unit of analysis than a larger one (Brumm and Cloninger, 1996; Stolzenberg and D’Alessio, 2004). Homicide Data Sources This section summarizes the advantages and disadvantages of each of the major homicide data sources that have been used in death penalty deterrence studies: (1) the Federal Bureau of Investigation’s (FBI’s) Uniform Crime Reports (UCR), (2) the Supplementary Homicide Reports (SHR), (3) the Vital Statistics, and (4) metropolitan police departments. Many scholars consider vital statistics to be superior because they are 100% complete for all areas, for all years since 1933, whereas UCR data are missing for many jurisdictions and must be estimated. The FBI’s UCR data provide a reasonable proxy for capital murders, so a large number of death penalty studies have relied extensively on the UCR (e.g., Bailey, 1984; Dezhbakhsh, Rubin, and Shepherd, 2003; Ehrlich, 1975, 1977; Peterson and Bailey, 1988; Shepherd, 2005; Zimmerman, 2006). UCR is an acceptable data source for researchers wishing
53 to examine the deterrent effect because almost all murders that occur are reported to the police (Cook, 1980). However, a well-recognized problem with UCR data is that it combines “murders” and “non-negligent homicides” into one homicide reporting category (Albert, 1999; Bailey, 1983; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; Peterson and Bailey, 1988). Although most researchers believe that that the UCR homicide data is still a good proxy for first- degree murders, based on the assumption that the ratio of first degree murder to total homicides is constant, this assumption has not been tested systematically (Bailey, 1983). Accordingly, the use of UCR homicide data reflects the total number of persons who died at the hand of another person, rather than the total number of persons who killed someone with premeditation and deliberation (Albert, 1999). Many police departments fail to report their crime statistics to the FBI, so the FBI must estimate all this missing data. Estimation introduce additional measurement errors. Alternatively, some researchers have turned to the FBI’s SHR data (Bailey, 1998; Cochran and Chamlin, 2000; Cochran, Chamlin, and Seth, 1994; Fagan, Zimring, and Geller, 2005; Peterson and Bailey, 1991; Shepherd, 2004; Sorensen, Wrinkle, Brewer, and Marquart, 1999; Thompson, 1997, 1999; Zimmerman, 2004). The SHR data contain an extensive range of detailed information on each homicide event known to the police, including the month, year, and location of an offense; the age, race/ethnicity, and gender of victims and offenders; the victim/offender relationship; the use of weapons; and circumstances of the crime. Researchers use monthly SHR homicide data to measure the deterrent effect more precisely than is possible using annual UCR data. However, SHR data suffers from problematic reporting practices (Fagan, Zimring, Geller, 2006; Stolzenberg and D’Alessio, 2004). First, non-reporting is an issue: Participation in the SHR program is voluntary, and some law enforcement agencies simply do not contribute their homicide statistics (Fagan, Zimring, and Geller, 2005). Second, important information about the characteristics of victim and offender is frequently missing. For example, as Stolzenberg and D’Alessio (2004) pointed out, the age of the offenders is often missing. These researchers note that such information is important for death penalty studies because it determines whether the offender is eligible to receive the death penalty. Third, law enforcement agencies can record an attack as a homicide only when the victim actually dies (Stolzenberg and D’Alessio, 2004). So,
54 police statistics may fail to record a homicide for a given time period because the homicide victim died weeks or months after being attacked or injured by the offender. Other researchers have used non-police data sources, such as mortality and morbidity data, or the Vital Statistics data compiled by the Centers for Disease Control and Prevention (Bailey, 1990; Bailey and Peterson, 1989; Bowers and Pierce, 1975; Cover and Thistle, 1988; Ehrlich, 1977; Grogger, 1990; King, 1978; Kleck, 1979; Marvell and Moody, 1999; McFarland, 1983; Layson, 1985, 1986; Phillips and Henley, 1984; Stack 1987, 1995). These data are useful for researchers attempting to measure the short-term deterrent effect on a daily basis, because the data contain information on the exact dates of homicides. In addition, a few researchers have used either homicide incident data provided by individual metropolitan police departments (Hjalmarsson, 2009; Stolzenberg and D’Alessio, 2004) or homicide data from the Crime Control Institute (Brumm and Cloninger, 1996). Except for two studies comparing state executions and homicide rates before and after the moratorium period (Chressanthis, 1989; Dezhbakhsh and Shepherd, 2006), most death penalty studies have used either pre-Moratorium data (e.g., Bowers and Pierce, 1975, 1980; Cover and Thistle, 1988; Ehrlich, 1975, 1977; Forst, 1977; Graves, 1956; Grogger, 1990; Hoenack and Weiler, 1980; Katz, Levitt, and Shustorovich, 2003; Kleck, 1979; Phillips, 1980; Phillips and Hensley, 1984; Shepherd, 2005; Stack, 1998) or post-Moratorium data (e.g., Albert, 1999; Dezhbakhsh, Rubin, and Shepherd, 2003; Fagan, Zimring, and Geller, 2006; Mocan and Gittings, 2003; Shepherd, 2004, 2005; Zimmerman, 2004, 2006). These two data sets were used because there were no executions in the U.S. for the 10-year moratorium on capital punishment for the periods 1968 to 1976. Post-Moratorium data will likely gain popularity among researchers, because, in the contemporary debate over capital punishment, research findings based on more recent data (post-1976) will be more relevant and applicable to current policy debates than research findings based on older data (pre-1968) (Dezhbakhsh, Rubin, and Shepherd, 2003). Summary Based on the literature review and the research results we identified some important future research directions. In the existent literature, the advantages and disadvantages of the research methods in the previous studies are presented and discussed. Therefore, future research needs to use small time units; use data covering all executions in the United States; use vital
55 statistics homicide data; and address likely shifts in perceptions of execution risk produced by volume of news about executions.
56 CHAPTER 4
RESEARCH METHODOLOGY
This chapter presents the research methods that were used to conduct this study. Research methods discussed herein include the research design, the research data sources, the dependent variable, the main independent variable of interest, control variables, and statistical analysis. Because some original data were collected only on a yearly basis, linear interpolation technique was used to yield daily estimates of relevant variables. Finally, count regression models are discussed. Research Design The present study employs a panel design combining time-series and cross-sectional data for all 50 states and the District of Columbia in the United States for each day of the 20 years from January 1, 1979, to December 31, 1998. The beginning and ending dates of the study period were chosen for a number of reasons. First, no executions were carried out anywhere in the United State between 1972 and 1976 because of the moratorium on all state executions imposed by the U.S. Supreme Court in Furman v. Georgia in 1972. Employing the post-moratorium data would make our statistical reference more relevant to America’s current capital punishment debate. Second, the choice of the starting and ending dates might be somewhat arbitrary because there was a two-year temporal gap between the starting year of this study period and the ending year of the de facto moratorium. Data for the years 1977 and 1978 are excluded from the dataset because only one execution was carried out in the United States in 1977 and none in 1978 (The Death Penalty Information Center, 2015; Espy and Smylka, 2004). The ending date of the dataset is chosen primarily because full national data on daily homicide counts after 1999 were unavailable to public at the time of data collection.23 The panel dataset used in the present study is balanced, comprising all daily homicides in the 50 U.S. states plus the District of Columbia between January 1, 1979 and December 31,
23 The researchers involved with this dissertation contacted the Centers for Disease Control and Prevention (CDC) to request access to restricted data on daily homicides at the state level. However, the CDC refused the request because it believed that the present study might violate the homicide victims’ privacy.
57 1998.24 Because the main purpose of the present study is to assess whether an execution has a short-term deterrent effect on homicides, the present study employs data disaggregated to the daily level. Using daily time units increases sample size and degrees of freedom more than using a longer temporal unit of analysis, such as year or month. Therefore, temporal disaggregation allows one to overcome aggregation bias associated with temporal aggregation, and to detect effects that may last only a few days. Given that state legislatures enact capital punishment laws and statutes, and the state supreme courts review all death sentences, the existence of the death penalty is determined by state legislatures. Employing states as the geographical unit of analysis is therefore theoretically appropriate. In any case, there is virtually no county-level variation in the number of persons executed (Zimmerman 2004, 2006). Therefore, the state-day is the unit of analysis in this study. This panel dataset in the present study contains 51 areas per wave (N = 7,305 days) and the total number of cases in the dataset, or the sample size, is 372,555.25 To our knowledge, this is the first research to use daily homicides for more than a single state or for more than two or three years. Accordingly, the present study should provide greater generalizability. Research Data Sources The panel dataset used in the present study is collected and integrated from several different data sources, including the National Center for Health Statistics, the Espy File, the Death Penalty Information Center, Calendars, Census Data, the National Prisoner Statistics, the Vanderbilt Television News Archive, and the Lexis-Nexis Academic Universe Data. The National Center for Health Statistics: Data on daily homicide counts are collected from the annual Mortality Detail File tapes from the Inter-University Consortium for Social and Political Research at the University of Michigan. The National Center for Health Statistics (NCHS) of the Centers for Disease Control and Prevention (CDC) produces a Mortality Detail
24 A panel dataset consists of observations of a set of observational units over time (Wooldridge, 2002). One needs to distinguish between balanced and unbalance panels. If data for each day are available for all 51 states and the District of Columbia, the panel is said to be balanced. If data are missing for some states and the District of Columbia on certain days, the panel is said to be unbalanced. Because there are no missing data in any of the variables, the dataset in this research is called a balanced panel. 25 The word “wave” refers to the total number of days between January 1, 1979, and December 31, 1998, and the word “area” refers to the states in the United States. Therefore, the sample size (N=372,555) is obtained by multiplying 51 by 7,305.
58 File (MDF) which is a computer-readable collection of all death certificates recorded in the United States for any given year, except for all American deaths outside the United States (Department of Health and Human Services, 1988).26 Each death certificate contains all details, including a single underlying cause of death classified in accordance with the ninth version of the International Classification of Diseases (ICD-9) codes and definition of 72 cause-of-death recodes as well as other significant information about the death: demographic information about the deceased victim, i.e., race, sex, marital status, state of birth, and age at death (specific age recorded to 16 age groups); the full date of death, including the day, month, and year of death; the place of death, i.e., state and county; place of autopsy performed; and so on. MDFs come in two versions: restricted-use files and public-use files. Although they both contain similar information, the difference between them is quite straightforward. Unlike the public-use MDF file, the restricted-use MDF file provides more detailed mortality information on the full date of death, including month, day, and year (NCHS, 2012). Because the purpose of the current study is to test the research hypothesis about the short-term deterrent effect of executions on homicides, the choice of data source to consider for this study is subject to the availability of daily homicide counts. To the best of our knowledge, the restricted-use MDF data are the only national-level data currently available to satisfy the requirements of the present research. Furthermore, the MDF is superior to police data resources such as the Uniform Crime Report (UCR) and the Supplementary Homicide Reports (SHR). Very often, the UCR data do not accurately reflect all homicides (Bowers and Pierce, 1975; Dezhbakhsh, Rubin, and Shepherd, 2003; Kleck, 1979), because not all police departments and law enforcement agencies are compelled to report crime to the UCR reporting program. Although the use of the MDF data is ideal for the purpose of this study, these MDF data should be used with caution. Death certificates may unintentionally contain misleading or inaccurate information about homicides. In general, death certificates are filed according to the date and place of the decedent’s death. This is problematic because some homicides do not
26 A physician, coroner, or medical examiner should complete a death certificate within 24 hours after every death is reported to relevant state agencies. Reporting of deaths is required by law. Failure to report a death could lead to prosecution. Once the death certificate record is registered with a local register, it is automatically transmitted to the NCHS. In case the death record provided is incomplete or inaccurate, the NCHS classifies the cause of the death. Finally, the NCHS compiles information from all death certificates furnished by the 50 States and produces the national mortality data files.
59 always follow immediately after unlawful physical attacks by one person against another person. Some deaths may result from injuries inflicted days, weeks, or even months after the physical attack occurred. Suppose that a person received a stab wound in a robbery on July 31st in a city in the state of Florida, located near the Florida and Georgia borders, but victim survived for the next four days in a local hospital in the state of Georgia. In this case, a medical examiner or a physician would issue a death certificate, declaring the date and place of the homicide as occurring in August rather than in July and in Georgia rather than Florida. This recording practice is problematic for the current research purposes because it would theoretically be best to use the date and place that the fatal attack occurred rather than the date and place that the victim died. The MDF and the UCR data do not report statistics about first degree murder. Use of these data does not allow us to separate first degree murder from second degree murder. Any attempt to differentiate first degree murder from second degree one without subjective judgement error is virtually impossible (Dezhbakhsh, Rubin, and Shepherd, 2003). The Espy File and the Death Penalty Information Center: Data on all executions carried out in the United States are taken from the Espy File, from the Inter-University Consortium for Social and Political Research at the University of Michigan. Death penalty historian Major Watt Espy Jr. devoted more than 40 years of his life to chronicling all executions that occurred in the United States between 1608 and 1987. The so-called Espy File was updated by two principal researchers, Major Watt Espy Jr. and John Ortiz Smylka, to include an additional 15 years, documenting 15,269 executions from 1608 through 2002. The Espy File includes information on age, race, name, sex, and occupation of the offender; place, jurisdiction, date, and method of execution; and the crime for which the offender was executed. Although the Espy File has been cited very often by death penalty researchers, some Espy records, with respect to dates, places, method of execution and race of the offender, were incorrectly coded.27 Accordingly, the present study uses another data resource from the Death Penalty Information Center (DPIC) to check on the Espy data. Using the DPIC data set ought to
27 For example, Espy and Smylka recorded the executions of (1) Harold Otey, executed by electrocution in Nevada on September 02, 1994, (2) John Joubert, electrocuted in Nevada on July 17, 1996, and (3) Robert E. Williams, electrocuted in Nevada on December 02, 1997. However, other sources consistently show that all of these executions had actually been carried out in Nebraska on the same execution dates. While this may be a minor coding error in the time-series or cross-sectional studies, this should be a serious error for the present research. Thus, the present research corrects the information on the state of execution for these execution events.
60 be the best choice because the DPIC monitors and collects information about the death penalty through Department of Corrections’ web sites and media coverage of the death penalty (DPIC, 2015). The presence of duplicate records is a major data quality concern in the present study. When duplicated execution records are detected, further investigation is undertaken. Also, the DPIC website offers invaluable information on the full dates of the abolition and/or reinstatement of the death penalty in all 50 states and the District of Columbia. Calendars: Calendars for the years between 1979 and 1998 are available online (www.timeanddate.com/calendar). These calendars are useful when national holiday and day variables are coded in this study. Seven days of the week and most national holidays fall on different dates each year. Although Martin Luther King, Jr. Day is observed on the third Monday of January each year, these are different dates every year.28 Other national holidays, such as Good Friday, Easter, Memorial Day, Labor Day, and Thanksgiving, are movable with dates shifting from year to year. In addition, dates have a different day of the week each year. The United States Census Bureau Data (from http://census.gov/popest/data/historical/index.html): The United States Census Bureau has counted every person residing in the United States, Puerto Rico, the U. S. Virgin Islands, and other U. S. territories every 10 years since 1790 (The United States Census Bureau, 2015). To allocate federal funds and calculate annual population change, the Census Bureau’s Population Estimates Program produces annual estimates of the total populations for each state. These estimates are based on the most recent decennial census data and the counts supplied by states and localities. While the U.S. Census survey has recently been conducted on April 1 every 10 years, the population estimates pertain to July 1 of each year. The current study will rely primarily on the annual population estimates and use the 1980, 1990, and 2000 decennial censuses. Because the census data and the population estimate data are collected annually, these data should be calculated again for the current study. Therefore, a linear interpolation method will be used to generate a total population estimate on a daily basis for all 50 states and the District of Columbia. Further explanation of this method will be provided later in the control variable section within this chapter.
28 For example, Martin Luther King Jr. Day was observed on January 15 in 1990 but was celebrated on January 21 in 1991.
61 The National Prisoner Statistics (NPS) (retrieved October 15, 2015, from http://www.bjs.gov/index.cfm?ty=pbdetail&iid=2080): The Bureau of Justice Statistics (BJS) publishes the National Prisoner Statistics (NPS) every year to provide national- and state-level data on the numbers of prisoners in state and federal prison facilities. The NPS contains information about the demographic characteristics of the prisoners from departments of corrections in all 50 states and the District of Columbia, including the age, race, and sex of the prisoner; number of state and federal prisoners held in private facilities and local jails; state prison capacity; and prisoners under age 18 in state and private adult correctional facilities. Like the U.S. Census data, the current study will use linear interpolation method to estimate daily state prison populations. The Vanderbilt Television News Archive (retrieved October 15, 2015, from http://tvnews.vanderbilt.edu/): This database is the most extensive and complete archive of evening television news broadcasts in the United States. The archive holds more than 30,000 individual regular and special network evening news broadcasts from major U. S. national broadcast networks: the American Broadcasting Company (ABC), Columbia Broadcasting Company (CBS), and the National Broadcasting Company (NBC) since 1968; Cable News Network (CNN) since 1995; and Fox Broadcasting Company (Fox News) since 2004 (The Vanderbilt Television News Archive, 2012). Because the present study covers January 1, 1979 through December 31, 1998, it will use television news stories broadcast only by three major national television networks: ABC, CBS, and NBC. Because data about state or local television networks are unavailable from the Vanderbilt Television News Archive, the present study does not employ the news stories broadcast by state or local television networks. The data about television news coverage of executions is appropriate in the present study for several reasons. Some surveys report that the majority of Americans consider that televisions provide the most complete, intelligent, trustworthy, and unbiased source of news, and use television more than all other news media sources for their daily news (Bailey and Peterson, 1994; Peterson and Bailey, 1991). Also, both illiterate and literate persons have access to television. Given that much of the adult U.S. inmate populations is illiterate (Ryan, 1990), television is one of the most important sources of information for this group of people. Also, television networks expect to bring execution news to as many as people as possible because few news outlets other than broadcasting television networks cover almost the entire United States.
62 General deterrence research and death penalty studies in particular have not directly measured how potential offenders perceive the risk of legal punishment, so this is a valuable data source for the present study, to use as a proxy for the perception of the risk of executions among prospective killers. Data about television news stories about executions thereby amplify over ability to assess the deterrent effect of executions. However, employing television as the source of information has one weakness. Only a few exceptional execution cases receive extensive attention from the television media. According to Jacoby, Bronson, Wilczak, Suter, Xu, and Rosenmerkel (2008), news editors are interested in picking up a story that they think newsworthy. Executions are less likely to be covered in news coverage when they are less competitive with contemporaneous events in terms of newsworthiness. The coverage of executions depends on the number of the federal, state, and international contemporaneous events. This implies that television coverage of executions provide little opportunity to remind prospective murderers of the threat of executions. In general, the searching procedure about past executions was as follows: From the Vanderbilt Television News Archive web page, one may look for the menu bar at the top of the page. Once one clicks on the “Search” section, one may open a new window. In the following window page named “TV-News Search,” one may put the cursor on the “Advanced Search” box. The next thing to do is to enter your keywords, such as full name of the offender, and the state and exact time of the given execution, into the “Enter Words to Search” box. Also, select two dates between 14 days before the execution date and 14 days after the date in the “Limit Search to a Specific Date” box. One may limit the search to all networks in the “Network” box and restrict the searching option to evening news in the “Exclude Results from” section. In addition, one may move the cursor onto “Sort the Results” and then click on “Oldest Material First.” Finally, one may click on the “Search” button. The Lexis-Nexis Academic Universe Data: In light of the limitations of data on television news, we also gathered data on news stories about executions appearing in print outlets. This database offers access to full-text publications from hundreds of sources, such as newspapers, magazines, newsletters, and journals in the 50 U.S. states and the District of Columbia (The Lexis-Nexis Academic Universe, 2012). Unlike many electronic databases that cover only materials published in a relatively recent time period, the Lexis-Nexis Universe database can cover daily newspaper stories going as far back as January 1, 1979. The Lexis-Nexis Universe
63 also is the best database to search for only daily newspaper articles published by newspapers and news providers in the United States because it covers hundreds of news outlets in all 50 states. The Lexis-Nexis Academic Universe Data is useful because it covers a variety of kinds of newspapers. In general, there are two types of newspapers, including national newspapers and state or local newspapers, depending on circulation. For example, the national newspapers considered in the present study are The New York Times, the Washington Post, the Washington Times, the Wall Street Journal, the Christian Science Monitor, and USA TODAY, and the state and local newspapers include other newspapers. The following represents the procedure used for discovering newspaper stories through the Lexis-Nexis Academic Universe database. One may start on the Florida State University’s Main Library website and click on the “Articles and Databases” box in the upper part of the page. Then, move the cursor onto the “Most Used Databases” section next to “A - Z List” and click on it. When a new window opens, there will be a list of most used library databases. Then, click the cursor onto “Lexis-Nexis Academic” out of the databases. In the following page, one may have “Search the News” box and enter your keywords, such as full name of the offender, and the state and full date of execution, into the “Search For” box. Also, one may click on “newspapers” in the “By Source Type” and on the “Search” button in the final. Analytical Model of Daily Homicide Counts The following analytical equation model represents the basic empirical specification:
Yij = α + [Any_Execi, j-n*γi, j-n + Any_Execi, j*γi, j + Any_Execi, j+n*γi, j+n] + [Any_Newspaperi,
j-n*δi, j-n + Any_Newspaperi, j*δi, j + Any_Newspaperi, j+n*δi, j+n] + [Any_Televisioni, j-n*ζi, j-n +
Any_Televisioni, j*ζi, j + Any_Televisioni, j+n*ζi, j+n] + Day of the Weeki, j*θi, j + Monthi, j*κi, j
+ Yeari, j*λi, j + National_Holidayi, j*νi, j + State Resident Populationi, j*ξi, j + State Prison
Populationi, j*οi, j + Death Penalty Statutei, j*ρi, j + µij + ƞij + Ɛij
, where n is the order of days from 1 to 14.
The number of homicide counts (Yij) in state i and day j is regressed on four types of the main independent variable of interest: a set of 29 binary variables indicating whether an
execution of State i in the 14 days before and after j (Any_Execi, j-n*γi, j-n + Any_Execi, j*γi, j +
Any_Execi, j+n*γi, j+n); a set of 29 binary variables indicating whether a newspaper coverage of
64 executions of State i in the 14 days before and after j (Any_Newspaperi, j-n*δi, j-n +
Any_Newspaperi, j*δi, j + Any_Newspaperi, j+n*δi, j+n); and, a set of 29 binary variables indicating whether there was television coverage of executions of State i in the 14 days before and after j
(Any_Televisioni, j-n*ζi, j-n + Any_Televisioni, j*ζi, j + Any_Televisioni, j+n*ζi, j+n), respectively.
Controls for day of the week (Day of the Weeki, j*θi, j) are included, and monthly (Monthi, j*κi, j)
and yearly (Yeari, j*λi, j) dummy variables are also included. A set of noncapital variables, including total resident populations of each state (State Resident Populationi, j*ξi, j), total prison populations of each state (State Prison Populationi, j*οi, j), and the presence of the death penalty
law of each state (Death Penalty Statutei, j*ρi, j), are included. State and daily fixed effects (µij +
ƞij) are included to control for unobserved state and day characteristics. Lastly, the error term, Ɛij, is assumed to be an unobserved, mean zero random variable that is uncorrelated with the observed covariates. Variables This study incorporates (1) the dependent variable: daily counts of homicide; (2) the independent variables of main interest: executions and news coverage of the executions; and (3) control variables into the model. Dependent Variable The dependent variable used in the current study is the daily counts of homicides that occurred in each of the 50 states and the District of Columbia for each day from January 1, 1979 to December 31, 1998. The data on the daily homicide counts were taken from the Mortality Detail Files (MDFs) compiled by the National Center for Health Statistics (NCHS) of the Centers for Disease Control and Prevention (CDC). Some of the homicide cases in the MDF do not have specific information on the time of death; in particular, the day of homicide is missing. For our research purpose, these homicide cases were removed from the analysis. After the omission of these cases, 445,420 homicides of the original 446,627 total homicides for the years between 1979 and 1998 remained in the study. The term “homicide” was used synonymously with all deaths from causes E960-E969 in the ninth Revision of the International Classification of Diseases. These include deaths from fight, brawl or rape (E960); from fatal injuries by corrosive or caustic substances, except poisoning (E961); by poisoning (E962), by hanging and strangulation (E963); by submersion (drowning) (E964); by firearms and explosives (E965); by cutting and piercing instruments
65 (E966); by pushing from a high place (E967); by other and unspecified means (E968); and by late effect of injury purposefully inflicted by another person or persons (E969), respectively, for the years 1979-1998. Given that “homicide” in this study refers to all deaths intentionally and knowingly causing the death of another person or causing severe physical injury that would result in the death of a homicide victim, suicide (E950-E959), war-related deaths (E990-E999), and legal intervention (E970-E978) are excluded, because these kinds of deaths are not supposed to be subject to the deterrent effects of executions. Main Independent Variables of Interest – Occurrence of Executions and Execution Publicity The primary independent variables of interest were: (1) the occurrence of execution events on a given day in a given state, (2) daily newspaper coverage of these execution events, and (3) national television network coverage of these execution events. The first and most important independent variable of interest refers to the occurrence of executions on a given day in a given state or the District of Columbia between January 1, 1979 and December 31, 1998. Of the original executions of the 499 that actually took place in the United States during this period, only 489 executions remained in the present research, because some states previously conducted six different double executions and two separate triple executions during the period.29 Although 10 executions are not included in the analysis, there would essentially be no negative effect on the quality of the present research analysis and data collection. As Jacoby, Bronson, Wilczak, Suter, Xu, and Rosenmerkel (2008) pointed out, as something deemed newsworthy, executions attract a great deal of debate and media attention. Accordingly, some double and triple executions are reported frequently by news media, because these executions were the first for a state or set a historical precedent. Therefore, these omitted executions may be reflected indirectly to some degree in either the daily newspaper coverage of these execution events or the national television network coverage of these executions. The main independent variable of interest, execution events on a given day in a given state, was operationalized in two ways: (1) 29 dummy variables indicating whether there was an execution on a single day j in a single state i; and (2) a dummy variable indicating whether there
29 For example, Arkansas conducted two separate triple executions on August 08, 1994 and January 08, 1997. Six different executions took place in Arkansas on May 11, 1994; in Illinois on March 22, 1995 and November 19, 1997; in South Carolina on December 4, 1998; and, in Texas on January 31, 1995 and June 4, 1997. Because the independent variable in the study is a binary variable, indicating whether an execution took place on a given execution day in a given state, these double and triple executions are coded the same as single executions.
66 was an execution on any of the days within the 9 days surrounding a given day j in a given state i. Regardless of whether an execution on a given day j in a given state i was a single execution, a double execution, or a triple execution, the independent variable used for the present study is coded as one if there were any number of executions on the day, and is coded as zero otherwise. Further, twenty-eight execution binary variables were created for the 14 calendar days immediately preceding and following a given execution date. To be more precise, the 14 preceding days are denoted as E-14, E-13, E-12, …., E-3, E-2, E-1, where the “E-14” variable equals one if this was 14 days before an execution occurring within the target state and equals zero otherwise, and the “E-1” variable equals one if this was the day before an execution occurred in that state; the execution day is denoted as E, where the “E” variable equals one if there was an execution on that day in that state and equals zero otherwise. The 14 days following are denoted as E+1, E+2, E+3, …, E+12, E+13, E+14, where the “E+1” variable equals one if this was the day after an execution took place in that state and equals zero otherwise, and the “E+14” variable equals one if this date was 14 days after an execution took place in that state. Therefore, the total number of the execution binary variables is twenty-nine, including the 14 preceding-day variables, the execution date variable, and the 14 following days. Although there is no consensus among researchers about the choice of the precise length of the leads and lags to be included in the model (e. g., Grogger, 1990; Phillips, 1980; Phillips and Hensley, 1984; Hjalmarsson, 2009), the present study follows Grogger’s (1990) stance to use 14 days of leads and 14 days of lags for at least two reasons. First, a significant drop in the number of daily homicides that took place shortly before or after an execution could be interpreted more as indicating deterrence than negative effects occurring during more remote periods. Second, if statistically significant deterrent effects close to executions overlapped with a large number of statistically insignificant effects of lags and leads in the analytical equation model, any joint test would fail to reject the null hypothesis. Finally, there is no strong theoretical reason to treat leads and lags asymmetrically, i.e., to have longer lags than leads or vice versa. The second independent variable of interest was operationalized as the occurrence of an execution any time within the 29 day period surrounding day j in a given state i. This independent variable was recorded dichotomously with one indicating whether there were any
67 executions within 14 calendar days of the target date and zero otherwise.30 Within states that often carried out executions, a series of executions was occasionally carried out in a short period of time. Consequently, the 29-day period surrounding one execution sometimes overlapped with the 29-day period surrounding another execution. To illustrate how this would affect coding of the lead and lag execution variables (E-2, E-1, E, E+1, E+2, …, etc.), suppose that the day would be coded one on both the 8th day after an earlier execution was also the 5th day before a later execution in that same state. In this case, the day would be coded one on both the E+8 and E-5 dummies. The next independent variable of interest is daily news coverage of executions. Prospective offenders perceive the risk of legal punishment through a number of communication channels, including television coverage, newspaper coverage, and social networks (Cook, 1980). We use both of the only two sources of data for daily news coverage.31 First daily newspaper coverage of executions is a numerical variable indicating the number of newspaper articles published about each execution for each of the 29 days surrounding the execution. Initially, the present study used a single variable, E-14, E-13, E-12, …., E-3, E-2, E-1, E, E+1, E+2, E+3, …, E+12, E+13, E+14, to detect the effect of daily newspaper coverage of executions on homicides. Twenty-eight daily newspaper coverage of executions variables are created for the 14 calendar days immediately preceding and following a given execution. To be more precise, the 14 preceding days are denoted as E-14, E-13, E-12, …., E-3, E-2, E-1, where the “E-14” variable represents the number of newspaper stories about executions on the 14 days before an execution occurred within the same state, and the “E-1” variable represents the number of newspaper stories about executions on one day before an execution occurred in that state; the execution day is denoted as E, where the “E” variable represents the number of newspaper stories about executions on that day in that state. The 14 following days are denoted as E+1, E+2, E+3, …, E+12, E+13, E+14, where the “E+1” variable represents the number of newspaper stories about executions the day after an execution
30 For example, Arthur Jones was executed on March 26, 1986 in Alabama. The 14th day before the execution day was March 7, 1986 and the 14th day after the execution day was April 4, 1986. Therefore, the days between March 7 and April 4 in Alabama are coded as one, and other days in Alabama and other states are coded as zero. 31 Although Cook (1980) argued that radio and prospective offenders’ close acquaintances are one of the communication channels to send the deterrence message to prospective offenders, national data are unavailable to measure the effect of daily radio news coverage of the executions on homicides. Also, the effect of daily news coverage of executions through the Internet cannot be estimated because there is no national data available.
68 took place in that state, and the “E+14” variable represents the number of newspaper stories about executions 14 days after an execution took place in that state. Therefore, there are 29 daily newspaper coverage of executions variables is twenty-nine, including the 14 preceding-day variables, the execution date variable, and the 14 following days. The process of coding this variable was undertaken as follows in the present study. Take as an example of the execution of Mark Hopkinson was executed in Wyoming on January 22, 1992. The database shows that news of this execution had been published on different days by many national and local newspapers, including USA TODAY on January 9, 14, 20, 21, 22, and 23, 1992; the Chicago Sun-Times on January 22; and, the New York Times, the Washington Post, the Palm Beach Post, the Houston Chronicle, the Seattle Post-Intelligencer, and the St. Petersburg Times on January 23.32 Because USA TODAY, the New York Times, and the Washington Post fall into the national newspaper category, news story publications on January 9, 14, 20, 21, 22, and 23, 1992 are counted in the 50 states and the District of Columbia on the same days. In contrast, the news report by the Chicago Sun-Times on January 22 is counted only for Illinois on that day. Likewise, news stories published by the Palm Beach Post and St. Petersburg Times on January 23, 1992 are counted only for Florida for that day. Care was used to detect whether a newspaper published the identical story in two separate editions in one day. Counting duplicated news stories can result in inadvertent double-counting of the same news story or inappropriate weighting of the newsworthiness of a single news story. Accordingly, the present study counted as one the similar news stories which were repeatedly published by the same newspaper. The second execution publicity variable was daily national television coverage of executions. Television is considered reliable source as news much more than other sources for daily news by subsets of the populations that are disproportionately involved in homicide, including young adults, blacks, and low-income and illiterate persons (Bailey, 1990; Peterson and Bailey, 1991). This variable measures the number of national network television news stories aired about each execution during the 29 day period surrounding day j in a given state i. Twenty-nine daily television coverage of executions variables were created for the 14 calendar
32 This finding may be inconsistent with one of the assumptions of the previous cross-sectional studies. As Kleck (1979) pointed out, the assumption that one area’s legal sanctions affect the behavior of residents in that area is highly suspect in any modern society due to national communication media. Our coding process may indirectly reflect that one area’s residents could be influenced by the legal sanctions of neighboring areas.
69 days immediately preceding and following a given execution. To be more precise, the 14 preceding days are denoted as E-14, E-13, E-12, …., E-3, E-2, E-1, where the “E-14” variable represents the number of television stories about executions on the 14 days before an execution occurred within the same state, and the “E-1” variable represents the number of television stories about executions on one day before an execution occurred in that state; the execution day is denoted as E, where the “E” variable represents the number of television stories about executions on that day j in that state i. The 14 following days are denoted as E+1, E+2, E+3, …, E+12, E+13, E+14, where the “E+1” variable represents the number of television stories aired about executions the day after an execution took place in that state, and the “E+14” variable represents the number of television stories about executions 14 days after an execution took place in that state. Therefore, there are 29 daily television coverage of executions variables, including the 14 preceding-day variables, the execution date variable, and the 14 following days. The process of coding this variable was slightly different from that of coding the newspaper coverage of executions variable because the measure addresses of stories broadcast the three national television networks, ABC, CBS, and NBC. Like the coding in national newspapers, network news stories aired about executions were counted for all 50 states and the District of Columbia on the same days. The present study counted as one the similar news stories that were repeatedly broadcasted by the same television network, to avoid double counting. The Presence or Absence of the Legal Status of the Death Penalty Finally, the active death penalty status variable refers to the legal status of the death penalty on a given day j in a given state i. It equals if a given state i had a death penalty statute active on a given day j, zero otherwise. Control Variables Daily Estimates of State Resident Population and Prison Population To identify any unique deterrent effects of executions, one must control for levels of noncapital punishment (National Academy of Sciences, 2012). While there are no national data on sentence lengths in each state, it is possible to control for the imprisonment rate, i.e. prison inmates in a given state divided by the state’s resident population. State resident populations estimates and the number of state and federal prison populations are available only a yearly basis. So, the data about the daily numbers of state residents and prisoner populations are unavailable. Accordingly, the linear interpolation method
70 was used to estimate the population on any given day. Total resident populations of each state denotes a daily estimate of the total resident and civilian population in each state between January 1, 1979 and December 31, 1998.33 Total state and federal prison populations denotes an estimate of the total number of prisoners under the jurisdiction of state and federal correction facilities in each state, for each day between January 1, 1979 and December 31, 1998.34 Temporal Control Variables Homicides are more common on weekends and during the summer, and some states always carry out executions on a particular day of the week. Therefore, temporal variables should be controlled to accurately assess the deterrent effect of executions on homicides. In the present study, temporal control variables include (1) day-of-the-week dummies, (2) monthly dummies, (3) yearly dummies, and (4) national holiday dummies. For all temporal control variables used in the present study, a continuous variable needs to be transformed into a categorical variable. To code categorical variables and include these variables in the regression
33 The following example will illustrate how linear interpolation is used to yield an estimate of total resident populations of a state on any one day. Suppose one wanted to estimate the population of Florida for August 1, 1989, but all one knew was that the estimated population was 12,800,000 on July 1, 1989 and was 12,938,000 on July 1, 1990 (the annual estimates for the two “bracketing” dates – the ones just before and after the date one is trying to estimate, which it is called the “target date”). The steps for estimating state population numbers are undertaken as follows: (1) Determine the fraction of a year that the target date was after the earlier of the two bracketing years. August 1 is 31 days after July 1, and there are 365 days in a year. Therefore, the target date, August 1, 1989, is 31 ÷ 365th (0.0849) of a year after July 1, 1989; (2) subtract the 1989 estimated population from the 1990 population; 12,938,000 – 12,800,000 = 138,000 (In states with declining populations, this quantity will be negative.); (3) multiply the fraction of a year obtained in step (1) times the quantity obtained in step (2): 0.0849 × 138,000 = 11,721; and, (4) add the quantity obtained in step (3) (which will sometimes be negative) to the estimated population for the earlier of the two bracketing years: 11,271 + 12,800,000 = 12,811,271. Therefore, this is the estimated population of Florida on August 1, 1989, obtained via linear interpolation. 34 Total prison populations of a state were estimated in accordance with the above steps of estimating state resident populations. Suppose one wanted to estimate the prison population of Florida for August 1, 1989, but all one knew was that the estimated population was 34,327 on December 31, 1988 and was 39,566 on December 31, 1989 (the annual estimates for the two “bracketing” dates – the ones just before and after the date one is trying to estimate, which it is called the “target date”). The steps for estimating state prison population numbers are undertaken as follows: (1) Determine the fraction of a year that the target date was after the earlier of the two bracketing years. August 1 is 214 days after December 31, 1988, and there are 365 days in a year. Therefore, the target date, August 1, 1989, is 214 ÷ 365th (0.58630137) of seven months after December 31, 1988; (2) subtract the 1988 estimated population from the 1989 population: 39,566 – 34,327 = 5,239 (In states with declining populations, this quantity will be negative.); (3) multiply the fraction of a year obtained in step (1) times the quantity obtained in step (2): 0.58630137 × 5,239 = 3,071.63; and, (4) add the quantity obtained in step (3) (which will sometimes be negative) to the estimated population for the earlier of the two bracketing years: 3,071.63 + 34,327 = 37,398.63. Therefore, this is the estimated prison population of Florida on August 1, 1989, obtained via linear interpolation.
71 equation, one of the categorical variables must be omitted from the analysis to avoid perfect multicollinearity (Lewis-Beck, 1980). The daily binary variables and the public holiday dummies were included to control for well-known day-of-the-week effects exhibited by homicide data (Grogger, 1990; Phillips and Hensley, 1994; Stack, 1995). This research involved creating six binary variables, one for each of six days of the week, omitting one in order to avoid perfect multicollinearity. Monday was designated as the omitted day category because both homicides and executions are the lowest on Mondays. The national holiday dummies include holiday dummies for New Year’s Day, Washington’s Birthday, Lincoln’s Birthday, Good Friday, Easter, Memorial Day, Independence Day, Labor Day, Thanksgiving, and Christmas. A dummy variable was coded to indicate the presence or absence of each of these holidays. For example, any day falling on any of the national holidays was coded “1” and all other days were coded “0.” In addition, an early study by Phillips and Hensley (1984) indicated that in many cases, national holidays extend several days, e.g. a “holiday weekend.” Some national holidays are scheduled next to Saturdays or Sundays. Consequently, a separate one-day lagged holiday variable was constructed for each of the ten holidays: any day falling one day after the holiday was coded “1” and all other days were coded “0.” The monthly binary variables were included to control for seasonal variation reported in some previous death penalty studies (i.e., Bowers and Pierce, 1980; Grogger, 1990; McFarland, 1983). Homicides are the highest in summer and lowest in winter. Twelve monthly binary variables were created for the regression equation and one of the monthly binary variables, the January dummy variable, was omitted to avoid perfect multicollinearity. Year binary variables were included to account for the longer-term historical trends in homicide over time (Grogger, 1990; Hjalmarsson, 2009). Nineteen year binary variables were created because the time period for this study is 20 years between 1979 and 1998. For example, the 1984 year dummy variable was created when any year falling on 1984 was coded “1” and all other years were coded “0.” In order to avoid multicollinearity, one of the 20 year dummy variables, the 1984 dummy variable, was arbitrarily omitted from the analysis.
72 Geographic Control Variables A variety of state characteristics can affect homicide rates. Many scholars have pointed out that state-level homicide rates may be correlated with such factors as the percentage of population between 18-24 years old, the percentage of population that is African American, the unemployment rate, economic inequality, the role of weapons used, drug markets, and relevant law enforcement policies (Blumstein and Rosenfeld, 1998; Kovandzic, Vieraitis, and Yeisley, 1998). Watt and Lee (2007) found that a state’s homicide rates and trends are causally influenced by the percentage of the state’s population that is African American, the percentage of the state’s population that obtain more than at least a high school degree, and states with one of the largest cities in the US (Watt and Lee, 2007). To accommodate the effect of these control variables, many previous death penalty studies have included a variety of these control variables or proxy variables into the equation model (i.e., Dezhbakhsh and Shepherd, 2006; Ehrlich, 1975; Mocan and Gittings, 2003). However, the present research may be limited because the data about these variables are available only on an annual or monthly basis. Therefore, we instead used a set of state dummy variables that serve to control for variation in homicides due to observed and unobserved different factors across states. Accordingly, this study created 50 state (including the District of Columbia) categorical variables for the regression analysis. In order to avoid perfect multicollinearity, one of the 50 state categorical variables, California, was arbitrarily omitted. Research Hypotheses The following are the key hypotheses to be tested in the current study. These hypotheses are linked to three distinctive inquiries. Hypothesis 1 concerns the deterrent effect of execution on homicides, while hypothesis 2 addresses the deterrent effect of publicized execution on homicides. Finally, hypothesis 3 concerns the sensitivity of the original results.
H1. Executions have the deterrent effects on homicides on a given day in a given state. H2. Publicized executions have the deterrent effects on homicide on a given day in a given state. H3. The results of the hypotheses 1 and 2 remain consistent under temporal, geographical, deterrence, and social conditions.
73 Estimation Models We used count regression methods, including Poisson regression and Negative Binomial regression, instead of ordinary least squares regression because the dependent variable is a count of homicides. The number of daily homicides for the 50 states and the District of Columbia over twenty years takes on only the non-negative integer values (0, 1, 2, 3, …., +∞) and takes on a positively skewed, nonnormal distribution. Therefore, the traditional Ordinary Least Squares (OLS) regression model is not an appropriate estimator. The OLS regression model might be adequate if the positively skewed dependent variable were log transformed, but a log transformation leads to the loss of data because the natural logarithm is defined only when x is greater than zero (x>0). As a result, the very large number of zeros contained in our dataset would be lost from the analysis. In count regression models, the Maximum Likelihood Estimator (MLE) is designed to estimate a count data model. Consistent parameters are estimated through an MLE procedure that has a number of desirable properties, including an asymptotic distribution, consistency, and efficiency (Fienberg 1984). Further, the Poisson coefficient divided by its standard error follows a standard t-distribution. Therefore, statistical significance as well as the direction of the effect of each independent variable can be assessed. The two best-known count regression models, the Poisson regression model and the Negative Binomial regression model, are identical with one important exception. While the Poisson regression model assumes that the mean and variance of the errors are equal, the Negative Binomial regression model assumes that the conditional mean and variances of the errors are not equal (Grogger, 1990). Overdispersion occurs when the variance of the errors is greater than the conditional mean. This may happen because there is unobserved state heterogeneity or an excessive number of zero observations in the count data, as when daily homicide counts are distributed in a positively skewed manner. To solve out the overdispersion issue, a distribution that allows each state’s Poisson parameter to have its own random distribution more than the Poisson regression model should be the alternative. Several methods of testing for overdispersion include regression-based tests, the Wald test, and the LR test (Long, 1997). When the variance of the errors is greater than the conditional, the Negative Binomial regression model is more appropriate to estimate the equation model than the Poisson regression model.
74 Because the present research employed panel data, it is necessary to compare the fixed- effect with the random-effect models. The Hausman test (Hausman and McFadden, 1984) was used to estimate the fixed- and random-effect models and decide which model, the fixed-effects or random-effect models. The Hausman test is based on the estimates of the Negative Binomial regression model and has two hypotheses. While the null hypothesis assumes that the random- effect model is more appropriate, the alternative hypothesis assumes that the fixed-effect model is more suitable. In order to conduct the overdispersion test, the Hausman test, the descriptive statistics, and the most appropriate count regression model, the present study employs version 14 of the STATA statistical software.
75 CHAPTER 5
FINDINGS
This chapter summarizes and integrates the results of this research project on the short- term deterrent effect of executions on homicides. Trends in Daily News Coverage of Executions One way that prospective murderers can become aware of the probability of being executed is for them to be exposed to information about recent and upcoming executions. This leads some to suggest that the deterrent effect is produced by frequent reminders of executions. Although any possible information outlet could allow prospective killers to perceive the threat of execution, the greatest volume of information is likely to come through the print and television news media. News stories about executions remind prospective killers that they could be punished by death for committing murder, which could result in a deterrent effect. Therefore, the deterrent effect should be strongest when newspaper and television stories about executions are published and broadcast most frequently. Figure 1 represents the number of national and state newspaper stories about executions per day for with the 14 calendar days immediately preceding and following an execution (Execution Day, denoted as “E”). As the chart shows, the number of news stories covered by the mass media increases prior to the execution day, reaches its peak one day after the execution day (E+1), and decreases substantially over the remaining days after the execution. For example, the largest number of newspaper stories about executions was 27,981 one day after the execution took place (E+1) and, the second highest was 16,235 on the execution date (E), followed by 5,705 one day before the execution day (E-1), 5,485 two days after the execution day (E+2), 2,901 two days before the execution day (E-2), and so on. Thus, the deterrent effect should manifest itself most strongly one day after the execution date (E) because the largest number of news stories about executions were printed by national and state newspapers on this day. The next strongest effect should be the day of the execution itself.
76 Newspaper Story Frequency Relative to Execution Days 30000 27981
25000
20000 16235
Number 15000 of Newspaper 10000 5705 5485 Stories 1463 1590 1482 5000 10721025 1366 384645 6051063764 393 173234 333 29011861 243124230165164216 7 59 0
Figure 1. Number of In-State35 Newspaper Stories about Executions
The national and state newspaper coverage of in-state executions is comparable to national television network coverage of in-state executions in some ways. Figure 2 shows a similar trend in the number of national television network stories covering in-state executions in the 29-day period surrounding an execution, with a sharp peak, in the middle and a steep decline after the execution day. These data cover only national network stories about executions. National television networks do not cover every execution. They broadcast stories about a narrow range of specific newsworthy executions that are interesting to a television audience. For example, national evening news networks may broadcast stories about the first execution in a state after the moratorium era, or about the executions of murderers involved in the most violent or shocking crimes. As with print news, the number of news stories covered by national evening television networks increased prior to the execution date and then decreased significantly. But, unlike print news, the largest number of news stories broadcast by evening news programs reached its peak on the execution date rather than the day after. For example, the largest number of network
35 Including stories in national newspapers, which reach all states.
77 television stories about executions was 99 on the execution day (E) and the second largest was 53 one day before (E-1), followed by 17 two days before the execution date (E-2), 13 one day after the execution date (E+1), and so on. Compared to print news, the deterrent effects would be the strongest on the given execution date (E) because the largest number of news stories about executions were broadcast by national television on the day of the execution.
Figure 2. Number of National Television Stories about Executions
Because the dependent variable in this study, the daily number of homicides, is count data, this study requires the researchers to decide whether a Poisson regression model is more appropriate than a negative binomial regression model or vice versa. Thus, to determine the most appropriate statistical analysis, this study conducts a series of statistical analyses: histogram and overdispersion test. Figure 3 is a histogram that pictorially demonstrates the skewness of the daily homicide count variable. The distribution in Figure 3 is positively skewed, as it has scores clustered to the left, with the tail extending to the right.
78 .3 .2 Density .1 0
0 50 100 150 200 THE NUMBER OF HOMICIDES ON THE GIVEN DAY IN THE GIVEN STATE
Figure 3. Histogram
Table 1 reports summary and overdispersion analysis for a count dependent variable. The variance (4.470106) is almost four times larger than the mean (1.195582). The mean of the Poisson distribution is equal to its variance, whereas the variance of the Negative Binomial distribution is not identical to its mean (Long and Freese, 2005). This summary statistics suggests that the Negative Binomial regression model is more appropriate than the Poisson model. Table 1. Overdispersion Test Std. Dependent Variable N Mean Variance Skewness Kurtosis Deviation The number of homicides in the same 372,555 1.195582 2.114263 4.470106 4.579158 125.1974 state on the execution day
79 Table 3 displays the summary statistics of homicide and execution data in the United States between January 1, 1979 and December 31, 1998. The second column reports the year, month, and day-of-week variations in homicide data. Over the sample period, 445,220 homicides were reported in the United States.36
36 For reference purpose, comparative homicide information is derived from the Federal Bureau of Investigation’s (FBI’)s annual Uniform Crime Reports (UCRs) of murder and nonnegligent manslaughter (http://www.ucrdatatool.gov/). The FBI data reports 424,076 homicides over the same period. Because the vital statistics system counts justifiable homicides, while the UCR system does not, the number of homicide in the data used this study is slightly higher than the estimated number of homicides in the FBI’s UCR data. Although the numbers in two data sources are different, they show the same general trend (See Figure 4).
Table 2. Comparative Counts of Mortality Detail File Data and Federal Bureau of Investigation Data: 1979-1998 Time Period Mortality Detail File Data Used in This Study FBI’s UCR Data Differences Year 1979 22,227 21,460 767 1980 24,010 23,040 970 1981 23,431 22,520 911 1982 22,140 21,010 1,130 1983 19,987 19,308 679 1984 19,582 18,692 890 1985 19,705 18,976 729 1986 21,538 20,613 925 1987 20,877 20,096 781 1988 21,859 20,675 1,184 1989 22,637 21,500 1,137 1990 24,685 23,438 1,247 1991 26,348 24,703 1,645 1992 25,215 23,760 1,455 1993 25,716 24,526 1,190 1994 24,634 23,326 1,308 1995 22,632 21,606 1,026 1996 20,711 19,645 1,066 1997 19,550 18,208 1,342 1998 17,936 16,974 962 Total 445,420 424,076 21,344
80 Annual variations exist in the occurrence of homicide in the United States, ranging from a low of 17,936 homicides in 1998 to a high of 26,348 in 1991. The number of homicides increased in the 1980s, reached a peak of 26,348 in 1991, and then decreased substantially thereafter. Evidence supports the conventional argument that violent crimes, such as homicide, take place in seasonal cycles. Table 3 shows that homicides occur most often in the summer months of July, August, and September, and least often during the early spring months of February, March, and April. In addition, homicides occur more on weekends than weekdays most commonly on Saturday, followed by Sunday and Friday. The third column of Table 3 provides summary statistics of the execution data. Between January 1, 1979 and December 31, 1998, 499 executions took place in the United States. A fair amount of annual variation is seen in the number of the executions over the sample period.37 The number of executions began to increase between the 1980s and the early 1990s, rose sharply from 1992 until 1996, and reached a peak of seventy-four in 1997. The number decreased in 1998 but was the second highest during the period studied.
30,000 27,500 25,000 22,500 Annual 20,000 Number of 17,500 Homicides 15,000 12,500 10,000 7,500 5,000 2,500 0 197980 81 82 83 84 85 86 87 88 89 90 91 92 93 94 95 96 97 98 Year Figure 4. Comparativ Analysis of Homicide Trends in the United States, 1979-1998
Mortality Detail Files Federal Bureau of Investigation (FBI)
37 For reference purposes, see the figures published by the Death Penalty Information Center (http://www.deathpenaltyinfo.org/documents/FactSheet.pdf).
81 The number of executions varied by month, ranging from 23 (4.61%) in February to 61 (12.22%) in May. The number of executions is slightly higher in May (12.22%) and June (10.54%), with the fewest occurring during February (4.6%), October (5.21%), and November (6.81%). In addition, there is substantial day-of-week variation, with executions most frequent on weekdays and lower on weekends: 98% of executions occur on Monday through Friday, with a peak on Wednesdays (146 executions, or 29.26%), followed by Fridays (106 executions, or 21.24%), and Tuesdays (105 executions, or 21.04%). Unlike previous studies reporting that executions occurred only on weekdays (Grogger, 1990; Hjalmarsson, 2009), this study reports that two percent of executions occurred on Saturdays (1.20%) and Sundays (0.80%). Table 3. Summary of Counts of Homicide and Execution Data: 1979-1998 Time Period Number of Homicides Number of Executions Year 1979 22,227 (4.99%) 2 (0.40%) 1980 24,010 (5.39%) 0 (0.00%) 1981 23,431 (5.26%) 1 (0.20%) 1982 22,140 (4.97%) 2 (0.40%) 1983 19,987 (4.49%) 5 (1.00%) 1984 19,582 (4.40%) 21 (4.21%) 1985 19,705 (4.42%) 18 (3.61%) 1986 21,538 (4.84%) 18 (3.61%) 1987 20,877 (4.69%) 25 (5.01%) 1988 21,859 (4.91%) 11 (2.20%) 1989 22,637 (5.08%) 16 (3.21%) 1990 24,685 (5.54%) 23 (4.61%) 1991 26,348 (5.92%) 14 (2.81%) 1992 25,215 (5.66%) 31 (6.21%) 1993 25,716 (5.77%) 38 (7.62%) 1994 24,634 (5.53%) 31 (6.21%) 1995 22,632 (5.08%) 56 (11.22%) 1996 20,711 (4.65%) 45 (9.02%) 1997 19,550 (4.39%) 74 (14.83%) 1998 17,936 (4.03%) 68 (13.63%) Total 445,420 (100.00%) 499 (100.00%) Month January 37,361 (8.39%) 40 (8.02%) February 33,382 (7.49%) 23 (4.61%) March 36,048 (8.09%) 44 (8.82%) April 34,820 (7.82%) 42 (8.42%) May 36,441 (8.18%) 61 (12.22%) June 36,717 (8.24%) 52 (10.42%) July 40,245 (9.04%) 42 (8.42%) August 40,897 (9.18%) 46 (9.22%) September 37,935 (8.52%) 43 (8.62%) October 37,830 (8.49%) 26 (5.21%) November 36,062 (8.10%) 34 (6.81%) December 37,682 (8.46%) 46 (9.22%) Total 445,420 (100.00%) 499 (100.00%)
82 Table 3 - Continued Time Period Number of Homicides Number of Executions Day of the Week Sunday 73,664 (16.54%) 4 (0.80%) Monday 58,507 (13.14%) 43 (8.62%) Tuesday 56,695 (12.73%) 105 (21.04%) Wednesday 55,854 (12.54%) 146 (29.26%) Thursday 56,790 (12.75%) 89 (17.84%) Friday 63,423 (14.24%) 106 (21.24%) Saturday 80,487 (18.07%) 6 (1.20%) Total 445,420 (100.00%) 499 (100.00%)
Table 4 summarizes the descriptive statistics of the dependent variable, the main independent variables of interest, and a list of other independent variables. The average daily number of homicides was 1.195582 per state between January 1, 1979 and December 31, 1998. All 29 execution dummy variables have the same value 0.0013126, because these variables are dichotomous, and lags and leads of the original execution dummy variable. The 29 dummy variable has a higher mean of 0.0299526 than any of the 29 execution dummy variables because all 29 individual execution dummy variables are coded into one dummy variable. The newspaper and television coverage variables have different values because these variables are numerical: the number of reported news stories about recent and upcoming executions. The newspaper variables range from 0.0000188 thirteen days following executions (E-13) to 0.0751057 one day after executions (E-1). The summary statistics indicate that the highest mean of the newspaper variable is 0.0751057 one day after an execution (E-1), followed by 0.0435775 on the day of the execution (E), 0.0153132 one day before the execution (E+1), and so on. This implies that newspapers tend to produce more news stories about executions as the execution day approaches. Because news stories about executions are routinely broadcast by national evening television news programs for just a few days surrounding an execution, some television variables on days long before or after executions have a value of zero. Only six days preceding and three days following an execution have non-zero values. Unlike the publication pattern of newspapers, the highest mean of individual television variables is 0.0135524 on the day of an execution (E), followed by 0.0072553 one day before the execution (E-1), 0.0023272 two days before the execution (E-2), 0.0017796 one day after the execution (E+1), and so on. Because the present study employs a large set of temporal control variables, including year, month, day-of-week, and national holidays, a series of patterns, so-called periodicity, would have repeated themselves over time. For example, one set of yearly dummy variables
83 among 20 yearly variables from 1979 to 1998 has a mean of 0.0499658, whereas the other set has a mean of 0.0501027. The descriptive statistics shows that the temporal pattern repeats every four years during the sample period. This is because the leap year repeats every four years (1980, 1984, 1988, 1992, 1996, etc.). The 12 monthly dummy variables have different means, 0.0848734, 0.0773443, or 0.0821355, depending on the total number of days in the month (31, 28, or 30, respectively). This implies that the months with larger days during the sample period tend to have higher mean values than any months with smaller days. In other words, months with more days have higher mean values than months with fewer days. The seven day-of-week variables have two types of mean values, 0.1427789 (Fridays, Saturdays, and Sundays) and 0.1429158 (Mondays through Thursdays). Like the month dummy variables, the total number of Mondays, Tuesdays, Wednesdays, and Thursdays during the sample period is larger than the total number of Fridays, Saturdays, and Sundays. In contrast, national public holiday variables and their lagged holiday variables have the same mean values of 0.0027379. Although the total number of sample cases for national public holiday variables is 372,555, the total number of sample cases for lagged national public holiday variables is 372,554. This occurred because the statistical analytical package used in the present study, STATA, automatically removed missing values from the analysis. The present study employs a set of state resident and prison populations. For example, the estimated average mean resident population in each state was 4,838,512 and the estimated average mean prison population in each state was approximately 12,220. Based on these numbers, the state prison population rates were estimated. The estimated average state prison rate was 242.055, indicating that there were approximately 242 prisoners in state prisons for every 1,000,000 state residents. The active death penalty statute variable has a mean of 0.7115996 during the sample period, meaning that death penalty statutes were in effect for more than 71 % of the total number of state-days (372,555) during the study period. In addition, the present study includes a list of 50 states and the District of Columbia and all state dummy variables have a mean of 0.0196078, respectively.
84 Table 4. Descriptive Statistics Variables Observations Mean Std. Deviation Minimum Maximum Dependent Variable Daily Count of Homicide 372,555 1.195582 2.114263 0 165 Independent Variables of Interest E-14 372,541 0.0013126 0.0362062 0 1 E-13 372,542 0.0013126 0.0362061 0 1 E-12 372,543 0.0013126 0.0362061 0 1 E-11 372,544 0.0013126 0.0362060 0 1 E-10 372,545 0.0013126 0.0362060 0 1 E-9 372,546 0.0013126 0.0362059 0 1 E-8 372,547 0.0013126 0.0362059 0 1 E-7 372,548 0.0013126 0.0362058 0 1 E-6 372,549 0.0013126 0.0362058 0 1 E-5 372,550 0.0013126 0.0362057 0 1 E-4 372,551 0.0013126 0.0362057 0 1 E-3 372,552 0.0013126 0.0362057 0 1 E-2 372,553 0.0013126 0.0362056 0 1 E-1 372,554 0.0013126 0.0362056 0 1 Execution Day 372,555 0.0013126 0.0362055 0 1 E+1 372,554 0.0013126 0.0362056 0 1 E+2 372,553 0.0013126 0.0362056 0 1 E+3 372,552 0.0013126 0.0362057 0 1 E+4 372,551 0.0013126 0.0362057 0 1 E+5 372,550 0.0013126 0.0362057 0 1 E+6 372,549 0.0013126 0.0362058 0 1 E+7 372,548 0.0013126 0.0362058 0 1 E+8 372,547 0.0013126 0.0362059 0 1 E+9 372,546 0.0013126 0.0362059 0 1 E+10 372,545 0.0013126 0.0362060 0 1 E+11 372,544 0.0013126 0.0362060 0 1 E+12 372,543 0.0013126 0.0362061 0 1 E+13 372,542 0.0013126 0.0362061 0 1 E+14 372,541 0.0013126 0.0362062 0 1 29 Day Dummy 372,555 0.0299526 0.1704569 0 1 Newspaper_E-14 372,555 0.0004644 0.0221583 0 3 Newspaper_E-13 372,555 0.0006281 0.0271122 0 5 Newspaper_E-12 372,555 0.0010307 0.0340368 0 6 Newspaper_E-11 372,555 0.0017313 0.051806 0 4 Newspaper_E-10 372,555 0.0008938 0.0305938 0 3 Newspaper_E-9 372,555 0.0016239 0.0488221 0 8 Newspaper_E-8 372,555 0.0028533 0.061169 0 2 Newspaper_E-7 372,555 0.0020507 0.0527952 0 5 Newspaper_E-6 372,555 0.0036666 0.0743417 0 6 Newspaper_E-5 372,555 0.0039269 0.0712116 0 6 Newspaper_E-4 372,555 0.0042678 0.0922028 0 7 Newspaper_E-3 372,555 0.0039779 0.0770911 0 5 Newspaper_E-2 372,555 0.0077868 0.1092717 0 8 Newspaper_E-1 372,555 0.0153132 0.1715938 0 15 Newspaper_Execution Day 372,555 0.0435775 0.2973563 0 18 Newspaper_E+1 372,555 0.0751057 0.4364567 0 28 Newspaper_E+2 372,555 0.0147227 0.1611606 0 11 Newspaper_E+3 372,555 0.0049952 0.0862539 0 7
85 Table 4 - Continued Variables Observations Mean Std. Deviation Minimum Maximum Newspaper_E+4 372,555 0.0028774 0.0643541 0 5 Newspaper_E+5 372,555 0.0028513 0.0730522 0 5 Newspaper_E+6 372,555 0.0010549 0.0331976 0 3 Newspaper_E+7 372,555 0.0006523 0.0260513 0 2 Newspaper_E+8 372,555 0.0003328 0.0182408 0 1 Newspaper_E+9 372,555 0.0006174 0.0251612 0 2 Newspaper_E+10 372,555 0.0004429 0.0211675 0 2 Newspaper_E+11 372,555 0.0004402 0.0209764 0 1 Newspaper_E+12 372,555 0.0005798 0.0241829 0 2 Newspaper_E+13 372,555 0.0000188 0.0043346 0 1 Newspaper_E+14 372,555 0.0001584 0.0125834 0 1 Television_E-14 372,555 0 0 0 0 Television_E-13 372,555 0 0 0 0 Television_E-12 372,555 0 0 0 0 Television_E-11 372,555 0 0 0 0 Television_E-10 372,555 0 0 0 0 Television_E-9 372,555 0 0 0 0 Television_E-8 372,555 0 0 0 0 Television_E-7 372,555 0 0 0 0 Television_E-6 372,555 0.0002738 0.0233986 0 2 Television_E-5 372,555 0.0004107 0.026159 0 2 Television_E-4 372,555 0.0001369 0.0116993 0 1 Television_E-3 372,555 0.0008214 0.0369899 0 2 Television_E-2 372,555 0.0023272 0.0691797 0 4 Television_E-1 372,555 0.0072553 0.1387417 0 6 Television_Execution Day 372,555 0.0135524 0.1826338 0 6 Television_E+1 372,555 0.0017796 0.0535872 0 2 Television_E+2 372,555 0.0002738 0.0165442 0 1 Television_E+3 372,555 0.0006845 0.0350937 0 2 Television_E+4 372,555 0 0 0 0 Television_E+5 372,555 0 0 0 0 Television_E+6 372,555 0 0 0 0 Television_E+7 372,555 0 0 0 0 Television_E+8 372,555 0 0 0 0 Television_E+9 372,555 0 0 0 0 Television_E+10 372,555 0 0 0 0 Television_E+11 372,555 0 0 0 0 Television_E+12 372,555 0 0 0 0 Television_E+13 372,555 0 0 0 0 Television_E+14 372,555 0 0 0 0 Demographic Variable State Resident Population 372,555 4838512 5277340 401851 3.29e+07 Non-Capital Punishment Variables State Prison Population (Number) 372,555 12220.56 18268.71 249 159563 State Prison Population Rates 372,555 242.055 191.2088 29.34652 1916.652 Active Death Penalty Statutes 372,555 0.7115996 0.4530189 0 1 Temporal Control Variables Sunday Dummy 372,555 0.1427789 0.3498477 0 1 Monday Dummy 372,555 0.1429158 0.3499874 0 1 Tuesday Dummy 372,555 0.1429158 0.3499874 0 1 Wednesday Dummy 372,555 0.1429158 0.3499874 0 1
86 Table 4 - Continued Variables Observations Mean Std. Deviation Minimum Maximum Thursday Dummy 372,555 0.1429158 0.3499874 0 1 Friday Dummy 372,555 0.1427789 0.3498477 0 1 Saturday Dummy 372,555 0.1427789 0.3498477 0 1 January Dummy 372,555 0.0848734 0.2786935 0 1 February Dummy 372,555 0.0773443 0.2671373 0 1 March Dummy 372,555 0.0848734 0.2786935 0 1 April Dummy 372,555 0.0821355 0.2745715 0 1 May Dummy 372,555 0.0848734 0.2786935 0 1 June Dummy 372,555 0.0821355 0.2745715 0 1 July Dummy 372,555 0.0848734 0.2786935 0 1 August Dummy 372,555 0.0848734 0.2786935 0 1 September Dummy 372,555 0.0821355 0.2745715 0 1 October Dummy 372,555 0.0848734 0.2786935 0 1 November Dummy 372,555 0.0821355 0.2745715 0 1 December Dummy 372,555 0.0848734 0.2786935 0 1 Year Dummy-1979 372,555 0.0499658 0.2178746 0 1 Year Dummy-1980 372,555 0.0501027 0.2181571 0 1 Year Dummy-1981 372,555 0.0499658 0.2178746 0 1 Year Dummy-1982 372,555 0.0499658 0.2178746 0 1 Year Dummy-1983 372,555 0.0499658 0.2178746 0 1 Year Dummy-1984 372,555 0.0501027 0.2181571 0 1 Year Dummy-1985 372,555 0.0499658 0.2178746 0 1 Year Dummy-1986 372,555 0.0499658 0.2178746 0 1 Year Dummy-1987 372,555 0.0499658 0.2178746 0 1 Year Dummy-1988 372,555 0.0501027 0.2181571 0 1 Year Dummy-1989 372,555 0.0499658 0.2178746 0 1 Year Dummy-1990 372,555 0.0499658 0.2178746 0 1 Year Dummy-1991 372,555 0.0499658 0.2178746 0 1 Year Dummy-1992 372,555 0.0501027 0.2181571 0 1 Year Dummy-1993 372,555 0.0499658 0.2178746 0 1 Year Dummy-1994 372,555 0.0499658 0.2178746 0 1 Year Dummy-1995 372,555 0.0499658 0.2178746 0 1 Year Dummy-1996 372,555 0.0501027 0.2181571 0 1 Year Dummy-1997 372,555 0.0499658 0.2178746 0 1 Year Dummy-1998 372,555 0.0499658 0.2178746 0 1 New Year Dummy 372,555 0.0027379 0.0522529 0 1 New Year Lag 372,554 0.0027379 0.0522529 0 1 Good Friday 372,555 0.0027379 0.0522529 0 1 Good Friday Lag 372,554 0.0027379 0.0522529 0 1 Easter 372,555 0.0027379 0.0522529 0 1 Easter Lag 372,554 0.0027379 0.0522529 0 1 Memorial Day 372,555 0.0027379 0.0522529 0 1 Memorial Day Lag 372,554 0.0027379 0.0522529 0 1 Thanksgiving Day 372,555 0.0027379 0.0522529 0 1 Thanksgiving Day Lag 372,554 0.0027379 0.0522529 0 1 Christmas Day 372,555 0.0027379 0.0522529 0 1 Christmas Day Lag 372,554 0.0027379 0.0522529 0 1 Geographical Control Variables Alabama 372,555 0.0196078 0.1386486 0 1 Alaska 372,555 0.0196078 0.1386486 0 1
87 Table 4 - Continued Variables Observations Mean Std. Deviation Minimum Maximum Arizona 372,555 0.0196078 0.1386486 0 1 Arkansas 372,555 0.0196078 0.1386486 0 1 California 372,555 0.0196078 0.1386486 0 1 Colorado 372,555 0.0196078 0.1386486 0 1 Connecticut 372,555 0.0196078 0.1386486 0 1 Delaware 372,555 0.0196078 0.1386486 0 1 Washington DC 372,555 0.0196078 0.1386486 0 1 Florida 372,555 0.0196078 0.1386486 0 1 Georgia 372,555 0.0196078 0.1386486 0 1 Hawaii 372,555 0.0196078 0.1386486 0 1 Idaho 372,555 0.0196078 0.1386486 0 1 Illinois 372,555 0.0196078 0.1386486 0 1 Indiana 372,555 0.0196078 0.1386486 0 1 Iowa 372,555 0.0196078 0.1386486 0 1 Kansas 372,555 0.0196078 0.1386486 0 1 Kentucky 372,555 0.0196078 0.1386486 0 1 Louisiana 372,555 0.0196078 0.1386486 0 1 Maine 372,555 0.0196078 0.1386486 0 1 Maryland 372,555 0.0196078 0.1386486 0 1 Massachusetts 372,555 0.0196078 0.1386486 0 1 Michigan 372,555 0.0196078 0.1386486 0 1 Minnesota 372,555 0.0196078 0.1386486 0 1 Mississippi 372,555 0.0196078 0.1386486 0 1 Missouri 372,555 0.0196078 0.1386486 0 1 Montana 372,555 0.0196078 0.1386486 0 1 Nebraska 372,555 0.0196078 0.1386486 0 1 Nevada 372,555 0.0196078 0.1386486 0 1 New Hampshire 372,555 0.0196078 0.1386486 0 1 New Jersey 372,555 0.0196078 0.1386486 0 1 New Mexico 372,555 0.0196078 0.1386486 0 1 New York 372,555 0.0196078 0.1386486 0 1 North Carolina 372,555 0.0196078 0.1386486 0 1 North Dakota 372,555 0.0196078 0.1386486 0 1 Ohio 372,555 0.0196078 0.1386486 0 1 Oklahoma 372,555 0.0196078 0.1386486 0 1 Oregon 372,555 0.0196078 0.1386486 0 1 Pennsylvania 372,555 0.0196078 0.1386486 0 1 Rhode Island 372,555 0.0196078 0.1386486 0 1 South Carolina 372,555 0.0196078 0.1386486 0 1 South Dakota 372,555 0.0196078 0.1386486 0 1 Tennessee 372,555 0.0196078 0.1386486 0 1 Texas 372,555 0.0196078 0.1386486 0 1 Utah 372,555 0.0196078 0.1386486 0 1 Vermont 372,555 0.0196078 0.1386486 0 1 Virginia 372,555 0.0196078 0.1386486 0 1 Washington 372,555 0.0196078 0.1386486 0 1 West Virginia 372,555 0.0196078 0.1386486 0 1 Wisconsin 372,555 0.0196078 0.1386486 0 1 Wyoming 372,555 0.0196078 0.1386486 0 1
88 Table 5 is a list of the seven most extreme homicide events on a single day during the study period. The Oklahoma City bombing resulted in 165 homicide casualties on April 9, 1995. The Happy Land fire resulted in 97 homicide deaths on March 23, 1990; the crash of Pacific Southwest Flight 1771 caused 51 homicide deaths on December 7, 1987; and, 32 homicide deaths resulted from the Los Angeles riot on April 30, 1992. However, there are no records on the causes of 32 homicide deaths on September 9, 1990 and 30 homicide deaths on January 1, 1980. Table 5. The Extreme Homicide Counts for State-Days between January 1, 1979 and December 31, 1998 Rank Extreme Homicide Cases Homicide Date State Notes 1 16538 April 19, 1995 Oklahoma Oklahoma City Bombing 2 97 March 25, 1990 New York Happy Land Fire 3 51 December 7, 1987 California David Augustus Burke, 32, caused the crash of Pacific Southwest Airlines flight 1771. 4 32 April 30, 1992 California Los Angeles Riot 32 September 9, 1990 California Resources are not available. 5 31 December 4, 1980 New York Luis Marin who was convicted in Westchester County, New York, of 26 counts of murder arising from a fire at a Stouffer’s Inn in Harrison, New York 6 30 January 1, 1980 California Resources are not available.
Multivariate Statistics We now come to our main results – multivariate estimates of the effects of executions on daily state homicide counts. Before discussing our main conclusions concerning deterrent effects of executions, we summarize results concerning the control variables. Total State Resident Population Variable One demographic variable, the total resident populations of each state, is included in the analysis. The coefficient of the total resident populations of each state variable (6.50e-08, or 0.0000000650) is statistically significant at the 0.01 level. This represents a very weak
38The annual Mortality Detail Files used in this dissertation indicate that the 165 homicides occurred as a result of the bombing of the Alfred P. Murrah Federal Building in Oklahoma City on April 19, 1995. However, the FBI’s UCR statistics and other media sources reported that the 168 murder and nonnegligent homicides that occurred as a result of this bombing are included in the national estimate (Federal Bureau of Investigation, 2015).
89 relationship between total resident populations of each state and homicides in the states, suggesting that as state resident populations increase, the number of homicides increases. Geographical (State) Control Variables The estimated coefficients of almost all of the geographical control variables are statistically significant at the 0.01 level and increased in a predicted negative direction, compared to the baseline (omitted) state, California. That is, nearly all states have fewer homicides than California. In contrast, the coefficient for one state, Florida, is in the negative direction but not statistically significant at the 0.10 level. However, these estimated coefficients have no specific interpretation. The primary purpose of including state dummy variables in the negative binomial regression model is to control for state-specific characteristics which vary across states, thereby helping to isolate any short-term deterrent effect of executions on homicides. The inclusion of the state dummy variables reduces the influence of unobservable causes variation in homicides arising from state-specific characteristics that could otherwise result in biased results (Shepherd, 2005; Zimmerman, 2004). Temporal Control Variables Because prior studies have documented possible seasonal and temporal trends in homicide rates, it is important to control for seasonality and long-term temporal trends (Hjalmarsson, 2008; Grogger, 1990; Phillips and Hensley, 1984). Like the state dummy variables, inclusion of a set of the temporal dummy variables controls for unobserved variation in homicide with time-specific characteristics that affect all states. These estimated coefficients have no specific interpretation. The present study incorporates both shortest-term and longest- term temporal control variables into the negative binomial regression equation. Thus, a set of different temporal dummies (e.g. day of the week, monthly, yearly, public holidays, and lagged public holidays) were created and introduced to account for temporal patterns in homicide rates. In general, several of the temporal control variables were significantly associated with the U. S. homicide rates. For example, the homicide rate was statistically significantly higher in all of the days of the week, compared to the baseline (omitted) day, Wednesday. The homicide rate on every other day of the week was significantly higher. On Saturdays, on average, 36.73 percent more homicides occur than on Wednesdays. Compared to February (the omitted month), homicide is significantly lower in March, and significantly higher in June, July, August, September, October, and December. In August, on
90 average, 11.02 percent more homicides occur than in February. However, homicide counts in January, April, May and November are not significantly different from February. Compared to the omitted year, 1995, homicide counts were significantly higher in the years 1991, 1992, 1993, and 1994. Homicide counts were significantly lower in the years 1979, 1980, 1981, 1982, 1983, 1984, 1985, 1986, 1987, 1988, 1989, 1996, 1997, and 1998. In 1984, on average, 24.14 percent less homicides occurred than in 1995. Finally, homicide counts were significantly higher on most public holiday, except for the day after Christmas. Homicide counts are significantly lower the days after Christmas, even though they are higher on Christmas itself. This represents that the drop in homicides following Christmas is caused by severe winter weather. In contrast, Independence Day, Labor Day, and Thanksgiving Day are significantly higher both on public holidays themselves and on the days after these holidays. We now state our main results on the effects of executions on daily state homicide counts. Table 6 presents the results of a negative binomial regression analytical model in which lead and lag effects as long as two-weeks were considered. The estimated negative binomial regression unstandardized regression coefficients and the standard errors of all independent variables are reported in Table 6. The Execution Variables Most of the coefficients for the variables representing the execution day (E) and the 14 calendar days immediately preceding and following a given execution day (E-14, through E+14) are not statistically significant at the 0.05 level, despite our very large sample size (n = 372,555 state-day). Model with newspaper and television variables is very similar with the model without the newspaper and television variables. A few of these variables, however, including “E-13”, “E-4”, “E”, “E+5”, and “E+6”, we are statistically significant and in the negative direction. For example, the estimated coefficient of the “E+5” variable is - 0.0907129 at the 0.01 level and is the strongest, followed by “E” with a coefficient of - 0.0623307 at the 0.10 level, “E+6” with a coefficient of - 0.0593144 at the 0.10 level, “E-4” with a coefficient of - 0.0577106 at the 0.10 level, and “E-13” with a coefficient of - 0.0517452 at the 0.10 level. These estimated coefficients mean that there are 9.07 percent fewer homicides on the day five days after an execution in the United States (E+5); there are 6.23 percent fewer homicides on the day of the executions (E); 5.93 percent fewer homicides on the day six days after the execution (E+6); 5.77 percent fewer
91 homicides on the day four days prior to the execution (E-4); and 5.17 percent fewer homicides on the day thirteen days prior to the execution (E-13). One model without newspaper and television variables is very similar with another model with the newspaper and television variables, except for the estimated coefficient of the “E” variable. The estimated coefficient of the day of execution “E” variable in the model without news variables is marginally statistically significant at p = 0.053 and in the negative direction. In contrast, the estimated coefficient of the day of execution “E” variable in the model with news variables is statistically significant at the 0.05 level and in the negative direction. Table 6. Negative Binomial Regression Models Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors E-14 372,541 - 0.0121964 0.0315453 -0.0085785 0.0316083 E-13 372,542 - 0.0517452* 0.0310916 -0.055455* 0.0313288 E-12 372,543 - 0.0404428 0.0303157 -0.055455 0.0303914 E-11 372,544 0.0107228 0.0293182 0.0112388 0.0293764 E-10 372,545 - 0.0164697 0.0295594 -0.0163397 0.0296904 E-9 372,546 0.0096602 0.03016 0.0077143 0.0302438 E-8 372,547 0.0231316 0.0310407 0.0217385 0.0311192 E-7 372,548 0.0035433 0.0314005 0.0062864 0.0315963 E-6 372,549 0.0045427 0.0305177 0.0062864 0.0307144 E-5 372,550 0.0065669 0.0298547 0.0048218 0.0301088 E-4 372,551 -0.0577106* 0.0299529 -0.0569111* 0.0301399 E-3 372,552 -0.0044376 0.0294581 -0.0118832 0.029806 E-2 372,553 -0.0335521 0.0307138 -0.0166482 0.0310176 E-1 372,554 -0.0260415 0.0317393 -0.0175882 0.0322647 Execution Day 372,555 -0.0623307* 0.0322277 -0.0695759** 0.0332603 E+1 372,554 -0.025698 0.0310109 -0.0203633 0.0319219 E+2 372,553 -0.0094446 0.0300119 -0.0087802 0.030186 E+3 372,552 -0.0345836 0.0297284 -0.0296111 0.0298557 E+4 372,551 -0.0314904 0.0297858 -0.0292947 0.0298783 E+5 372,550 -0.0907129** 0.0314144 -0.0896959** 0.0314642 E+6 372,549 -0.0593144* 0.0319737 -0.0617688* 0.0320935 E+7 372,548 -0.0488551 0.0319898 -0.0494023 0.0320585 E+8 372,547 0.0296735 0.0302657 0.02698 0.0303587 E+9 372,546 -0.0168848 0.0299228 -0.0158498 0.030008 E+10 372,545 0.0073414 0.0292942 0.0047874 0.0293098 E+11 372,544 -0.0098798 0.0295749 -0.0106005 0.029592 E+12 372,543 0.0351367 0.0298786 0.03627 0.0298973 E+13 372,542 -0.0411186 0.0317105 -0.0418706 0.0317242 E+14 372,541 -0.0322977 0.0316575 -0.0341151 0.0316678 Newspaper_E-14 372,555 -0.0872596 0.08241 Newspaper_E-13 372,555 0.0576651 0.0512041 Newspaper_E-12 372,555 0.0130487 0.0428806 Newspaper_E-11 372,555 -0.0178627 0.0325533
92 Table 6 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Newspaper_E-10 372,555 -0.0135708 0.0506208 Newspaper_E-9 372,555 0.030048 0.0300475 Newspaper_E-8 372,555 0.0272212 0.026911 Newspaper_E-7 372,555 0.0120995 0.0293604 Newspaper_E-6 372,555 0.0007994 0.0217291 Newspaper_E-5 372,555 -0.0020025 0.02226 Newspaper_E-4 372,555 0.0007591 0.0173589 Newspaper_E-3 372,555 0.0384297 0.0240707 Newspaper_E-2 372,555 -0.0206747 0.0159291 Newspaper_E-1 372,555 -0.0010144 0.0102766 Newspaper_Execution Day 372,555 0.0053058 0.0064292 Newspaper_E+1 372,555 -0.0022376 0.0038492 Newspaper_E+2 372,555 -0.0006609 0.0100297 Newspaper_E+3 372,555 -0.0378773** 0.0190688 Newspaper_E+4 372,555 -0.0200481 0.0235083 Newspaper_E+5 372,555 -0.0017014 0.0225218 Newspaper_E+6 372,555 0.0411075 0.046772 Newspaper_E+7 372,555 0.0299159 0.0606174 Newspaper_E+8 372,555 0.0713015 0.0784109 Newspaper_E+9 372,555 -0.028741 0.0617393 Newspaper_E+10 372,555 0.2236596** 0.0654225 Newspaper_E+11 372,555 0.0775391 0.0741531 Newspaper_E+12 372,555 -0.0962324 0.074668 Newspaper_E+13 372,555 0.1910177 0.2813564 Newspaper_E+14 372,555 0.1664543 0.1166185 Television_E-14 372,555 Television_E-13 372,555 Television_E-12 372,555 Television_E-11 372,555 Television_E-10 372,555 Television_E-9 372,555 Television_E-8 372,555 Television_E-7 372,555 Television_E-6 372,555 -0.051564 0.0862441 Television_E-5 372,555 0.0349031 0.0703333 Television_E-4 372,555 -0.197799 0.1499367 Television_E-3 372,555 -0.0520614 0.0510562 Television_E-2 372,555 -0.0112502 0.025287 Television_E-1 372,555 0.0187519 0.0137703 Television_Execution Day 372,555 -0.0033731 0.0110946 Television_E+1 372,555 -0.136101 0.0336773 Television_E+2 372,555 0.0355378 0.102652 Television_E+3 372,555 0.0390745 0.0492713 Television_E+4 372,555 Television_E+5 372,555 Television_E+6 372,555 Television_E+7 372,555 Television_E+8 372,555 Television_E+9 372,555 Television_E+10 372,555
93 Table 6 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Television_E+11 372,555 Television_E+12 372,555 Television_E+13 372,555 Television_E+14 372,555 Demographic Variable State Resident Population 372,555 6.50e-08*** 3.26e-09 6.50e-08*** 3.26e-09 Non-Capital Punishment Variables State Prison Population (Number) 372,555 -5.69e-06*** 2.23e-07 -5.69e-06*** 2.23e-07 Active Death Penalty Statutes 372,555 -0.2808466*** 0.01282 -0.2807452*** 0.012819 Temporal Control Variables Sunday Dummy 372,555 0.2719245*** 0.0062229 0.2719639*** 0.0062897 Monday Dummy 372,555 0.0382049*** 0.0065716 0.0381754*** 0.0066161 Tuesday Dummy 372,555 0.01254* 0.0065688 0.0116919* 0.0065957 Wednesday Dummy (omitted) 372,555 Thursday Dummy 372,555 0.013125** 0.006533 0.0125206** 0.0065482 Friday Dummy 372,555 0.1273274*** 0.0064243 0.1269458*** 0.0064503 Saturday Dummy 372,555 0.3673488*** 0.0061225 0.3671921*** 0.0061605 January Dummy 372,555 -0.0081679 0.0084545 -0.0086178 0.008491 February Dummy (omitted) 372,555 March Dummy 372,555 -0.016382** 0.0083418 -0.0158217** 0.0083588 April Dummy 372,555 -0.0159195 0.008616 -0.0142307 0.008648 May Dummy 372,555 -0.0079551 0.0084381 -0.0071392 0.0084683 June Dummy 372,555 0.034309*** 0.0083124 0.0346881*** 0.008326 July Dummy 372,555 0.0849105*** 0.0082993 0.0853515*** 0.008311 August Dummy 372,555 0.1102893*** 0.0081275 0.1106475*** 0.0081401 September Dummy 372,555 0.0627202*** 0.0084008 0.0633094*** 0.0084117 October Dummy 372,555 0.035659*** 0.0082524 0.035153*** 0.0082637 November Dummy 372,555 0.015889 0.0084912 0.0161454 0.0085007 December Dummy 372,555 0.0335222*** 0.0083968 0.0338362*** 0.0084128 Year Dummy-1979 372,555 -0.1047104*** 0.0111515 -0.1043872*** 0.0112345 Year Dummy-1980 372,555 -0.0357605*** 0.0109694 -0.0351434*** 0.0110532 Year Dummy-1981 372,555 -0.0593561*** 0.0109705 -0.0587592*** 0.0110537 Year Dummy-1982 372,555 -0.1136127*** 0.0110151 -0.1134148*** 0.0110934 Year Dummy-1983 372,555 -0.2173245*** 0.0112016 -0.2174944*** 0.0112756 Year Dummy-1984 372,555 -0.2414679*** 0.0112237 -0.2411447*** 0.0112926 Year Dummy-1985 372,555 -0.2337797*** 0.0111734 -0.2327924*** 0.0112322 Year Dummy-1986 372,555 -0.1421063*** 0.0109172 -0.1413327*** 0.0109825 Year Dummy-1987 372,555 -0.1683865*** 0.0109326 -0.1676814*** 0.0109902 Year Dummy-1988 372,555 -0.1261323*** 0.0107842 -0.1256261*** 0.0108568 Year Dummy-1989 372,555 -0.0806033*** 0.0106268 -0.0802784*** 0.0107101 Year Dummy-1990 372,555 0.0102734 0.0103648 0.0108733 0.0104169 Year Dummy-1991 372,555 0.0801895*** 0.0101931 0.0808454*** 0.0102583 Year Dummy-1992 372,555 0.0408538*** 0.0102321 0.0428622*** 0.0103072 Year Dummy-1993 372,555 0.0744452*** 0.0101366 0.0748758*** 0.0101907 Year Dummy-1994 372,555 0.0514548*** 0.0101668 0.0524856*** 0.0102192 Year Dummy-1995 (omitted) 372,555 Year Dummy-1996 372,555 -0.0619271*** 0.0105194 -0.0612865*** 0.0105628 Year Dummy-1997 372,555 -0.1067892*** 0.010657 -0.1063287*** 0.0107114 Year Dummy-1998 372,555 -0.1887708*** 0.0108853 -0.1888772*** 0.0109871 New Year Dummy 372,555 0.6432177*** 0.0256168 0.6442319*** 0.025647
94 Table 6 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors New Year Lag 372,554 0.0210769 0.0324803 0.0219739 0.0324904 Good Friday 372,555 0.0641803** 0.0319979 0.0734049** 0.0330219 Good Friday Lag 372,554 -0.009454 0.0298352 -0.0136195 0.0302815 Easter 372,555 -0.0167019 0.0310202 -0.0099266 0.0314023 Easter Lag 372,554 -0.0281227 0.0343715 -0.0346315 0.0346273 Memorial Day 372,555 0.0467108 0.0334064 0.0462442 0.0334156 Memorial Day Lag 372,554 0.0706935** 0.0332472 0.0702466** 0.0332958 Independence Day 372,555 0.2279262*** 0.0285137 0.2291255*** 0.0285247 Independence Day Lag 372,554 0.0857269** 0.0301005 0.0858229** 0.0301002 Labor Day 372,555 0.1672492*** 0.0308832 0.1670448*** 0.0308809 Labor Day Lag 372,554 0.0842737** 0.0322839 0.0844441** 0.0323403 Thanksgiving Day 372,555 0.1751065*** 0.0319009 0.1757269*** 0.0319031 Thanksgiving Day Lag 372,554 0.0559896** 0.0319242 0.0564592** 0.0319243 Christmas Day 372,555 0.1632321*** 0.0300986 0.1635915*** 0.0300993 Christmas Day Lag 372,554 -0.0887199** 0.0331363 -0.0884503** 0.033137 Geographical Control Variables Alabama 372,555 -0.6477044*** 0.0683304 -0.6485224*** 0.0683189 Alaska 372,555 -3.205663*** 0.0864574 -3.206531*** 0.0864453 Arizona 372,555 -1.022503*** 0.0700935 -1.023338*** 0.0700819 Arkansas 372,555 -1.300826*** 0.0732048 -1.301706*** 0.0731932 California (omitted) 372,555 Colorado 372,555 -1.598864*** 0.0705136 -1.599748*** 0.0705022 Connecticut 372,555 -1.788184*** 0.0718521 -1.789048*** 0.0718407 Delaware 372,555 -3.150307*** 0.085558 -3.15126*** 0.0855463 Washington DC 372,555 -1.191466*** 0.0809897 -1.192338*** 0.0809767 Florida 372,555 -0.0200612 0.0456962 -0.0206833 0.0456889 Georgia 372,555 -0.3164223*** 0.0620338 -0.3172921*** 0.0620238 Hawaii 372,555 -3.215148*** 0.0846885 -3.215996*** 0.0846768 Idaho 372,555 -3.224921*** 0.0846043 -3.225874*** 0.084593 Illinois 372,555 -0.187611*** 0.0457984 -0.1882669*** 0.0457911 Indiana 372,555 -1.090901*** 0.0634912 -1.091877*** 0.0634808 Iowa 372,555 -3.01173*** 0.078034 -3.012523*** 0.0780229 Kansas 372,555 -2.115202*** 0.0757601 -2.116028*** 0.0757484 Kentucky 372,555 -1.357414*** 0.0690077 -1.358259*** 0.0689964 Louisiana 372,555 -0.3317942*** 0.0672896 -0.3325739*** 0.067278 Maine 372,555 -3.745788*** 0.088546 -3.746636*** 0.0885349 Maryland 372,555 -0.7283789*** 0.0668246 -0.7291658*** 0.0668136 Massachusetts 372,555 -1.889384*** 0.0644159 -1.890112*** 0.0644058 Michigan 372,555 -0.5409847*** 0.0565636 -0.5414928*** 0.0565545 Minnesota 372,555 -2.428294*** 0.0706671 -2.429012*** 0.0706564 Mississippi 372,555 -0.9394395*** 0.0721543 -0.9403272*** 0.0721424 Missouri 372,555 -0.7304772*** 0.0649367 -0.7314347*** 0.0649263 Montana 372,555 -3.129082*** 0.0844548 -3.130039*** 0.0844432 Nebraska 372,555 -2.7955*** 0.079745 -2.796481*** 0.079734 Nevada 372,555 -1.772484*** 0.0777575 -1.773422*** 0.0777452 New Hampshire 372,555 -3.851174*** 0.0905034 -3.852067*** 0.0904927 New Jersey 372,555 -1.171812*** 0.0576517 -1.172473*** 0.0576421 New Mexico 372,555 -1.676633*** 0.0761235 -1.677559*** 0.0761113 New York 372,555 -0.2560291*** 0.03246 -0.2562809*** 0.0324546 North Carolina 372,555 -0.4844331*** 0.0611687 -0.485163*** 0.0611585
95 Table 6 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors North Dakota 372,555 -4.426224*** 0.1000403 -4.427084*** 0.1000301 Ohio 372,555 -0.8533598*** 0.0490158 -0.8539457*** 0.0490075 Oklahoma 372,555 -1.199673*** 0.0710101 -1.200507*** 0.0709989 Oregon 372,555 -1.924483*** 0.0726797 -1.925366*** 0.0726682 Pennsylvania 372,555 -0.7692921*** 0.0442734 -0.7698592*** 0.044266 Rhode Island 372,555 -3.264985*** 0.0852009 -3.265866*** 0.0851891 South Carolina 372,555 -0.9591369*** 0.0705857 -0.9599987*** 0.070574 South Dakota 372,555 -3.683076*** 0.0906115 -3.684033*** 0.0906007 Tennessee 372,555 -0.6968989*** 0.0649575 -0.6976975*** 0.0649468 Texas 372,555 0.2344797*** 0.0345282 0.2340851*** 0.0345215 Utah 372,555 -2.680781*** 0.0786372 -2.681749*** 0.0786258 Vermont 372,555 -4.452164*** 0.1009916 -4.453031*** 0.1009813 Virginia 372,555 -0.8023588*** 0.0622129 -0.8031153*** 0.0622026 Washington 372,555 -1.472321*** 0.0658761 -1.473162*** 0.0658656 West Virginia 372,555 -2.324692*** 0.0781888 -2.325521*** 0.078177 Wisconsin 372,555 -2.024423*** 0.0686388 -2.02512*** 0.0686281 Wyoming 372,555 -3.682677*** 0.0913702 -3.683646*** 0.0913592 P-values: * p< 0.10; ** p< 0.05; *** p< 0.01 These data provide some evidence of a short-term deterrent effect associated with the occurrence of an execution. In particular, the estimates show that there are significantly fewer homicides the day of executions, in states that carried out executions than on other state-days. On the other hand, these apparent deterrent effects indicated over the 29-day period do not correspond very well to patterns of news stories about the executions over the same period. There are apparent “deterrent effects” on 13 days before executions and 5 or 6 days after executions, yet no apparent effects for days closer to executions, such as those one to three days before executions, or one to three days after executions, when execution publicity was higher (See Figure 1). Like some prior studies (Grogger, 1990; Hjalmarsson, 2008; Phillips, 1980; Phillips and Hensley, 1984), the present study also finds that a few of the days more remote from executions show negative and statistically significant coefficients. For example, Phillips and Hensley (1984) argued that a deterrent effect of executions remains four days after the execution date. Phillips (1980) proposed that the number of homicides during weeks long after one execution decreases because a new execution event occurred at this time. Philipps did not empirically test this possibility, but the present study supports it. Our data reveal that a 29-day period surrounding any one executions often overlapped with the 29-day period of other executions. Table 7 shows that the State of Texas, the nation’s
96 leading death penalty state which carried out 163 out of the 499 executions, or 32.67 percent, has a mean of 35.90 days between an execution and another execution between 1979 and 1998. This figure does not represent that 4-week periods surrounding an execution overlap with the 4-week period surrounding another execution in the same state. However, its mean value is meaningless because the mean is smaller than the standard deviation. Counting days among execution event dates is more appropriate than calculating the mean and the standard deviation. Thus, 271 out of the 499 executions represent that the time period between one execution event and a new publicized execution event in the same state is less than 28 days. With these data, supplementary analysis is needed to avoid the problem of confusing the effects of one execution with the effects of another execution in the same state. Table 7. Average Number of Days between Execution Dates by State Death Penalty States N Mean Std. Deviation Alabama 15 295.40 265.159 Arizona 11 204.45 247.529 Arkansas 16 183.88 221.042 California 4 568.75 377.654 Delaware 7 213.86 130.294 Florida 43 160.12 236.636 Georgia 22 240.50 245.560 Illinois 10 268.80 403.057 Indiana 5 1234.00 1319.251 Louisiana 23 212.17 283.234 Maryland 2 822.00 452.548 Mississippi 3 706.33 653.534 Missouri 31 109.45 139.676 Montana 1 1021.00 . Nebraska 2 593.50 127.986 Nevada 6 1153.83 913.301 North Carolina 10 536.20 525.428 Oklahoma 12 251.67 308.169 Oregon 1 252.00 . Pennsylvania 1 106.00 . South Carolina 19 267.84 456.313 Texas 163 35.90 56.643 Utah 4 1737.00 1520.752 Virginia 58 102.74 142.708 Washington 2 1053.50 772.868 Total 471 191.70 387.274
The Newspaper and Television Variables The present research estimates two analytical models: one model with a set of newspaper and television publicity variables, and another model without these variables. While two newspaper variables (“E+3” and “E+10”) are statistically significant at the 0.05 level, the rest
97 newspaper variables are not significant. Because these findings do not correspond to the patterns of newspaper and television coverage of executions displayed in Figures 1 and 2, they have no meaningful interpretation. And, all television variables are statistically insignificant, suggesting that the volume of television news stories about executions has no effect on homicidal behavior. Taken together, this could be explained by the newspaper reading and television viewing habits of potential murderers (Hjalmarsson, 2008). Potential murderers may be more likely to be aware of the existence and application of executions through social networks of criminals than through reading the newspaper or watching the evening news. Noncapital offenders who are released from prison back to their community may be better informed about executions than other individuals, without benefit of news media transmitted information Although the coefficients and standard errors of the rest of the independent variables increase or decrease slightly, these variables remain statistically significant and in the same direction as in the model that included the 29 newspaper and television variables. To check whether the apparent insignificance of the newspaper and television variables was due to the collinearity with the execution dummies, the negative binomial regression model was estimated with the execution variables excluded. None of the newspaper and television variables were statistically significant. Table 6 presents two models with and without the set of 28 leads and lags of newspaper and television variables and the contemporaneous variable. Non-Capital Punishment Variables Three kinds of non-execution punishment variables are included in the analysis: (1) the existence of an active death penalty statute of each state, (2) the raw number of state and federal prison inmates, and (3) total state and federal prison population rates. The coefficient of the active death penalty statute variable, - 0.2808466, is statistically significant at the 0.01 level. Although the effect is not large in absolute value, active death penalty laws are associated with fewer daily homicides in states. There are about 28.08 percent fewer homicides when the death penalty statute of each state is in effect than when no death penalty statute is in effect. The coefficient of the total state and federal prison population count variable, (- 5.69e-06, or 0.00000569), is statistically significant at the 0.01 level. This represents a very weak negative relationship between the total state and federal prison populations and homicides in the states, suggesting that as the number of inmates in state and federal prisons increases, the number of homicides decreases. This is clear empirical evidence enough to support the incapacitative effect
98 of imprisonment, suggesting that prisoners are deprived of the opportunity to commit homicides while incarcerated. Thus, our study shows that the deterrent effect of executions on homicides is separated from the incapacitative effect of imprisonment on homicides. Although this variable is an indirect measure of imprisonment, our study overcomes the weakness of prior studies, the omission of the incapacitative effect of imprisonment, and is based on more appropriate theoretical specification than the previous studies. As shown in Table 6, the negative binomial regression analysis, the individual estimated coefficients for the 29 daily execution variables suggest that any deterrent effects of executions on homicides are diluted and may be too small to be important from a policy standpoint. For example, the estimated coefficient of the “E” variable is -0.0623307 (Or, - 0.0695759 when a model includes news variables), indicating that the average state-day with an execution has 0.0623307 (Or, 0.06955759) fewer homicides than state-day that are not within 2 weeks surrounding an execution. There were, on average, approximately sixty-one (445,420 homicides / 7,305 days = 60.9746749) homicides per day across the U.S. in 1979-1998, about 4.14 homicides are deterred by an execution on the execution day in the U.S. There were 499 execution state-days in the U.S. in 1979-1998, so if each execution only deterred homicide on the day the execution occurred, in the state where it occurred, the aggregate effect in the U.S. the U.S. as a whole would be just 32 fewer homicides-only 7/1000 of one percent of the national homicide total of 445,420. The deterrent effect of executions, however, is not necessarily limited to the day of the execution. In Table 8, we can produce an alternative estimate of the short-term effects of executions by summing the coefficients for all 29 days surrounding executions. The total of all 29 execution coefficients in the final model is -0.5748874. There were 499 executions in the U.S. in 1979-1998. If each execution deterred 0.574 homicides across the entire 4-week period surrounding it, these estimates would imply that 288 homicides were deterred in these periods in the states where executions were carried out, which is just 6/100th of one percent of the total U.S. homicides committed in this period. Estimated this way, the short-term deterrent effect of executions is extremely modest. Table 8. The Sum of the Coefficient Values for 4-Week Period Surrounding Executions Variables Model without News Variables Independent Variables of Interest The Estimated Coefficients E-14 - 0.0121964 E-13 - 0.0517452*
99 Table 8 - Continued Variables Model without News Variables Independent Variables of Interest The Estimated Coefficients E-12 - 0.0404428 E-11 0.0107228 E-10 - 0.0164697 E-9 0.0096602 E-8 0.0231316 E-7 0.0035433 E-6 0.0045427 E-5 0.0065669 E-4 -0.0577106* E-3 -0.0044376 E-2 -0.0335521 E-1 -0.0260415 Execution Day -0.0623307* E+1 -0.025698 E+2 -0.0094446 E+3 -0.0345836 E+4 -0.0314904 E+5 -0.0907129** E+6 -0.0593144* E+7 -0.0488551 E+8 0.0296735 E+9 -0.0168848 E+10 0.0073414 E+11 -0.0098798 E+12 0.0351367 E+13 -0.0411186 E+14 -0.0322977 Total Coefficient Values -0.5748874
100 0.04 0.03 0.02 0.01 4 1 - E 3 1 - E 2 1 - E 1 1 - E 0 1 - E 9 - E 8 - E 7 - E 6 - E 5 - E 4 - E 3 - E 2 - E 1 - E 1 + E 2 + E 3 + E 4 + E 5 + E 6 + E 7 + E 8 + E 9 + E 0 1 + E 1 1 + E 2 1 + E 3 1 + E 4 1 + E
0 AY D N IO T U C E X E -0.01 -0.02 -0.03 -0.04 -0.05 -0.06 * * -0.07 * * or ** -0.08 -0.09 -0.1 ** Figure 5. The Estimated Coefficient Graph for the 4- Week Period Surrounding Executions Model w/o News Variables Model with News Variables
Figure 5 illustrates the temporal pattern of estimated “deterrent effects” of execution. The estimate for the day of execution (Execution Day) makes sense in that it is large and negative, but other estimates make little sense from the standpoint of deterrence theory. There is no clear reason why supposed deterrent effects should be just strongest five days after executions, and stronger for that day than for days just one to four days after an execution. Likewise, it is not plausible that relatively large effects would occur 13 days before an execution but not one to three days before an execution. Further, a comparison of Figure 5 with Figures 1 and 2 shows that these days of fewer homicides do not correspond with days when publicity about executions peaked, other than the day when executions occurred. Supplementary Analyses for the Test of Sensitivity We now turn our attention to a series of robust tests of our main results. In Table 9, we estimate a model in which the only execution variable (E) as the independent variable of interest is considered. This variable is a single binary variable (0/1) indicating the day of an execution. The estimated coefficient of the “E” variable is – 0.0686933 and statistically significant at the 0.05 level. When newspaper and television variables are introduced into the analytical model, its coefficient increases up to – 0.0845291 and significant at the 0.05 level. Thus, the aggregate
101 effect of 499 executions in the U.S. would be approximately 34 fewer homicides – only 7/1000 of one percent of the national homicide total of 445,420. The negative binomial regression results of the test of sensitivity test is robust with respect to the deterrent effect of execution on homicides on the day of execution. Table 9. Negative Binomial Regression Models with the only “E” Variable Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Execution Day 372,555 -0.0686933** 0.0327003 -0.0845291** 0.0329927 Newspaper_E-14 372,555 -0.0885556 0.0822701 Newspaper_E-13 372,555 0.048291 0.0508859 Newspaper_E-12 372,555 0.0093454 0.0427777 Newspaper_E-11 372,555 -0.0176049 0.0325207 Newspaper_E-10 372,555 -0.0169968 0.0504125 Newspaper_E-9 372,555 0.0314008 0.0299826 Newspaper_E-8 372,555 0.0280083 0.026844 Newspaper_E-7 372,555 0.0119861 0.0291732 Newspaper_E-6 372,555 0.002061 0.02159 Newspaper_E-5 372,555 -0.0015162 0.0220445 Newspaper_E-4 372,555 -0.0035212 0.0172748 Newspaper_E-3 372,555 0.0370587 0.023799 Newspaper_E-2 372,555 -0.0226913 0.0157921 Newspaper_E-1 372,555 -0.0027246 0.0101194 Newspaper_Execution Day 372,555 0.0059239 0.0064282 Newspaper_E+1 372,555 -0.0029487 0.0037437 Newspaper_E+2 372,555 -0.0009497 0.0099733 Newspaper_E+3 372,555 -0.040451** 0.0190013 Newspaper_E+4 372,555 -0.021817 0.023451 Newspaper_E+5 372,555 -0.0054857 0.0225203 Newspaper_E+6 372,555 0.030672 0.0465742 Newspaper_E+7 372,555 0.0262107 0.0604853 Newspaper_E+8 372,555 0.0779635 0.078178 Newspaper_E+9 372,555 -0.0319771 0.0615835 Newspaper_E+10 372,555 0.2245249** 0.0653809 Newspaper_E+11 372,555 0.0714596 0.0740905 Newspaper_E+12 372,555 -0.093365 0.0746302 Newspaper_E+13 372,555 0.1848138 0.2808223 Newspaper_E+14 372,555 0.1632146 0.1165429 Television_E-14 372,555 Television_E-13 372,555 Television_E-12 372,555 Television_E-11 372,555 Television_E-10 372,555 Television_E-9 372,555 Television_E-8 372,555 Television_E-7 372,555 Television_E-6 372,555 -0.0548555 0.086234 Television_E-5 372,555 0.0365952 0.0703224 Television_E-4 372,555 -0.1963815 0.150061
102 Table 9 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Television_E-3 372,555 -0.0502198 0.0509479 Television_E-2 372,555 -0.0111851 0.0252932 Television_E-1 372,555 0.0193987 0.0137637 Television_Execution Day 372,555 -0.0039198 0.0110956 Television_E+1 372,555 -0.0125892 0.0336771 Television_E+2 372,555 0.0319508 0.1026718 Television_E+3 372,555 0.039188 0.0492959 Television_E+4 372,555 Television_E+5 372,555 Television_E+6 372,555 Television_E+7 372,555 Television_E+8 372,555 Television_E+9 372,555 Television_E+10 372,555 Television_E+11 372,555 Television_E+12 372,555 Television_E+13 372,555 Television_E+14 372,555 Demographic Variable State Resident Population 372,555 6.57e-08*** 3.26e-09 6.57e-08*** 3.26e-09 Non-Capital Punishment Variables State Prison Population (Number) 372,555 -5.80e-06*** 2.21e-07 -5.80e-06*** 2.21e-07 Active Death Penalty Statutes 372,555 -0.2791786*** 0.0128147 -0.279035*** 0.0128137 Temporal Control Variables Sunday Dummy 372,555 0.2719539*** 0.0061956 0.2720561*** 0.0062684 Monday Dummy 372,555 0.0380016*** 0.0065537 0.0379487*** 0.0066021 Tuesday Dummy 372,555 0.0124766* 0.0065621 0.011596* 0.0065913 Wednesday Dummy (omitted) 372,555 Thursday Dummy 372,555 0.013283** 0.0065264 0.0126941** 0.0065425 Friday Dummy 372,555 0.12751*** 0.0064061 0.1270976*** 0.0064352 Saturday Dummy 372,555 0.3675275*** 0.0060959 0.3673616*** 0.0061371 January Dummy 372,555 -0.0080012*** 0.0084547 -0.0083132 0.008491 February Dummy (omitted) 372,555 March Dummy 372,555 -0.0167287** 0.0083432 -0.0160844** 0.0083603 April Dummy 372,555 -0.0166795* 0.0086159 -0.0147785* 0.0086483 May Dummy 372,555 -0.0092212 0.0084335 -0.0081936 0.008465 June Dummy 372,555 0.0335849*** 0.0083126 0.0340148*** 0.0083263 July Dummy 372,555 0.0848526*** 0.0083011 0.0852843*** 0.0083127 August Dummy 372,555 0.1099569*** 0.0081292 0.1103411*** 0.0081417 September Dummy 372,555 0.0621467*** 0.0084015 0.0627471*** 0.0084123 October Dummy 372,555 0.0359803*** 0.0082533 0.0362497*** 0.0082644 November Dummy 372,555 0.0157615* 0.0084926 0.0159922* 0.0085021 December Dummy 372,555 0.0331276*** 0.0083973 0.0334841*** 0.0084134 Year Dummy-1979 372,555 -0.10386*** 0.0111481 -0.1038319*** 0.0112305 Year Dummy-1980 372,555 -0.0348749** 0.0109686 -0.0345902** 0.0110521 Year Dummy-1981 372,555 -0.058414*** 0.0109694 -0.0580992*** 0.0110522 Year Dummy-1982 372,555 -0.1126551*** 0.011014 -0.1127363*** 0.011092 Year Dummy-1983 372,555 -0.2164489*** 0.0112009 -0.2168755*** 0.0112746 Year Dummy-1984 372,555 -0.2416906*** 0.0112256 -0.2415189*** 0.0112931 Year Dummy-1985 372,555 -0.2337937*** 0.0111758 -0.2331079*** 0.0112334
103 Table 9 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Year Dummy-1986 372,555 -0.1423672*** 0.01092 -0.1418797*** 0.0109834 Year Dummy-1987 372,555 -0.1684437*** 0.0109348 -0.1680188*** 0.0109911 Year Dummy-1988 372,555 -0.1252484*** 0.0107834 -0.1250744*** 0.0108558 Year Dummy-1989 372,555 -0.0797142*** 0.0106259 -0.0797013*** 0.0107091 Year Dummy-1990 372,555 0.011067 0.0103646 0.0114467 0.0104164 Year Dummy-1991 372,555 0.0814244*** 0.0101899 0.0817792*** 0.0102555 Year Dummy-1992 372,555 0.0412179*** 0.0102344 0.0433512*** 0.0103084 Year Dummy-1993 372,555 0.0742121*** 0.0101395 0.0745364*** 0.0101927 Year Dummy-1994 372,555 0.0524082*** 0.0101659 0.0533019*** 0.0102179 Year Dummy-1995 (omitted) 372,555 Year Dummy-1996 372,555 -0.0603146*** 0.0105118 -0.0597679*** 0.0105553 Year Dummy-1997 372,555 -0.1076395*** 0.0106573 -0.1073113*** 0.0107106 Year Dummy-1998 372,555 -0.1887727*** 0.0108868 -0.1889033*** 0.0109874 New Year Dummy 372,555 0.6426828*** 0.0256169 0.6436752*** 0.0256465 New Year Lag 372,554 0.0232779 0.0324462 0.0239919 0.0324564 Good Friday 372,555 0.0647084** 0.0320022 0.0749877** 0.0330134 Good Friday Lag 372,554 -0.0086718 0.0298391 -0.012982 0.0302816 Easter 372,555 -0.0167682 0.0310273 -0.009792 0.0314076 Easter Lag 372,554 -0.0273711 0.0343772 -0.033627 0.0346256 Memorial Day 372,555 0.0457746 0.0334133 0.045087 0.0334227 Memorial Day Lag 372,554 0.06967** 0.0332556 0.0692304** 0.0333039 Independence Day 372,555 0.2275787*** 0.0285176 0.2288207*** 0.0285281 Independence Day Lag 372,554 0.0854802** 0.0301057 0.0854055** 0.030106 Labor Day 372,555 01680098*** 0.0308879 0.1676958*** 0.0308859 Labor Day Lag 372,554 0.0839157** 0.0322906 0.0840464** 0.032347 Thanksgiving Day 372,555 0.1739728*** 0.0319016 0.1745392*** 0.031904 Thanksgiving Day Lag 372,554 0.0555332 0.0319227 0.0559185 0.0319229 Christmas Day 372,555 0.1637616*** 0.0301006 0.1639225*** 0.0301019 Christmas Day Lag 372,554 -0.0876507** 0.0331387 -0.0875557** 0.03314 Geographical Control Variables Alabama 372,555 -0.6381099*** 0.0682895 -0.6388561*** 0.0682769 Alaska 372,555 -3.192053*** 0.0863938 -3.192854*** 0.0863805 Arizona 372,555 -1.012386*** 0.0700533 -1.013147*** 0.0700406 Arkansas 372,555 -1.290643*** 0.0731673 -1.291413*** 0.0731543 California (omitted) 372,555 Colorado 372,555 -1.588599*** 0.0704732 -1.589402*** 0.0704606 Connecticut 372,555 -1.77743*** 0.0718074 -1.778222*** 0.0717947 Delaware 372,555 -3.138896*** 0.0855166 -3.139764*** 0.0855037 Washington DC 372,555 -1.177493*** 0.0809163 -1.178302*** 0.0809019 Florida 372,555 -0.0153911 0.0456858 -0.0159326 0.0456778 Georgia 372,555 -0.3080213*** 0.0620042 -0.3088054*** 0.061993 Hawaii 372,555 -3.201931*** 0.0846276 -3.20271*** 0.0846145 Idaho 372,555 -3.213453*** 0.0845618 -3.214319*** 0.0845493 Illinois 372,555 -0.1818309*** 0.0457806 -0.1824153*** 0.0457725 Indiana 372,555 -1.081982*** 0.0634579 -1.08288*** 0.0634465 Iowa 372,555 -2.999601*** 0.0779786 -3.000331*** 0.0779662 Kansas 372,555 -2.103009*** 0.075702 -2.103768*** 0.075689 Kentucky 372,555 -1.347356*** 0.0689681 -1.348124*** 0.0689556 Louisiana 372,555 -0.3228925*** 0.067259 -0.3236013*** 0.0672464 Maine 372,555 -3.732757*** 0.0884895 -3.733537*** 0.0884772
104 Table 9 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Maryland 372,555 -0.718155*** 0.0667811 -0.718873*** 0.0667688 Massachusetts 372,555 -1.879503*** 0.0643711 -1.880169*** 0.0643599 Michigan 372,555 -0.5309211*** 0.056508 -0.5313979*** 0.0564979 Minnesota 372,555 -2.41736*** 0.0706183 -2.418014*** 0.0706064 Mississippi 372,555 -0.9287606*** 0.0721112 -0.9295696*** 0.072098 Missouri 372,555 -0.7228039*** 0.0649155 -0.7236549*** 0.064904 Montana 372,555 -3.117567*** 0.0844119 -3.118438*** 0.0843991 Nebraska 372,555 -2.784527*** 0.0797041 -2.785399*** 0.0796917 Nevada 372,555 -1.761138*** 0.0777122 -1.761994*** 0.0776986 New Hampshire 372,555 -3.838666*** 0.0904527 -3.839482*** 0.0904407 New Jersey 372,555 -1.163352*** 0.057618 -1.163953*** 0.057075 New Mexico 372,555 -1.665278*** 0.076077 -1.666122*** 0.0760635 New York 372,555 -0.2504968*** 0.0324306 -0.2507376*** 0.0324248 North Carolina 372,555 -0.4756498*** 0.0611346 -0.4763144*** 0.0611234 North Dakota 372,555 -4.412872*** 0.0999878 -4.413661*** 0.0999764 Ohio 372,555 -0.8460834*** 0.0489847 -0.8466193*** 0.0489756 Oklahoma 372,555 -1.189694*** 0.0709726 -1.19043*** 0.0709601 Oregon 372,555 -1.91401*** 0.0726388 -1.914814*** 0.0726262 Pennsylvania 372,555 -0.7638665*** 0.0442574 -0.7643645*** 0.0442492 Rhode Island 372,555 -3.252027*** 0.0851419 -3.252837*** 0.0851289 South Carolina 372,555 -0.9492565*** 0.0705485 -0.9500418*** 0.0705355 South Dakota 372,555 -3.671353*** 0.0905698 -3.672226*** 0.0905578 Tennessee 372,555 -0.6873484*** 0.0649199 -0.6880729*** 0.064908 Texas 372,555 0.2306715*** 0.0345153 0.230363*** 0.034509 Utah 372,555 -2.669951*** 0.0785972 -2.670831*** 0.0785845 Vermont 372,555 -4.438699*** 0.1009385 -4.439496*** 0.1009272 Virginia 372,555 -0.7969667*** 0.0622039 -0.7976189*** 0.0621929 Washington 372,555 -1.463059*** 0.0658415 -1.463812*** 0.0658299 West Virginia 372,555 -2.312093*** 0.0781291 -2.312847*** 0.078116 Wisconsin 372,555 -2.013443*** 0.0685875 -2.01408*** 0.0685756 Wyoming 372,555 -3.672607*** 0.091328 -3.673488*** 0.0913158 P-values: * p< 0.10; ** p< 0.05; *** p< 0.01 Table 10 presents the results of a negative binomial regression analytical model in which a 29 day dummy variable as the main independent variable of interest was considered. This variable was a dichotomous variable that was coded as one if there were any executions within the 14 calendar days of the target execution date, and zero otherwise. The estimated coefficient of the 29-day dummy variable is – 0.0229074 and statistically significant at the 0.05 level. This estimate would imply that 11 homicides were deterred in these periods in the states where executions were carried out, which is just 3/1000 of one percent of the total U.S. homicides committed in this period. The negative binomial regression results of the test of sensitivity test is robust with respect to the deterrent effect of the sum of 29 execution variables (E-14 through E+14) on homicides.
105 Table 10. Negative Binomial Regression Models with the only 29-Day Dummy Variable Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors 29-DAY DUMMY 372,541 -0.0229074** 0.0075683 -0.0232123** 0.0076164 Newspaper_E-14 372,555 -0.0865396 0.0822917 Newspaper_E-13 372,555 0.0505001 0.05089 Newspaper_E-12 372,555 0.0114994 0.0427846 Newspaper_E-11 372,555 -0.0162783 0.0325222 Newspaper_E-10 372,555 -0.0146781 0.0504237 Newspaper_E-9 372,555 -0.0146781 0.0299875 Newspaper_E-8 372,555 0.0290284 0.0268463 Newspaper_E-7 372,555 0.0139052 0.0291845 Newspaper_E-6 372,555 0.0034777 0.0215975 Newspaper_E-5 372,555 0.0006053 0.022057 Newspaper_E-4 372,555 -0.0023433 0.0172786 Newspaper_E-3 372,555 0.0390538 0.0238083 Newspaper_E-2 372,555 -0.021051 0.0157979 Newspaper_E-1 372,555 -0.0017947 0.0101253 Newspaper_Execution Day 372,555 0.0027542 0.0062494 Newspaper_E+1 372,555 -0.0025261 0.0037459 Newspaper_E+2 372,555 -0.0005501 0.0099744 Newspaper_E+3 372,555 -0.0393176** 0.0189967 Newspaper_E+4 372,555 -0.0206761 0.0234434 Newspaper_E+5 372,555 -0.0049748 0.0225162 Newspaper_E+6 372,555 0.0334429 0.0465717 Newspaper_E+7 372,555 0.0272778 0.0604886 Newspaper_E+8 372,555 0.0819436 0.078189 Newspaper_E+9 372,555 -0.0300226 0.0615968 Newspaper_E+10 372,555 0.2265436** 0.0653875 Newspaper_E+11 372,555 0.0720341 0.0740879 Newspaper_E+12 372,555 -0.0914521 0.0746385 Newspaper_E+13 372,555 0.1886517 0.2810783 Newspaper_E+14 372,555 0.1658423 0.1165454 Television_E-14 372,555 Television_E-13 372,555 Television_E-12 372,555 Television_E-11 372,555 Television_E-10 372,555 Television_E-9 372,555 Television_E-8 372,555 Television_E-7 372,555 Television_E-6 372,555 -0.0535387 0.0862343 Television_E-5 372,555 0.0366597 0.0703214 Television_E-4 372,555 -0.1947678 0.1499703 Television_E-3 372,555 -0.0516666 0.0509407 Television_E-2 372,555 -0.0114779 0.0252875 Television_E-1 372,555 0.0193461 0.0137659 Television_Execution Day 372,555 -0.0025052 0.0110778 Television_E+1 372,555 -0.0128829 0.0336757 Television_E+2 372,555 0.0325119 0.1026678 Television_E+3 372,555 0.0401607 0.0492668 Television_E+4 372,555 Television_E+5 372,555
106 Table 10 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Television_E+6 372,555 Television_E+7 372,555 Television_E+8 372,555 Television_E+9 372,555 Television_E+10 372,555 Television_E+11 372,555 Television_E+12 372,555 Television_E+13 372,555 Television_E+14 372,555 Demographic Variable State Resident Population 372,555 6.60e-08*** 3.26e-09 6.60e-08*** 3.26e-09 Non-Capital Punishment Variables State Prison Population (Number) 372,555 -5.80e-06*** 2.21e-07 -5.80e-06*** 2.21e-07 Active Death Penalty Statutes 372,555 -0.2797281*** 0.0128176 -0.2796337*** 0.0128167 Temporal Control Variables Sunday Dummy 372,555 0.2723023*** 0.0061928 0.2722396*** 0.0062678 Monday Dummy 372,555 0.0382409*** 0.0065523 0.0380997*** 0.0066018 Tuesday Dummy 372,555 0.0124297* 0.0065618 0.0115216* 0.0065909 Wednesday Dummy (omitted) 372,555 Thursday Dummy 372,555 0.0133804** 0.0065258 0.0126811** 0.0065422 Friday Dummy 372,555 0.127645*** 0.0064054 0.1272252*** 0.0064347 Saturday Dummy 372,555 0.367864*** 0.0060932 0.3675335*** 0.0061365 January Dummy 372,555 -0.0080997 0.0084543 -0.0084155 0.0084909 February Dummy (omitted) 372,555 March Dummy 372,555 -0.0163668** 0.0083438 -0.0157127** 0.0083609 April Dummy 372,555 -0.0161389 0.0086176 -0.0143383 0.0086494 May Dummy 372,555 -0.0084264 0.0084391 -0.0074584 0.008469 June Dummy 372,555 0.0338251*** 0.0083128 0.0342736*** 0.0083264 July Dummy 372,555 0.0850958*** 0.0083011 0.0855414*** 0.0083127 August Dummy 372,555 0.1100801*** 0.0081289 0.1104801*** 0.0081415 September Dummy 372,555 0.0626499*** 0.0084031 0.063299*** 0.008414 October Dummy 372,555 0.0357768*** 0.0082534 0.03599*** 0.0082645 November Dummy 372,555 0.0159843*** 0.0084925 0.0162452*** 0.0085022 December Dummy 372,555 0.0332638*** 0.008397 0.0336003*** 0.0084132 Year Dummy-1979 372,555 -0.105701*** 0.0111663 -0.1057659** 0.0128167 Year Dummy-1980 372,555 -0.0368383** 0.0109897 -0.0365795*** 0.0112435 Year Dummy-1981 372,555 -0.0604078*** 0.0109913 -0.0601292*** 0.0110681 Year Dummy-1982 372,555 -0.114552*** 0.0110338 -0.11468*** 0.0111065 Year Dummy-1983 372,555 -0.2182403*** 0.0112183 -0.2187103*** 0.0112875 Year Dummy-1984 372,555 -0.2422678*** 0.0112265 -0.2420776*** 0.0112933 Year Dummy-1985 372,555 -0.2345535*** 0.0111778 -0.2337844*** 0.0112338 Year Dummy-1986 372,555 -0.1432402*** 0.0109224 -0.1427327*** 0.0109837 Year Dummy-1987 372,555 -0.1693141*** 0.0109376 -0.1688217*** 0.0109921 Year Dummy-1988 372,555 -0.1267077*** 0.0107953 -0.1265068*** 0.0108637 Year Dummy-1989 372,555 -0.0809859*** 0.0106352 -0.081008*** 0.0107148 Year Dummy-1990 372,555 0.0100894 0.01037 0.010522 0.0104204 Year Dummy-1991 372,555 0.0801732*** 0.0101997 0.080565*** 0.0102621 Year Dummy-1992 372,555 0.0406339*** 0.0102354 0.042579*** 0.0103102 Year Dummy-1993 372,555 0.0737752*** 0.0101393 0.07405*** 0.0101918 Year Dummy-1994 372,555 0.051497*** 0.0101707 0.0523896*** 0.0102219
107 Table 10 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Year Dummy-1995 (omitted) 372,555 Year Dummy-1997 372,555 -0.1081634*** 0.0106576 -0.1079616*** 0.0107099 Year Dummy-1998 372,555 -0.1887665*** 0.0108862 -0.1890606*** 0.0109867 New Year Dummy 372,555 0.6422924*** 0.0256168 0.6432361*** 0.0256464 New Year Lag 372,554 0.022878 0.032446 0.0235968 0.032456 Good Friday 372,555 0.0646102** 0.0319991 0.0743223** 0.0330135 Good Friday Lag 372,554 -0.0089739 0.0298362 -0.0134338 0.0302803 Easter 372,555 -0.017042 0.0310243 -0.0101806 0.0314057 Easter Lag 372,554 -0.0279151 0.0343755 -0.0343587 0.0346262 Memorial Day 372,555 0.045891 0.0334087 0.0452725 0.0334183 Memorial Day Lag 372,554 0.0701173** 0.0332507 0.0694838 0.0332999 Independence Day 372,555 0.2276593*** 0.0285157 0.2288243*** 0.0285265 Independence Day Lag 372,554 0.0856621** 0.0301039 0.0856012** 0.0301045 Labor Day 372,555 0.1680145*** 0.0308854 0.1676792*** 0.0308836 Labor Day Lag 372,554 0.08443** 0.0322864 0.0843625** 0.0323435 Thanksgiving Day 372,555 0.174445*** 0.0318992 0.175032*** 0.0319021 Thanksgiving Day Lag 372,554 0.0559599** 0.0319203 0.0562637** 0.031921 Christmas Day 372,555 0.1636851*** 0.0300985 0.163877*** 0.0300999 Christmas Day Lag 372,554 -0.087846** 0.0331371 -0.0877056** 0.0331384 Geographical Control Variables Alabama 372,555 -0.6301068*** 0.0683209 -0.6306743*** 0.0683079 Alaska 372,555 -3.184787*** 0.0864076 -3.18538*** 0.086394 Arizona 372,555 -1.004566*** 0.0700814 -1.005146*** 0.0700683 Arkansas 372,555 -1.282405*** 0.0731976 -1.283003*** 0.0731838 California (omitted) 372,555 Colorado 372,555 -1.581535*** 0.0704932 -1.582167*** 0.0704801 Connecticut 372,555 -1.770399*** 0.0718263 -1.771011*** 0.0718132 Delaware 372,555 -3.130506*** 0.0855417 -3.131174*** 0.0855283 Washington DC 372,555 -1.170215*** 0.0809313 -1.170808*** 0.0809165 Florida 372,555 -0.0080888 0.0457359 -0.0085234 0.0457271 Georgia 372,555 -0.3003751*** 0.0620371 -0.3009952*** 0.0620254 Hawaii 372,555 -3.194825*** 0.0846412 -3.195403*** 0.0846278 Idaho 372,555 -3.205692*** 0.0845817 -3.206366*** 0.0845687 Illinois 372,555 -0.1765243*** 0.0458022 -0.177001*** 0.0457934 Indiana 372,555 -1.075174*** 0.0634809 -1.07591*** 0.0634689 Iowa 372,555 -2.993002*** 0.0779918 -2.993544*** 0.0779791 Kansas 372,555 -2.096166*** 0.0757167 -2.096738*** 0.0757034 Kentucky 372,555 -1.340393*** 0.0689883 -1.340991*** 0.0689754 Louisiana 372,555 -0.3147959*** 0.0672934 -0.3153318*** 0.0672805 Maine 372,555 -3.725682*** 0.0885026 -3.726264*** 0.08849 Maryland 372,555 -0.7113216*** 0.0668006 -0.7118688*** 0.066788 Massachusetts 372,555 -1.873738*** 0.0643851 -1.874238*** 0.0643735 Michigan 372,555 -0.5262372*** 0.0565159 -0.5265674*** 0.0565057 Minnesota 372,555 -2.411214*** 0.0706311 -2.411702*** 0.0706189 Mississippi 372,555 -0.9212436*** 0.0721341 -0.9218708*** 0.0721205 Missouri 372,555 -0.7142189*** 0.0649591 -0.714915*** 0.0649467 Montana 372,555 -3.109681*** 0.0844328 -3.110357*** 0.0844196 Nebraska 372,555 -2.776759*** 0.0797264 -2.777454*** 0.0797131 Nevada 372,555 -1.753057*** 0.0777369 -1.753716*** 0.0777228 New Hampshire 372,555 -3.831297*** 0.0904675 -3.831916*** 0.0904552
108 Table 10 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors New Jersey 372,555 -1.157705*** 0.0576334 -1.158169*** 0.0576225 New Mexico 372,555 -1.657761*** 0.0760972 -1.658416*** 0.0760832 New York 372,555 -0.2482183*** 0.0324335 -0.2483841*** 0.0324278 North Carolina 372,555 -0.4687467*** 0.0611598 -0.4692514*** 0.0611481 North Dakota 372,555 -4.405636*** 0.0999999 -4.406221*** 0.0999882 Ohio 372,555 -0.8412904*** 0.0489982 -0.842327*** 0.0489889 Oklahoma 372,555 -1.181767*** 0.0710012 -1.182327*** 0.0709879 Oregon 372,555 -1.906718*** 0.0726599 -1.907344*** 0.0726467 Pennsylvania 372,555 -0.7591976*** 0.0442741 -0.7595973*** 0.0442655 Rhode Island 372,555 -3.244827*** 0.0851571 -3.245437*** 0.0851438 South Carolina 372,555 -0.9410189*** 0.0705812 -0.94162*** 0.0705678 South Dakota 372,555 -3.663579*** 0.0905882 -3.664256*** 0.0905757 Tennessee 372,555 -0.6808184*** 0.0649382 -0.6813793*** 0.0649259 Texas 372,555 0.2405732*** 0.0346872 0.2403263*** 0.03681 Utah 372,555 -2.662163*** 0.0786199 -2.662857*** 0.0786066 Vermont 372,555 -4.431436*** 0.1009505 -4.432027*** 0.1009389 Virginia 372,555 -0.7867815*** 0.0622802 -0.787283*** 0.0622685 Washington 372,555 -1.456256*** 0.0658622 -1.456845*** 0.0658501 West Virginia 372,555 -2.305207*** 0.0781434 -2.305763*** 0.0781298 Wisconsin 372,555 -2.007456*** 0.0685998 -2.007924*** 0.0685877 Wyoming 372,555 -3.664685*** 0.0913471 -3.665367*** 0.0913345 P-values: * p< 0.10; ** p< 0.05; *** p< 0.01 Table 11 presents the results of a negative binomial regression analytical model in which a 15 day dummy variable as the main independent variable of interest was considered. This variable was a dichotomous variable that was coded as one if there were any executions in the state within the 14 days of the indicated execution date, and zero otherwise. The estimated coefficient of the 15-day dummy variable is – 0.0366124 and statistically significant at the 0.05 level. This estimate would imply that 18 homicides were deterred in these periods in the states where executions were carried out, which is just 4/1000 of one percent of the total U.S. homicides committed in this period. The negative binomial regression results of the test of sensitivity test is robust with respect to the deterrent effect of the sum of 29 execution variables (E-14, through E+14) on homicides. A comparison of the absolute values of the coefficients of the 29-day- and 15-day dummy execution variables would indicate that the deterrent effect of executions lessens as days pass by. Table 11. Negative Binomial Regression Models with the only 15-Day Dummy Variable Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors 15-DAY DUMMY 372,541 -0.0366124*** 0.0094318 -0.0363972*** 0.0095297 Newspaper_E-14 372,555 -0.0876206 0.0822413 Newspaper_E-13 372,555 0.0462157 0.050884 Newspaper_E-12 372,555 0.0090343 0.0427635
109 Table 11 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Newspaper_E-11 372,555 -0.0168934 0.0325234 Newspaper_E-10 372,555 -0.0161422 0.0503979 Newspaper_E-9 372,555 0.0312535 0.0299751 Newspaper_E-8 372,555 0.0280747 0.0268432 Newspaper_E-7 372,555 0.0153808 0.0291943 Newspaper_E-6 372,555 0.0043549 0.0216036 Newspaper_E-5 372,555 0.0019922 0.0220664 Newspaper_E-4 372,555 -0.0016935 0.017269 Newspaper_E-3 372,555 0.0408856* 0.0238192 Newspaper_E-2 372,555 -0.0199454 0.0158039 Newspaper_E-1 372,555 -0.0010324 0.0101311 Newspaper_Execution Day 372,555 0.0033802 0.0062547 Newspaper_E+1 372,555 -0.0021354 0.0037487 Newspaper_E+2 372,555 -0.0000154 0.009977 Newspaper_E+3 372,555 -0.0384544** 0.0189968 Newspaper_E+4 372,555 -0.019849 0.0234415 Newspaper_E+5 372,555 -0.0041914 0.022514 Newspaper_E+6 372,555 0.0347755 0.0465745 Newspaper_E+7 372,555 0.0290331 0.0604901 Newspaper_E+8 372,555 0.0777785 0.0781752 Newspaper_E+9 372,555 -0.0313588 0.0615632 Newspaper_E+10 372,555 0.2257468** 0.0653668 Newspaper_E+11 372,555 0.0728555 0.0740657 Newspaper_E+12 372,555 -0.0937476 0.0746295 Newspaper_E+13 372,555 0.1830571 0.2807927 Newspaper_E+14 372,555 0.1633205 0.1165165 Television_E-14 372,555 Television_E-13 372,555 Television_E-12 372,555 Television_E-11 372,555 Television_E-10 372,555 Television_E-9 372,555 Television_E-8 372,555 Television_E-7 372,555 Television_E-6 372,555 -0.0525959 0.0862299 Television_E-5 372,555 0.0360885 0.070315 Television_E-4 372,555 -0.1929947 0.1498996 Television_E-3 372,555 -0.0532616 0.0509374 Television_E-2 372,555 -0.0115961 0.0252818 Television_E-1 372,555 0.0191007 0.013767 Television_Execution Day 372,555 -0.0028216 0.0110777 Television_E+1 372,555 -0.0129687 0.0336746 Television_E+2 372,555 0.0337769 0.1026637 Television_E+3 372,555 0.0399764 0.0492671 Television_E+4 372,555 Television_E+5 372,555 Television_E+6 372,555 Television_E+7 372,555 Television_E+8 372,555 Television_E+9 372,555
110 Table 11 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Television_E+10 372,555 Television_E+11 372,555 Television_E+12 372,555 Television_E+13 372,555 Television_E+14 372,555 Demographic Variable State Resident Population 372,555 6.58e-08*** 3.26e-09 6.58e-08*** 3.26e-09 Non-Capital Punishment Variables State Prison Population (Number) 372,555 -5.77e-06*** 2.21e-07 -5.78e-06*** 2.21e-07 Active Death Penalty Statutes 372,555 -0.2798793*** 0.0128167 -0.2797595*** 0.0128157 Temporal Control Variables Sunday Dummy 372,555 0.2722259*** 0.0061927 0.2722782*** 0.0062677 Monday Dummy 372,555 0.0381943*** 0.0065521 0.0381472*** 0.0066017 Tuesday Dummy 372,555 0.0124412* 0.0065616 0.0115793* 0.0065908 Wednesday Dummy (omitted) 372,555 Thursday Dummy 372,555 0.013357** 0.0065257 0.0126834** 0.006542 Friday Dummy 372,555 0.1276198*** 0.0064052 0.127245*** 0.0064346 Saturday Dummy 372,555 0.3677989*** 0.0060931 0.3675531*** 0.0061364 January Dummy 372,555 -0.0080286 0.008454 -0.0083689 0.0084904 February Dummy (omitted) 372,555 March Dummy 372,555 -0.0164594** 0.0083428 -0.0158426** 0.0083599 April Dummy 372,555 -0.0162311 0.0086161 -0.0145205 0.008648 May Dummy 372,555 -0.00843 0.008436 -0.0075704 0.0084662 June Dummy 372,555 0.033873*** 0.0083123 0.0342704*** 0.0083259 July Dummy 372,555 0.0849879*** 0.0083005 0.0854204*** 0.0083121 August Dummy 372,555 0.1100534*** 0.0081285 0.1104279*** 0.0081411 September Dummy 372,555 0.0627385*** 0.0084023 0.0633486*** 0.0084131 October Dummy 372,555 0.0356425*** 0.0082533 0.0358475*** 0.0082645 November Dummy 372,555 0.0158957*** 0.0084919 0.0161648*** 0.0085016 December Dummy 372,555 0.0333395*** 0.0083967 0.0336436*** 0.0084128 Year Dummy-1979 372,555 -0.10529*** 0.0111544 -0.1051526** 0.0112331 Year Dummy-1980 372,555 -0.0363877** 0.0109758 -0.0358868*** 0.0110547 Year Dummy-1981 372,555 -0.0599598*** 0.010977 -0.0594519*** 0.0110555 Year Dummy-1982 372,555 -0.1141438*** 0.011021 -0.1140546*** 0.0110951 Year Dummy-1983 372,555 -0.2178601*** 0.0112071 -0.218142*** 0.0112776 Year Dummy-1984 372,555 -0.2420484*** 0.0112251 -0.2417733*** 0.0112922 Year Dummy-1985 372,555 -0.2343122*** 0.0111755 -0.2333903*** 0.0112323 Year Dummy-1986 372,555 -0.1429079*** 0.0109194 -0.1422474*** 0.0109818 Year Dummy-1987 372,555 -0.1690547*** 0.0109348 -0.1684178*** 0.0109901 Year Dummy-1988 372,555 -0.1264459*** 0.0107878 -0.1260527*** 0.0108573 Year Dummy-1989 372,555 -0.0808057*** 0.0106296 -0.0806215*** 0.01071 Year Dummy-1990 372,555 0.0101991 0.0103667 0.0107238 0.0104175 Year Dummy-1991 372,555 0.0802858*** 0.0101943 0.0808523*** 0.0102573 Year Dummy-1992 372,555 0.0407984*** 0.0102337 0.0427725*** 0.0103082 Year Dummy-1993 372,555 0.0738874*** 0.0101385 0.0742591*** 0.0101912 Year Dummy-1994 372,555 0.051651*** 0.0101672 0.05261*** 0.0102188 Year Dummy-1995 (omitted) 372,555 Year Dummy-1996 372,555 -0.0611396*** 0.0105144 -0.060575*** 0.0105569 Year Dummy-1997 372,555 -0.1079676*** 0.0106565 -0.1076749*** 0.0107091 Year Dummy-1998 372,555 -0.1887431*** 0.010886 -0.1889605*** 0.0109865
111 Table 11 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors New Year Dummy 372,555 0.6423056*** 0.0256152 0.6433079*** 0.0256449 New Year Lag 372,554 0.0229636 0.0324445 0.0237826 0.0324546 Good Friday 372,555 0.0646248** 0.0319976 0.074106** 0.0330154 Good Friday Lag 372,554 -0.0088618 0.0298336 -0.0134907 0.0302789 Easter 372,555 -0.0169527 0.0310217 -0.0102238 0.0314038 Easter Lag 372,554 -0.0277956 0.0343729 -0.0343755 0.0346246 Memorial Day 372,555 0.0457972 0.0334077 0.0452745 0.0334174 Memorial Day Lag 372,554 0.0698714** 0.0332498 0.06923** 0.0332991 Independence Day 372,555 0.2272125*** 0.0285155 0.2284009*** 0.0285262 Independence Day Lag 372,554 0.0852257** 0.0301035 0.0852463** 0.0301039 Labor Day 372,555 0.1675053*** 0.030886 0.1672366*** 0.0308841 Labor Day Lag 372,554 0.0838677** 0.0322876 0.0839189** 0.0323446 Thanksgiving Day 372,555 0.1741531*** 0.0318986 0.1748267*** 0.0319014 Thanksgiving Day Lag 372,554 0.0556845** 0.0319203 0.0560567** 0.0319208 Christmas Day 372,555 0.1628133*** 0.0301008 0.163113*** 0.0301018 Christmas Day Lag 372,554 -0.0888218** 0.0331398 -0.0885726** 0.0331407 Geographical Control Variables Alabama 372,555 -0.6347359*** 0.0682857 -0.6354841*** 0.0682729 Alaska 372,555 -3.189973*** 0.0863876 -3.190721*** 0.0863742 Arizona 372,555 -1.009264*** 0.0700491 -1.01002*** 0.0700362 Arkansas 372,555 -1.287246*** 0.0731629 -1.288042*** 0.0731495 California (omitted) 372,555 Colorado 372,555 -1.585977*** 0.0704676 -1.586774*** 0.0704548 Connecticut 372,555 -1.774928*** 0.0718018 -1.775703*** 0.0717889 Delaware 372,555 -3.135647*** 0.0855115 -3.136507*** 0.0854984 Washington DC 372,555 -1.175481*** 0.0809102 -1.176229*** 0.0808956 Florida 372,555 -0.0115509 0.0456895 -0.0121692 0.0456809 Georgia 372,555 -0.3046811*** 0.0620013 -0.3054838*** 0.0619898 Hawaii 372,555 -3.199877*** 0.0846215 -3.200607*** 0.0846084 Idaho 372,555 -3.210612*** 0.0845561 -3.211467*** 0.0845434 Illinois 372,555 -0.1794807*** 0.0457786 -0.1800939*** 0.0457702 Indiana 372,555 -1.07927*** 0.0634537 -1.080169*** 0.063442 Iowa 372,555 -2.99766*** 0.0779731 -2.998364*** 0.0779607 Kansas 372,555 -2.100921*** 0.0756961 -2.101643*** 0.075683 Kentucky 372,555 -1.344758*** 0.0689627 -1.345518*** 0.0689501 Louisiana 372,555 -0.3193686*** 0.0672562 -0.3200875*** 0.0672434 Maine 372,555 -3.730685*** 0.0884838 -3.731419*** 0.0884714 Maryland 372,555 -0.7156872*** 0.0667756 -0.7163904*** 0.0667632 Massachusetts 372,555 -1.877657*** 0.0643673 -1.878289*** 0.0643559 Michigan 372,555 -0.5298361*** 0.0565042 -0.5302582*** 0.0564941 Minnesota 372,555 -2.415474*** 0.0706129 -2.416098*** 0.070601 Mississippi 372,555 -0.9259273*** 0.0721056 -0.9267285*** 0.0720923 Missouri 372,555 -0.718634*** 0.0649151 -0.7195417*** 0.0649031 Montana 372,555 -3.114657*** 0.0844062 -3.115516*** 0.0843933 Nebraska 372,555 -2.781588*** 0.0796988 -2.782467*** 0.079686 Nevada 372,555 -1.758085*** 0.0777064 -1.758929*** 0.0776925 New Hampshire 372,555 -3.836293*** 0.0904472 -3.837077*** 0.0904351 New Jersey 372,555 -1.161299*** 0.0576135 -1.161893*** 0.0576028 New Mexico 372,555 -1.662575*** 0.0760707 -1.663405*** 0.076057 New York 372,555 -0.2500847*** 0.0324291 -0.2502893*** 0.0324233
112 Table 11 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors North Carolina 372,555 -0.4728577*** 0.0611308 -0.4735221*** 0.0611193 North Dakota 372,555 -4.410759*** 0.0999825 -4.411501*** 0.0999711 Ohio 372,555 -0.8443603*** 0.0489815 -0.8448876*** 0.0489723 Oklahoma 372,555 -1.186472*** 0.0709682 -1.187222*** 0.0709553 Oregon 372,555 -1.911282*** 0.0726333 -1.912078*** 0.0726205 Pennsylvania 372,555 -0.761851*** 0.0442552 -0.7623715*** 0.0442469 Rhode Island 372,555 -3.249858*** 0.0851367 -3.250626*** 0.0851236 South Carolina 372,555 -0.9458015*** 0.0705449 -0.9465903*** 0.0705317 South Dakota 372,555 -3.66856*** 0.0905643 -3.669418*** 0.0905521 Tennessee 372,555 -0.6849323*** 0.0649768 -0.6856482*** 0.0649024 Texas 372,555 0.238259*** 0.0345768 0.2377664*** 0.03457 Utah 372,555 -2.666971*** 0.0785917 -2.66785*** 0.0785787 Vermont 372,555 -4.436591*** 0.1009333 -4.437338*** 0.1009218 Virginia 372,555 -0.7912539*** 0.0622138 -0.792001*** 0.0622021 Washington 372,555 -1.460409*** 0.0658365 -1.461165*** 0.0658247 West Virginia 372,555 -2.310058*** 0.0781232 -2.310771*** 0.0781099 Wisconsin 372,555 -2.011673*** 0.0685822 -2.012272*** 0.0685704 Wyoming 372,555 -3.669727*** 0.0913224 -3.6728958*** 0.0913101 P-values: * p< 0.10; ** p< 0.05; *** p< 0.01 Our data show that a significant number of executions (271 out of the original executions of 499 that were actually carried out between 1979 and 1998) very closely overlap with each other. To overcome this overlap problem, we would delete all days in either of the two 4-week periods in the same state, if two periods overlap. For example, suppose that Texas carried out one execution on January 16, 1995 and another on February 8, 1995. The 4-week periods surrounding these 2 executions would be January 2 to 30, 1995 and January 21 to February 22, 1995. Thus, these executions would be omitted from the sample. For this supplementary analysis, 45.69 (228) percent of the original executions of 499 are retained. Table 12 represents the results of a negative binomial regression analytical model in which lead and lag effects as long as two weeks were considered, without any overlaps of the 4- week periods. Only two execution variables (“E+8” and “E+12”) are statistically significant at the 0.05 level. The estimated coefficient of the “E+8” variable is 0.1298235 and the estimated coefficient of the “E+12” variable is 0.0946076. This pattern of estimated “deterrent effects” of execution is quite different from the pattern of the “deterrent effects” of execution in the original model shown in Table 6. In other words, the deterrent effect of execution disappears. Thus, the negative binomial regression results of this sensitivity test is not robust, depending on the model specification. This may occur either because too many execution cases are omitted from the sample or because execution actually has no deterrent effect on homicides.
113 Table 12. Negative Binomial Regression Models w/o Overlaps of 4-Week Periods of Executions Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors E-14 372,541 0.0040361 0.0478927 0.0061497 0.0479232 E-13 372,542 0.0125118 0.0460673 0.0074185 0.0463476 E-12 372,543 -0.0398496 0.0462343 -0.0405962 0.0462712 E-11 372,544 0.0350943 0.0442264 0.0371813 0.044254 E-10 372,545 -0.0667558 0.0462565 -0.0675597 0.0463741 E-9 372,546 0.0119129 0.0460769 0.009883 0.0461275 E-8 372,547 -0.0126537 0.0480663 -0.0159153 0.0481567 E-7 372,548 -0.0118707 0.0482386 -0.014877 0.0486292 E-6 372,549 0.0357725 0.0455304 0.0368505 0.0457801 E-5 372,550 0.0238132 0.0448839 0.0222727 0.0452017 E-4 372,551 -0.0741507 0.0459806 -0.0828415 0.0461745 E-3 372,552 0.0331541 0.04436 0.0248361 0.0448337 E-2 372,553 -0.0807133 0.0480775 -0.0698873 0.0485874 E-1 372,554 0.0146 0.0477249 0.0118835 0.0483811 Execution Day_Supplementary 372,555 -0.0312294 0.0484702 -0.0360635 0.049318 E+1 372,554 0.0161757 0.0462423 0.0242667 0.0469035 E+2 372,553 -0.0163308 0.045607 -0.0163947 0.0457747 E+3 372,552 -0.0065094 0.0447049 0.0000229 0.0448151 E+4 372,551 -0.0215032 0.0453851 -0.018973 0.0454928 E+5 372,550 -0.0395403 0.047533 -0.038461 0.0475782 E+6 372,549 -0.0545405 0.0488693 -0.0582632 0.0490668 E+7 372,548 0.0138928 0.047658 0.0134204 0.0477305 E+8 372,547 0.1298235** 0.0440982 0.1267602** 0.0442603 E+9 372,546 0.0275521 0.0446627 0.0293663 0.0447569 E+10 372,545 0.0190799 0.0444121 0.0137451 0.0444359 E+11 372,544 0.03163 0.0446004 0.0313287 0.0446019 E+12 372,543 0.0946076** 0.0447613 0.0965096** 0.0448014 E+13 372,542 -0.0441281 0.0487122 -0.0442367 0.048716 E+14 372,541 -0.0266407 0.0485009 -0.0293072 0.0485358 Newspaper_E-14 372,555 -0.0901313 0.0823364 Newspaper_E-13 372,555 0.0465162 0.0511958 Newspaper_E-12 372,555 0.010521 0.0428199 Newspaper_E-11 372,555 -0.0177912 0.0325511 Newspaper_E-10 372,555 -0.0112719 0.0505688 Newspaper_E-9 372,555 0.0313427 0.0300198 Newspaper_E-8 372,555 0.0284907 0.0268943 Newspaper_E-7 372,555 0.0128744 0.0294078 Newspaper_E-6 372,555 -0.0003251 0.0217071 Newspaper_E-5 372,555 -0.0026438 0.0222063 Newspaper_E-4 372,555 -0.0008911 0.0173293 Newspaper_E-3 372,555 0.0353843 0.0240386 Newspaper_E-2 372,555 -0.0191788 0.0159448 Newspaper_E-1 372,555 -0.0034084 0.010236 Newspaper_Execution Day 372,555 0.0026554 0.0063407 Newspaper_E+1 372,555 -0.0033342 0.0037989 Newspaper_E+2 372,555 -0.0009308 0.0100072 Newspaper_E+3 372,555 -0.0405985** 0.0190494
114 Table 12 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Newspaper_E+4 372,555 -0.0213292 0.0235127 Newspaper_E+5 372,555 -0.0041594 0.0225334 Newspaper_E+6 372,555 0.0361136 0.0467393 Newspaper_E+7 372,555 0.0240292 0.0605784 Newspaper_E+8 372,555 0.0600634 0.0784479 Newspaper_E+9 372,555 -0.0361789 0.0617029 Newspaper_E+10 372,555 0.2255789** 0.0654333 Newspaper_E+11 372,555 0.0727934 0.0740833 Newspaper_E+12 372,555 -0.0986632 0.0746859 Newspaper_E+13 372,555 0.1892393 0.2810405 Newspaper_E+14 372,555 0.1671313 0.1166918 Television_E-14 372,555 Television_E-13 372,555 Television_E-12 372,555 Television_E-11 372,555 Television_E-10 372,555 Television_E-9 372,555 Television_E-8 372,555 Television_E-7 372,555 Television_E-6 372,555 -0.053591 0.0862473 Television_E-5 372,555 0.0330246 0.0703098 Television_E-4 372,555 -0.1919485 0.1498386 Television_E-3 372,555 -0.04936684 0.0510203 Television_E-2 372,555 -0.0115387 0.025282 Television_E-1 372,555 0.0194423 0.0137618 Television_Execution Day 372,555 -0.0025401 0.0110846 Television_E+1 372,555 -0.012388 0.0336785 Television_E+2 372,555 0.0337901 0.1026865 Television_E+3 372,555 0.0400665 0.0492805 Television_E+4 372,555 Television_E+5 372,555 Television_E+6 372,555 Television_E+7 372,555 Television_E+8 372,555 Television_E+9 372,555 Television_E+10 372,555 Television_E+11 372,555 Television_E+12 372,555 Television_E+13 372,555 Television_E+14 372,555 Demographic Variable State Resident Population 372,555 6.58e-08*** 3.26e-09 6.58e-08*** 3.26e-09 Non-Capital Punishment Variables State Prison Population (Number) 372,555 -5.81e-06*** 2.21e-07 -5.82e-06*** 2.21e-07 Active Death Penalty Statutes 372,555 -0.2789597*** 0.0128135 -0.2788729*** 0.0128127 Temporal Control Variables Sunday Dummy 372,555 0.272631*** 0.0062114 0.2723719*** 0.0062821 Monday Dummy 372,555 0.0387675*** 0.0065642 0.0384333*** 0.006611 Tuesday Dummy 372,555 0.0128253* 0.0065676 0.011854* 0.0065953 Wednesday Dummy (omitted) 372,555
115 Table 12 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Thursday Dummy 372,555 0.0132266** 0.0065321 0.012625** 0.0065474 Friday Dummy 372,555 0.1276323*** 0.0064167 0.1272011*** 0.0064442 Saturday Dummy 372,555 0.3677885*** 0.0061116 0.3673881*** 0.0061519 January Dummy 372,555 -0.0077934 0.0084559 -0.0080252 0.008492 February Dummy (omitted) 372,555 March Dummy 372,555 -0.0167508** 0.0083435 -0.0161626** 0.0083607 April Dummy 372,555 -0.0166112** 0.0086166 -0.0147571** 0.0086488 May Dummy 372,555 -0.0094469 0.0084344 -0.0083825 0.0084658 June Dummy 372,555 0.0335403*** 0.0443086 0.0339606*** 0.0083262 July Dummy 372,555 0.0849096*** 0.0083008 0.0854003*** 0.0083124 August Dummy 372,555 0.1100192*** 0.0081289 0.1103769*** 0.0081415 September Dummy 372,555 0.062048*** 0.0084033 0.0626663*** 0.0084142 October Dummy 372,555 0.0361211*** 0.0082531 0.0363052*** 0.0082643 November Dummy 372,555 0.0157589* 0.0084922 0.0159421* 0.0085019 December Dummy 372,555 0.0331297*** 0.0083971 0.0334628*** 0.0084133 Year Dummy-1979 372,555 -0.103712*** 0.0111664 -0.1039987*** 0.0112466 Year Dummy-1980 372,555 -0.0347067** 0.0109876 -0.0347394** 0.0110678 Year Dummy-1981 372,555 -0.0582353*** 0.0109884 -0.0582578*** 0.0110683 Year Dummy-1982 372,555 -0.112478*** 0.0110293 -0.1128752*** 0.011105 Year Dummy-1983 372,555 -0.2163029*** 0.0112131 -0.2170143*** 0.0112851 Year Dummy-1984 372,555 -0.2417406*** 0.0112284 -0.2417117*** 0.0112958 Year Dummy-1985 372,555 -0.2337279*** 0.011178 -0.2331622*** 0.0112349 Year Dummy-1986 372,555 -0.1423727*** 0.0109303 -0.1420718*** 0.0109918 Year Dummy-1987 372,555 -0.1684183*** 0.0109413 -0.168146*** 0.0109962 Year Dummy-1988 372,555 -0.1251112*** 0.0107877 -0.125172*** 0.0108594 Year Dummy-1989 372,555 -0.0795644*** 0.0106276 -0.0797523*** 0.0107106 Year Dummy-1990 372,555 0.0111637 0.0103688 0.011448 0.0104204 Year Dummy-1991 372,555 0.0815932*** 0.0101928 0.0817522*** 0.010258 Year Dummy-1992 372,555 0.0412737*** 0.0102358 0.04328*** 0.0103109 Year Dummy-1993 372,555 0.0742386*** 0.0101407 0.0743876*** 0.0101935 Year Dummy-1994 372,555 0.0525497*** 0.0101703 0.0533266*** 0.0102225 Year Dummy-1995 (omitted) 372,555 Year Dummy-1996 372,555 -0.0601107*** 0.0105157 -0.0597377*** 0.0105551 Year Dummy-1997 372,555 -0.1077681*** 0.0106583 -0.1075519*** 0.010711 Year Dummy-1998 372,555 -0.1887376*** 0.0108868 -0.1890601*** 0.010988 New Year Dummy 372,555 0.6438989*** 0.0256211 0.6445224*** 0.025651 New Year Lag 372,554 0.021601 0.0324843 0.0220999 0.0324945 Good Friday 372,555 0.0649257** 0.0319999 0.0740052** 0.0330222 Good Friday Lag 372,554 -0.0089175 0.0298398 -0.0129279 0.0302838 Easter 372,555 -0.0164352 0.0310229 -0.0099389 0.0314055 Easter Lag 372,554 -0.0276632 0.0343803 -0.0334496 0.0346287 Memorial Day 372,555 0.0456012 0.0334146 0.0447846 0.0334243 Memorial Day Lag 372,554 0.0708011** 0.0332542 0.0702363** 0.0333036 Independence Day 372,555 0.2282248*** 0.0285167 0.2290589*** 0.0285277 Independence Day Lag 372,554 0.0852322*** 0.0301058 0.0850505*** 0.0301062 Labor Day 372,555 0.1677066*** 0.0308887 0.1674313*** 0.0308867 Labor Day Lag 372,554 0.0845651*** 0.0322882 0.0844297*** 0.0323448 Thanksgiving Day 372,555 0.1749715*** 0.0319017 0.1752936*** 0.0319046 Thanksgiving Day Lag 372,554 0.0555511* 0.0319237 0.0557443* 0.0319242 Christmas Day 372,555 0.1632746*** 0.0301044 0.1633502*** 0.0301057
116 Table 12 - Continued Variables Obs. Model w/o News Variables Model with News Variables Christmas Day Lag 372,554 -0.0872206** 0.033138 -0.0872336** 0.0331393 Geographical Control Variables Alabama 372,555 -0.6370843*** 0.0684047 -0.6375742*** 0.0683923 Alaska 372,555 -3.190355*** 0.0864763 -3.19086*** 0.0864633 Arizona 372,555 -1.011143*** 0.070157 -1.011645*** 0.0701444 Arkansas 372,555 -1.289437*** 0.0732685 -1.289906*** 0.0732552 California (omitted) 372,555 Colorado 372,555 -1.587326*** 0.0705567 -1.587871*** 0.0705442 Connecticut 372,555 -1.776096*** 0.0718901 -1.776625*** 0.0718776 Delaware 372,555 -3.137526*** 0.0856142 -3.138102*** 0.0856014 Washington DC 372,555 -1.175743*** 0.081006 -1.176252*** 0.0809919 Florida 372,555 -0.0149064 0.0458027 -0.0152483 0.0457944 Georgia 372,555 -0.3070142*** 0.0621029 -0.3075575*** 0.0620917 Hawaii 372,555 -3.200282*** 0.0847076 -3.200775*** 0.0846949 Idaho 372,555 -3.212039*** 0.084647 -3.212619*** 0.0846345 Illinois 372,555 -0.1811299*** 0.045845 -0.1815373*** 0.0458366 Indiana 372,555 -1.080889*** 0.0635431 -1.081546*** 0.0635317 Iowa 372,555 -2.998089*** 0.0780526 -2.998551*** 0.0780405 Kansas 372,555 -2.10149*** 0.0757827 -2.101978*** 0.0757699 Kentucky 372,555 -1.346111*** 0.0690506 -1.346626*** 0.0690383 Louisiana 372,555 -0.3218405*** 0.0673673 -0.3223027*** 0.0673549 Maine 372,555 -3.731132*** 0.0885649 -3.731625*** 0.0885529 Maryland 372,555 -0.7168835*** 0.0668663 -0.7173525*** 0.0668541 Massachusetts 372,555 -1.878275*** 0.0644359 -1.878699*** 0.0644248 Michigan 372,555 -0.5296544*** 0.0565636 -0.5299345*** 0.056554 Minnesota 372,555 -2.416*** 0.0706874 -2.416412*** 0.0706757 Mississippi 372,555 -0.9274419*** 0.0722049 -0.9279835*** 0.0721918 Missouri 372,555 -0.7219097*** 0.0650227 -0.7224978*** 0.0650109 Montana 372,555 -3.11614*** 0.0845 -3.116722*** 0.0844872 Nebraska 372,555 -2.783182*** 0.079794 -2.783758*** 0.0797812 Nevada 372,555 -1.759744*** 0.0778123 -1.760313*** 0.0777987 New Hampshire 372,555 -3.837111*** 0.0905291 -3.83764*** 0.0905172 New Jersey 372,555 -1.162306*** 0.0576828 -1.162702*** 0.0576724 New Mexico 372,555 -1.663872*** 0.0761659 -1.664436*** 0.0761525 New York 372,555 -0.2497911*** 0.0324533 -0.2499329*** 0.0324479 North Carolina 372,555 -0.4746514*** 0.0612286 -0.4750784*** 0.0612175 North Dakota 372,555 -4.411207*** 0.1000578 -4.411704*** 0.1000466 Ohio 372,555 -0.8451766*** 0.0490393 -0.8455364*** 0.0490303 Oklahoma 372,555 -1.188508*** 0.0710748 -1.188969*** 0.071062 Oregon 372,555 -1.912735*** 0.0727254 -1.913275*** 0.0727128 Pennsylvania 372,555 -0.7632114*** 0.0443086 -0.7635425*** 0.0443002 Rhode Island 372,555 -3.250412*** 0.0852219 -3.250933*** 0.0852092 South Carolina 372,555 -0.9481731*** 0.0706566 -0.9486918*** 0.0706439 South Dakota 372,555 -3.669901*** 0.0906497 -3.670484*** 0.0906377 Tennessee 372,555 -0.6861653*** 0.0649966 -0.6866455*** 0.0649847 Texas 372,555 0.2300207*** 0.0346319 0.2297719*** 0.0346255 Utah 372,555 -2.668654*** 0.0786887 -2.669246*** 0.078676 Vermont 372,555 -4.43702*** 0.1010086 -4.437523*** 0.1009975 Virginia 372,555 -0.7964079*** 0.0623468 -0.7968246*** 0.0623356 Washington 372,555 -1.461915*** 0.0659231 -1.462419*** 0.0659114 West Virginia 372,555 -2.310523*** 0.0782096 -2.310985*** 0.0781965
117 Table 12 - Continued Variables Obs. Model w/o News Variables Model with News Variables Independent Variables of Interest Coefficients Std. Errors Coefficients Std. Errors Wisconsin 372,555 -2.012075*** 0.0686562 -2.01247*** 0.0686446 Wyoming 372,555 -3.66943*** 0.091411 -3.670019*** 0.0913989 P-values: * p< 0.10; ** p< 0.05; *** p< 0.01
118 CHAPTER 6
CONCLUSIONS
This chapter provides a summary of the study presented in this dissertation, which was conducted to measure the short‐term effect of executions on homicides in the United States between January 1, 1979 and December 31, 1998. The first section of the chapter provides a brief summary of the present study’s key findings, and the findings are compared and contrasted with the results of previous studies. This section also discusses the advantages of the present study. The second section examines the theoretical and policy implications of the study’s findings. The third section addresses the study’s limitations and proposes recommendations for future research. A Summary of Empirical Findings This study reveals a statistically significant deterrent effect of executions on homicides on the day of an execution. Although this study found apparent deterrent effects of execution on the days 5 and 6 days afterward, these do not appear to be genuine effects. This pattern of the deterrent effects has nothing to do with the patterns of newspaper and television coverage of executions. Also, this study finds no scientific evidence of a brutalization effect of executions on homicides. Therefore, it can be concluded that executions do affect the behavior of prospective killers, but only for a very brief period of time in a modest way. Overall, the empirical evidence from the present study is different from the findings of many previous death penalty studies because the deterrent effect of executions is so small and short-lived that it could not detected in previous studies that used yearly and monthly aggregated data (Donohue and Wolfers, 2005). However, the particular pattern of apparent deterrent “effects” reported in the present study is not found even in some of the prior studies that employed daily data (Grogger, 1990; Hjalmarsson, 2009). The present study improves four aspects of prior research by adopting more sophisticated methodological approaches. First, this is the first study to cover a large daily sample period and a large geographical area, which results in a much larger sample size (N=372,555 cases and 499 executions) than any of the previously published studies. Because the present study employs
119 daily disaggregated data at the state level, it naturally has a larger sample size than prior studies employing annually and monthly aggregated data at the state level. Although Shepherd’s study (2005) employed longer sample periods than the present study’s, using state-level annual data between 1960 and 2000 (N=2,040 cases) and state-level monthly data between 1977 and 1999 (N=13,464 cases), the sample sizes are much smaller than the present study’s. The benefit achieved from using large sample also applies to prior studies employing daily disaggregated data. For example, Phillips and Hensley (1984) used data covering the whole United States but for a short time period (1973 to 1979). Hjalmarsson (2009) covered three metropolitan cities in Texas (Houston, San Antonio, and Dallas) during a relatively recent time period (1999 to 2004). Grogger (1990) used daily data to estimate the deterrent effect of publicized executions on homicides, but he covered only California, and only for 1960 to 1963. However, the present study’s findings about the deterrent effect of executions on homicides are based on more precise estimates and nationally generalizable results than previous studies. Secondly, using daily disaggregated homicide data enables researchers to observe an extremely small short-lived effects of executions on homicides. In a highly temporally disaggregated study, it is possible to distinguish between a true deterrent effect caused by publicity immediately before and after an execution and a false deterrent effect caused by other factors. Like several previous studies using daily disaggregated data (Grogger, 1990; Phillips and Hensley, 1984; Phillips, 1980), the present study distinguishes the true deterrent effect of executions occurring during the period immediately surrounding the execution from the effects of random fluctuations occurring at more remote time periods. Third, the present study attempts to overcome one of the major limitations of previous studies that ignores the distinction between the deterrent effect of the death penalty and the incapacitative effect of punishment. The National Research Council has long recommended that the deterrent effect of the death penalty should be distinguished from the incapacitative effect of imprisonment (Klein, Forst, and Filitov, 1978). However, only some studies to date have attempted to incorporate this recommendation into their research strategy. The present study, on the other hand, provides solid evidence for the deterrent effect of executions independent of the incapacitative effect of daily state prisoner counts. Last, homicide follows strong and consistent seasonal patterns. For example, homicides tend to decrease in cold weather and in warm and hot weathers, on weekends, and during holiday
120 seasons. Some prior studies employing daily aggregated data have been criticized for their failure to include particular temporal dummy variables, which could account for their reported detection of a deterrent effect of the death penalty on homicides (for example, Grogger, 1990; McFarland, 1983). In contract, the present study employs a more complete set of temporal dummy variables including years, months, weeks, and national public holiday periods. Because this study controls for temporal variations in homicide, it is able to isolate deterrent effects of executions. Theoretical Implications The present study highlights several important theoretical implications regarding capital punishment’s general deterrent effect on homicides. It seems clear that evidence from the present study at least partially fulfills some theoretical rationales underlying general deterrence and capital punishment, but also falls short of satisfying other rationales. Although executions do affect the behavior of prospective killers, they do so only for a brief period of time: the day of an execution. However, no statistically significant deterrent effect was found on the first through the fourth days after an execution, nor on days before executions. This study provides a theoretical explanation for why previous studies employing longer time units have failed to provide solid evidence in support of the deterrent effect of the death penalty on homicides in the United States – the effects are too short-lived to show up in such studies. This study also found that there are no deterrent effects of execution on the days 1 to 4 days after an execution, while there are apparent deterrent effects of execution on the 5 and 6 days after an execution. There is no deterrence theory to predict such a pattern. In other words, this evidence is not consistent with deterrence theory. This could be explained because there is no correlation between perceptions of legal punishment risks and actual punishment levels, leading to the overall conclusion that increases in punishment levels usually do not reduce crimes through the general deterrent effects (Kleck, Sever, Li, and Gertz, 2005). On the other hand, this study finds no statistically significant evidence for the brutalization effect of executions on homicides over an extremely short period of time. However, it would be premature to conclude from the scientific evidence presented here that executions unequivocally have no brutalization effect on homicides. The possibility remains that a long- term cumulative effect of many executions may exist but be undetectable by the data or the statistical analytical methods used here. For example, some of the previous studies employing monthly and weekly aggregated data reported evidence of a relatively long-term brutalization
121 effect of executions on homicides (Bowers and Piece, 1980; Cochran, Chamlin, and Seth, 1994; Thompson 1997, 1999). One piece of information suggests a genuine deterrent effect of executions on homicides: homicide counts go down a little bit on the day of execution. It may not really reflect people who are prevented from committing homicides. Rather, it may only delay or postpone homicides. It is always possible that those people might have done homicides later. Generally speaking, the present study did not find any significant deterrent effects of executions on homicides a few days after executions. Therefore, we do not need to worry about being confused with nearly delaying homicide. Although Gibbs (1975) argued that executions will avert prospective offenders from committing murders, only if the deterrence messages about executions are communicated to the public audience mainly through a variety of means, the present study does not support a deterrent effect of publicity about executions. There were no statistically significant deterrent effects of television and newspaper coverage of executions on homicides. There is at least one possible explanation for the lack of evidence demonstrating that newspaper and television coverage deters homicides. For a deterrent effect to occur, the target audience (prospective murderers) must receive enough information about executions to cause them to update their perceived risks of that punishment. But, mass media does not disseminate information about executions to the target audience in the most efficient and effective fashion (Hjalmarsson, 2009). The findings from the present study do not support the conclusion that newspaper and television coverage of executions provides an adequate foundation for forming an accurate perceptions of the deterrent effect of the death penalty. However, it is with precaution to conclude that the general deterrence theory is premature, as other sources of information, such as the Internet, radio, and personal experience of active criminal and his friends and associates, may have a significant influence on the perceptions of the risk of the death penalty and change the behavior of prospective murderers (Cook, 1980; Tittle, 1980; Zimring and Hawkins, 1973). Our findings do not support the general deterrence proposition that the deterrent effect of executions on homicides becomes stronger as the execution day approaches, due to growing media coverage (for instance, Hjalmarsson, 2009; McFarland, 1983; Phillips, 1980; Phillips and Hensley, 1984). The news reports about incoming executions printed and broadcast by mass media do significantly increases a few days before the date of execution, yet this increasing
122 amount of media coverage of executions does not appear to cause corresponding increases in the deterrent effect of the death penalty other than an the day of an execution. The National Research Council has pointed out that the incapacitative effect of imprisonment can be confused with the deterrent effect of executions (Klein, Forst, and Filitov, 1978). The present research avoids this problem by incorporating the estimated daily state prison populations into the multivariate analytical model, enabling us to separate the possible deterrent effect of executions on homicides from the incapacitative effect of imprisonment. The statistical evidence of a deterrent effect of executions on homicides on the day of executions remains robust even though the estimated daily state-level prison population variable is controlled. This study suggests that a modest short-term deterrent effect of the death penalty on homicides coexists with the incapacitative effect of prison sentences on homicides. Policy Implications The evidence presented here, which is based on a far more fine-grained temporal units than most previous studies, suggests that executions do cause the homicide rate to drop, but only to a very small degree – almost too small to be detected. It appears that, in the aggregate, the small number of executions carried out in a typical year in the United States has very little impact on the recent declines in number of homicides. The annual number of executions carried out in the United States has decreased substantially since 1999, when the total was 98. This trend of ever-decreasing execution rates means that the death penalty has had little to do with total homicide rates. If current trends continue, the death penalty may further lose its power to lower total homicide rates. The key finding in the present study – that a deterrence effect exists, but is very small in magnitude – does is not likely to satisfy conservative politicians or crime control policy makers who call for capital punishment to lower homicide rates, or citizens who demand measures to get tough on crime. The study instead generally supports proposals to abolish the death penalty because its deterrent effect is so small and to develop other crime control strategies. Limitation of the Study Although this study has several strengths in its methodology and analysis, it also has limitations that should be acknowledged. First, the data set cannot reflect the impact of executions on homicides in recent years, because the Centers for Disease Control’s (CDC’s) latest U.S. Mortality Detail File (MDF), with data from 1999 to the present, could not be
123 obtained. Therefore, the study period does not reflect trends in national homicide counts after year 1999. Unlike in the past years, the homicide rate fluctuated very slightly between 1999 and 2008, then steadily decreased in recent years. A second limitation of this study is that, we were unable to measure non‐capital punishment variables that may affect homicide counts independent of the deterrent effect of the death penalty. The National Academy of Sciences noted that for studies employing daily data; it is possible that deployment changes among law enforcement officers immediately before, during, and immediately after executions may also drive homicide rates to fluctuate, just as executions do (Nagin and Pepper, 2012). The National Academy of Sciences suggests that adding more relevant law enforcement variables that affect homicides to the multivariate regression equation would enable researchers to separate the deterrent effect of executions from the effects of non-law enforcement variables. This, of course, assumes the police deployment affects homicide. The National Academy of Sciences suggested that researcher needed to control for the incapacitative effects of imprisonment. In the present study we used the estimated daily state prison populations to separate the incapacitative effect of imprisonment from the deterrent effect of the death penalty on homicides. The results indicates that although their coefficients decrease by a small amount, some daily execution variables still remain statistically significant even after the estimated daily prison population count variable is included to the equation. Decreases in homicide rates before and after executions therefore cannot be attributed to fluctuations in the number of people imprisoned. A possible explanation of the result is that the state prison population changes very little on a daily basis so the death penalty has a statistically significant direct effect on homicides, independent of the incapacitative effect of imprisonment. For the same reason, it is unlikely that changes in daily law enforcement deployments immediately before and after executions would cause significant changes in daily homicide counts during these periods. The third limitation of the present study is regarding an indirect measure of the perceptions of the risk of the death penalty among potential murderers. Although potential offenders’ perceptions of the risks of the death penalty play an important role in general deterrence theory, potential murderers’ risk perceptions of the death penalty cannot be directly measured in macro-level research. The present study sought to overcome this limitation by
124 employing indirect measures of the perceptions of the death penalty, such as newspaper and television news coverage of executions on the assumption that perceived risk of executions covaries with the volume of news stories about executions. Nevertheless, many sources of information were not considered. For example, we did not take account of local television news coverage of executions, a source that was used in Hjalmarsson’s (2009) study. Furthermore, prospective murderers update their knowledge about execution levels through other information sources, such as the Internet, the radio, and personal acquaintances (Cook, 1980). Recommendations for Future Research This study’s limitations point to needed improvements in future research. First, it would be useful to include the time period from 1999 to the present, so as to provide a more recent sample. It is possible that results obtained from using the extended sample period would yield different results about the deterrent effect of the death penalty Second, data are needed about the coverage of executions by local television stations. Prior studies in this area have exclusively employed national television evening news coverage, which tends to be largely limited to especially newsworthy and unusual execution cases. Nearly all previous studies have ignored local television news coverage of executions. As Jacoby et al. (2008) argued, executions in one’s own state are more interesting to local television audiences and therefore receive more coverage than executions in distant states. This suggests that prospective killers would perceive the risks of each execution differently, depending on their proximity to the execution. If and when local television news archives becomes accessible in the future, researchers may be able to test any effects of local. Third, it may be worthwhile to test for differential short-term deterrent effects of the death penalty on homicides among sub-populations in the United States. For example, different racial groups may be differentially response to executions because the frequency of executions differs across racial groups. Mortality data by race are available for each of the 50 states, so it should be possible for future researchers to compare the deterrent effect of the death penalty on homicides involving victims of different races. Finally, future research could try to test for deterrent effects of executions on homicides in states other than the one in which the executions occurred. This study estimated within-state deterrent effect of executions on homicides. It is possible that prospective killers update their information on the perceived risks of execution based on information about executions in other
125 states. An execution in one state may affect the behavior of prospective killers in that state, but also in neighboring states, albeit more than the behavior of potential murderers in more distant states. For example, an execution carried out in Florida could influences the behavior of residents of Florida and its bordering states, such as Alabama and Georgia, though more than those who reside in remote states such as California or Washington. Conclusion One of the major limitations of previous studies is that they used aggregated annual and monthly counts of the number of homicides. The deterrent effect of the death penalty may be so short-lived that it is unlikely to be detected when using longer temporal units. To overcome the limitation of prior studies, the present study employs daily disaggregated counts of the number of homicides and finds that executions have a statistically significant but small deterrent effect on homicides the day of the execution, but its deterrent effect diminishes very soon after an execution. The present study discusses the theoretical and policy implications of these findings. With regard to the theoretical implication, the present study provides some limited support for the general deterrence theory of the death penalty. As for the policy implication, the present research suggests that use of the death penalty probably has very little aggregate impact on the total number of homicides. The empirical evidence from the present study could encourage politicians and crime control policymakers to reconsider the application of the death penalty as a deterrent to homicides in the United States.
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CASES CITED:
Fowler v. North Carolina. 1976. 428 U.S. 904. Gregg v. Georgia. 1976. 428 U.S. 153. Jurek v. Texas. 1975. 428 U.S. 262. Proffitt v. Florida. 1976. 428 U.S. 242. Roberts v. Louisiana. 1976. 428 U.S. 325. Woodson v. North Carolina. 1976. 428 U.S. 153
139 BIOGRAPHICAL SKETCH
The author holds a Bachelor of Arts degree in Public Administration from Gachon University (former, Kyungwon University) in South Korea and a Master of Arts degree in Criminal Justice and Criminology from Sam Houston State University in Huntsville, Texas. Moonki Hong will receive his Doctor of Philosophy in Criminology and Criminal Justice from Florida State University in spring 2016. While attending Florida State University, he worked as an OPS Government Operations Consultant II for the Florida Department of Juvenile Justice (DJJ) and had previously taught at different universities in Florida, Georgia, and Oklahoma. His research interests include deterrence, capital punishment, crime control policy, juvenile delinquency, and corrections/penology.
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