ABSTRACT 
 
 
Title of Document: WHAT IS THE PRICE OF CRIME? NEW 
ESTIMATES OF THE COST OF CRIMINAL 
VICTIMIZATION 
  
 Jonathan Kilbourn Roman, M.P.P., 1997 
Directed By: Professor Peter Reuter, School of Public Policy  
 
 
Robust estimates of the price of crime, measured as the costs of crime to victims, inform 
a wide range of policy analysis. The most commonly cited studies are constrained by 
limited data and rely on indirect methods to estimate prices.  In these studies, health 
statistics are used to estimate direct losses from crime, jury award data are used to 
estimate indirect damages from crime, and self-reported crime data are used to weight 
injury prevalence within broad crime categories.  While the relationship between injury 
and damages can be observed at the individual level in civil court records, individual 
level data have not previously been available that link crimes and injury.  Since both 
individual and aggregate data are combined in these studies, prior research has not 
corrected sampling bias, and the estimates of victimization costs have been reported only 
as point estimates without confidence intervals.  Estimates have been developed for only 
 
a few broad categories of crime and these estimates have not been robust to study design.
 This study analyzes individual-level data from two sources: jury award and injury 
data from the RAND Institute of Civil Justice and crime and injury data from the 
National Incident-Based Reporting System.  Propensity score weights are developed to 
account for heterogeneity in jury awards. Data from the jury awards are interpolated onto 
the NIBRS data based on the combination of all attributes observable in both data sets. 
From the combined data, estimates are developed of the price of crime to victims for 
thirty-one crime categories. Until data become available linking information about 
criminal incidents to jury award data, the strategy used here is likely to yield the most 
robust estimates of the costs to crime victims that can be generated from the jury 
compensation method. 
 
 
WHAT IS THE PRICE OF CRIME? NEW ESTIMATES OF THE COST OF 
CRIMINAL VICTIMIZATION 
 
 
By 
 
Jonathan Kilbourn Roman 
 
 
Dissertation submitted to the Faculty of the Graduate School of the  
University of Maryland, College Park, in partial fulfillment 
of the requirements for the degree of 
Ph.D. in Policy Studies 
2009 
 
 
 
Advisory Committee: 
Schelling Visiting Professor, Philip Cook 
Professor Peter Reuter, Chair 
Assistant Professor, Randi Hjalmarsson  
Professor, Raymond Paternoster 
William J. Sabol, Ph.D. 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
? Copyright by 
Jonathan Kilbourn Roman 
2009 
 
Dedication 
 
To: Mildred and Francis P. Roman 
John and Elizabeth Vance 
 
 
 
 
 
 
 
 
 
 
 
 
 ii
Acknowledgements 
Like any large research project this dissertation required the assistance of many others 
and the paper was substantially improved by their efforts. First, I would like to thank my 
committee for guiding me toward a project that was superior to the one I initially 
envisioned. Foremost, thanks to Peter Reuter for his endless patience, critical insights, 
and thoughtful prodding. Randi Hjalmarsson was always willing to discuss the project, 
and provided invaluable guidance on both methods and substance. Bill Sabol met with 
me on several occasions to talk about my project even before he joined my committee. 
Phil Cook pressed me to seriously address the limitations of the jury method in measuring 
victim costs from the perspective of neo-classical economic theory. Ray Paternoster 
provided a much needed criminological perspective that kept the project grounded.  
I wish to thank many others who volunteered their time to help me finish this 
paper.  Carly Knight, who was unfortunate enough to work across the hall from me, 
offered flawless technical assistance, and provided thoughtful comments in response to 
my nearly endless stream of methodological, substantive and metaphysical concerns. Eric 
Grodsky spent a good deal of Iowa and Nebraska discussing the relative merits of 
covariates versus propensity matching methods, among other esoterica, and for that and 
all the other ad hoc guidance I am grateful. I benefited greatly from working at the Urban 
Institute during the course of this research, and many of my colleagues supported this 
project. In particular, Aaron Chalfin, Bogdan Tereshchenko, Avi Bhati, Adele Harrell and 
Shelli Rossman all offered critical insights during this process. I am also particularly in 
debt to Nick Pace at the RAND Institute of Civil Justice, who was kind enough not only 
 iii
to share the jury data used in this analysis but to answer my queries?spread out over 
more than a year?about the data.   
If you are lucky, a dissertation turns into a labor of love. Either way, dissertation 
labors put an enormous strain on those you love. Over the last three decades, my father 
has probably used the phrase ?now that would make a great dissertation!? hundreds of 
times. So, Dad, here it is, and I thank you for your boundless intellectual curiosity, some 
of which I was fortunate enough to inherit. My mother has always been my role model, 
and I have tried to emulate her intelligence, persistence, dedication, and earnestness in 
approaching my work. I thank my brother Pete for being my rock and truly showing me 
what hard work is.  
And finally, to Caterina, my partner in crime and in life. You said if I should ever 
fall behind, you?d wait for me. I am so grateful you did.  
 iv
Table of Contents 
 
Chapter One: Developing Robust Estimates of the Price of Crime.................................... 1 
Why Robust Estimates of the Price of Crime are Important to Policy-Making ............. 4 
Research Applying Cost of Crime Estimates.................................................................. 9 
Limitations of Strategies to Estimate the Costs of Crime to Victims........................... 10 
Limitations of the Jury Award Method......................................................................... 13 
The Cohen, Miller Literature Using Jury Awards to Estimate Victim Costs ............... 15 
Modifying the Jury Award Method to Develop New Estimate of Costs to Crime 
Victims.......................................................................................................................... 18 
Jury Data ................................................................................................................... 19 
NIBRS Data .................................................................................................................. 20 
Methods......................................................................................................................... 22 
Interpolating the RAND data onto NIBRS ................................................................... 25 
Structure of the Dissertation ......................................................................................... 27 
Chapter Two: Review of Prior Research on the Price of Crime....................................... 29 
Applying the Law and Economics Literature to the Study of Crime ........................... 44 
Properties of a Good Price Estimator............................................................................ 45 
Costs to Society............................................................................................................. 48 
Contingent Valuation.................................................................................................... 57 
Jury Awards .................................................................................................................. 61 
Are Juries Objective Arbiters of Victim Losses? ......................................................... 71 
Prior Research............................................................................................................... 72 
 v
The Competency of the Civil Jury............................................................................ 75 
Jury Competency in Highly Complex Cases ............................................................ 77 
Are Jury Award?s for Damages Commensurate with the Facts of a Case?.............. 78 
Extra-Legal Factors in Jury Awards ............................................................................. 80 
Extra-Legal Considerations by Case Type ............................................................... 80 
Geographical and Temporal Factors......................................................................... 82 
Defendant Wealth Effects and the ?Deep Pockets? Hypothesis............................... 84 
Plaintiff Gender......................................................................................................... 88 
Defendant Culpability/Reprehensibility ................................................................... 90 
Race and Socio-Economic Status ............................................................................. 92 
Counting Property Losses............................................................................................. 93 
Risk of Death ................................................................................................................ 95 
Summary of Prior Research.......................................................................................... 98 
Chapter Three: Damages Awarded by Jury in Civil Cases............................................. 100 
Analysis Discussed in Chapter Three ......................................................................... 105 
Data............................................................................................................................. 105 
Definitions................................................................................................................... 106 
RAND Data Reduction ............................................................................................... 106 
Adjustments to the Dependent Variable ..................................................................... 110 
Distribution of the Dependent Variable...................................................................... 113 
Identifying Crime and Non-Crime Cases ............................................................... 118 
Comparative Negligence......................................................................................... 121 
Weights ................................................................................................................... 123 
 vi
Effect of Adjustments to the Dependent Variable ...................................................... 124 
Economic and Non-economic Awards ................................................................... 125 
Selecting the Analytic Samples .................................................................................. 126 
Propensity Score Analysis .......................................................................................... 127 
Choice of Weighting or Matching .......................................................................... 133 
Reducing the Sample to Achieve Better Balance on Covariates ............................ 134 
Results......................................................................................................................... 138 
Conclusion .................................................................................................................. 139 
Chapter Four: Estimates of the Price of Crime............................................................... 141 
Multiple Victimizations during a Single Event .......................................................... 142 
Estimating Losses in Serious Property Crimes....................................................... 142 
Results......................................................................................................................... 144 
Estimating Losses in Serious Person Crimes.......................................................... 144 
Estimating Losses in Less Serious Property Crimes............................................... 147 
Estimating Losses in the Least Serious Property Crimes ....................................... 150 
Testing the Generalizability of the NIBRS Data ........................................................ 151 
Study Limitations........................................................................................................ 152 
Are the Results Representative of all Crimes? ....................................................... 152 
Limitations of the RAND Data............................................................................... 157 
Representativeness of NIBRS................................................................................. 159 
Social Costs............................................................................................................. 160 
Conclusion .................................................................................................................. 161 
Chapter Five: Implications for Research and Policy ...................................................... 167 
 vii
Rape and Homicide................................................................................................. 171 
Implications for Future Research................................................................................ 172 
Implications of the Research....................................................................................... 173 
Appendix A.1.................................................................................................................. 179 
Recovering Missing Ratio?s of Economic to Non-economic values.......................... 179 
Appendix A.2.................................................................................................................. 183 
Selection into Civil Trial............................................................................................. 183 
Economic Theory........................................................................................................ 183 
Prior Research............................................................................................................. 186 
Conclusion .................................................................................................................. 188 
Appendix A.3.................................................................................................................. 189 
Assessing the Effectiveness of the Propensity Score Weights ................................... 189 
Independent Variables ................................................................................................ 191 
Bibliography ................................................................................................................... 194 
 
 viii
List of Tables 
 
Table 3.1. Variation in the number of cases by state/region and year............................ 111 
Table 3.2. Variation in the probability of an award for the plaintiff by state/region and 
year.................................................................................................................................. 112 
Table 3.3. Variation in the mean jury award by state and year (unadjusted) ................. 114 
Table 3.4. Distribution of Total Award (Unweighted) ................................................... 116 
Table 3.5. Mean of Total Awards with and without Outliers (Unweighted).................. 118 
Table 3.6. Distribution of Total Award (Unweighted) ................................................... 122 
Table 3.7. Distribution of Total Award (Weighted) ....................................................... 124 
Table 3.8. Distribution of Total Award (Weighted). ...................................................... 125 
Table 3.9. Distribution of Injuries in RAND .................................................................. 130 
Table 3.10.  Theoretical Predictors of Jury Award Bias................................................. 131 
Table 3.11.  Types of Claim in Civil Cases .................................................................... 132 
Table 3.12.  Propensity Score Diagnostics (N=5,403) ................................................... 136 
Table 3.13. Award Estimates by Type of Injury, RAND Data Only.............................. 139 
Table 4.1. Estimates of Harms for Serious Injuries (RAND and NIBRS Data)............. 145 
Table 4.2. Price Estimates for Aggregated Part One Crimes, Propensity Score Models 146 
Table 4.2. Price Estimates for Aggregated Part One Crimes, Propensity Score Models 149 
Table 4.4. Estimates of Harms for Crimes with Property Losses Only, Plus Indirect Costs
......................................................................................................................................... 150 
Table 4.5. Percentage of Cases Matched ........................................................................ 154 
Table 4.5. Comparison of New Price Estimates to Extant Estimates (mean)................. 162 
 ix
Table 4.6. Comparison of New Price Estimates to Extant Estimates (median).............. 163 
Table 4.7. Price Estimates for Crimes ............................................................................ 166 
List of Figures 
Figure 1. Trends in Estimated Social Costs of Crime (1982-2003).................................... 7 
Figure 2. Conceptual Map of Cohen (1988) ..................................................................... 63 
Figure 3. Conceptual Map of Miller and Cohen (1999) ................................................... 68 
 
 
 
 
 
 
 
 
 
 
 
 
 
 
 x
 
Chapter One: Developing Robust Estimates of the Price of Crime 
 
Crime creates a substantial burden and results in diseconomies through the sub-
optimal allocation of scarce resources. As described in Becker?s foundational work on the 
economics of crime (1968), harms from crime are understood to include the direct losses 
to victims not internalized by offenders, the costs of crime control, and the losses to 
society from incapacitation of offenders. Since much of the harm from crime results from 
externalities, and safety is a (quasi-)public good, there is under-investment in private 
crime prevention (Samuelson, 1954; Tiebout, 1956). Public crime control expenditures 
are intended to create a more efficient equilibrium, by investing in crime control up to the 
point that marginal expenditures are set equal to marginal harms (social costs) from 
crime. Among Becker?s costs of crime, external costs to victims are the most difficult to 
quantify.  Optimal allocation of state resources therefore requires accurate estimates of 
the social costs of crime. The most widely cited estimates of the social costs of crime rely 
on civil jury award data with serious limitations (Cohen, 1998; Cohen et al., 1994; Cohen 
and Miller, 1999; Miller, Cohen and Rossman, 1993; Miller, Cohen and Wiersema, 1996; 
Miller, Fisher and Cohen, 2001; Rajkumar and French, 1997). 
Most prior work in the field seeks to estimate costs of crime rather than focusing on 
the price to victims. Costs of crime include the price and quantity of victimizations and 
the prices and quantities of subsequent criminal justice response, including crime 
prevention. Developing estimates of the costs to the criminal justice system is a relatively 
trivial exercise, since data are available from the Bureau of Justice Statistics to directly 
estimate these prices and quantities. By contrast, the price of crime to a victim or 
 1
 
potential victim can not be directly observed. As is discussed later in this chapter, victim 
harms are estimated to be at least as large as the criminal justice system costs (if not 
larger) and are thus a critical part of the policy calculus. However, prior estimates of the 
prices of crime have not proven to be particularly robust, as they rely on small samples, 
and inconsistent (and unreliable) methods.  This dissertation will develop new estimates 
of the price of crime to victims, measured as the willingness to accept crime losses as 
estimated from administrative data and jury award verdicts.  
The award estimates will use jury award data from the RAND Institute of Civil 
Justice to estimate the average jury award by type of physical injury. These micro-level 
data will then be linked with data from the National Incident-Based Reporting System 
(NIBRS) to estimate harms for 31 types of offenses.  
There are six stages in the estimation process. First, four variables (with 19 possible 
values) are identified that are observable in both the RAND and NIBRS data, including 
age and gender of the victim, type of injury, and region of the case. Second, a mean 
award is estimated for each of the possible cross-combination of those four variables in 
the RAND data.  For example, a mean award is estimated for a 30-39 male with a major 
injury in the west, a mean award is estimated for a 30-39 female with the same injury in 
the same region, etc. The process is repeated until a mean award has been estimated for 
all possible combinations (there are 1,213 valid combinations in NIBRS, and fewer in 
RAND, yielding a total of 342 combinations that are available in both datasets). The 
process is repeated in the NIBRS data to create cross-combinations in that data set. Third, 
three analytic data sets are created in the RAND dataset, including: all observations in the 
 2
 
RAND dataset (12,918); only those observations that can be affirmatively coded as 
crimes (895) and a subgroup of a propensity weighted sample (5,415).  
Fourth, the estimated mean award in RAND is interpolated onto the NIBRS dataset 
for all observations in NIBRS that have a cross-combination of attributes that also 
appears in the RAND data.  These estimates are then aggregated within crime types 
yielding an estimated distribution of expected awards for 10 types of Part I crimes. Fifth, 
estimates are developed for the prices of crime for victims of 8 serious property crimes. 
The estimate is the product of the reported property loss from NIBRS and a weight to 
account for non-economic losses. The non-economic loss weight is calculated as the ratio 
of economic to noneconomic losses in the RAND data for crimes where the victims 
suffered no injury or apparent minor injuries. Sixth, the price of crime is estimated for 13 
types of minor property crimes. The estimates are developed directly from reported losses 
in the NIBRS data. Finally, to address the concern that those cases in NIBRS that are 
linked to a case in RAND (about 1.4 million) are not different from those cases in NIBRS 
that do not match to RAND (about 400,000), t-tests are used to compare the mean 
property loss in Part I property crimes (burglary and robbery).  
This approach offers substantial advantages over extant estimates.  This study had 
the advantage of access to more comprehensive data than was available in previous 
research. This minimizes the number and breadth of assumptions that must be made in 
the analysis. The consistent use of micro-level data avoids problems associated with 
aggregation and the large datasets improves power. The study narrative describes a 
transparent method to aid replicability, and complicated (and unnecessary) regression 
analyses were not included in the analysis.  The final product of this research will be the 
 3
 
development of estimates for a full distribution of crime prices, including estimates for 
dozens of crime that do not currently have price estimates in the literature.  
 
Why Robust Estimates of the Price of Crime are Important to Policy-Making 
While there is general agreement that crime in the United States results in significant 
costs, there is limited consensus about the magnitude of those costs. The 1967 President?s 
Commission on Law Enforcement yielded the first estimate of the costs of crime to 
victims, and estimated total harms from crime at $650 billion (all monetary estimates in 
this paper are in 2003 dollars). More recent estimates of the crime burden are generally 
around $1 trillion: Collins (1994), writing in the popular press, estimated a total cost of 
$900 million, and Anderson (1999), writing in Law and Economics estimated about $1.36 
trillion in losses, net of transfers
1
. In testimony before the US Senate in 2006, Ludwig 
estimated the total costs of crime at $2 trillion. While these estimates reveal a consensus 
that there is a substantial crime burden, there is substantial variation in the magnitude of 
crime costs. Annual crime costs are equivalent to between 7% and 17% of GDP, and 
between $3,000 and $6,500 per US resident.  
Total costs of crime have several components: direct costs to victims; indirect costs 
to victims; public crime control expenditures; crime induced production (including 
private crime prevention, drug trafficking, and costs of substance abuse); white collar 
crime/corporate fraud; and, opportunity costs to offenders. Direct losses (also referred to 
as tangible losses) from crime include lost wages and medical care. The most recent 
                                                 
1
 Anderson estimates more than $730 billion in transfers, e.g. the value of goods transferred from a victim 
to an offender. There is substantial debate in the law and economics literature about whether these costs 
should be included in total costs calculations, as is discussed in Chapter 2. 
 4
 
national estimates of the direct costs of crime to victims from the Bureau of Justice 
Statistics (Klaus, 1994) estimates that direct costs of crime in 1992 was $25.6 billion, 
with a median direct economic loss per crime of $38.70.  
Most of the published literature in this area has focused on both the direct and 
indirect costs of crime to victims, where indirect costs (also referred to as intangible 
losses) include fear, pain and suffering, and risk of death. There is substantial variation in 
the estimates of the total direct and indirect costs associated with crime, including fear of 
repeated victimization, but the total of both indirect and direct costs are an order of 
magnitude larger than the BJS estimates of direct losses alone. Using surveys to estimate 
private citizen?s willingness to pay to avoid victimization yields the largest estimates. 
Using a contingent valuation technique, Cohen (2005) estimates the total direct and 
indirect costs of crime at $500 billion (also see Cohen, Rust, Steen and Tidd, 2005)
2
. 
Ludwig (2006) weights the Cohen estimates to account for the exclusion of less serious 
crimes and estimates total intangible costs of about $700 billion.  
Estimates derived from willingness to accept approaches yield slightly smaller 
estimates, ranging from $75 to $300 billion annually. McCollister (2004) estimates $200 
to $300 billion, Miller, Cohen and Wiersema (1996) estimate $80 to $135 billion, 
Rajkumar and French (1997) estimate between $130 and $200 billion and Cohen (1988) 
estimates between $70 and $100 billion.  Anderson (1999) uses a willingness to accept 
strategy and estimates an annual cost of $165 billion to victims who survive crime and 
                                                 
2
 Author?s calculations. Cohen et al.?s cost to victims were multiplied by the number of crimes in each of 
seven index offenses for each year between 1982 and 2003 and translated into 2003 dollars. The same 
methodology was applied to the other four extant estimates of costs of crime to victims. 
 5
 
$540 billion in lost life. Miller et al. (1996) estimate the total costs of crime, including 
intangible costs, totaled $585 billion.  
These costs of crime estimates have three important applications. First, they inform 
cost-benefit analysis of new policies and programs by creating a standardized metric with 
which to evaluate outcomes.  Second, because the costs of crime vary between crimes, 
these estimates can inform the optimal allocation of criminal justice resources in crime 
control, where criminal justice system stakeholders must choose among a range of anti-
crime strategies with heterogeneous impact on types of crime. Third, they provide new 
information that can be used to evaluate the effectiveness of crime control efforts over 
time.  
In addition, these estimates can be observed longitudinally to compare these changes 
to trends in public anti-crime expenditures, and trends in population growth and inflation.  
If the estimates of the costs of crime to victims are robust, then these data can offer 
answers to critical policy questions: Are costs to victims increasing or decreasing over 
time? Do the costs of crime to victims exceed public investment in anti-crime 
expenditures
3
? Do these results hold when changes in population size and inflation, are 
accounted for? Figure 1 combines population data from the Census Bureau, inflation data 
from the Bureau of Labor Statistics Consumer Price Index, public crime expenditure data 
                                                 
3
 Descriptive data suggest that crime rates have been relatively volatile over the last two decades, but 
display a general trend where annual increases in the 1980s were followed by declines in the 1990s. The 
same general pattern holds for both violent crimes and all crimes. By contrast, crime control expenditures 
have been stable throughout the period. Crime control expenditures increased every year, and increased at a 
rate greater than inflation, generally between 3 and 6 percent above inflation.  If economic theory holds, 
and crime control expenditures reflect the expected marginal harms from crime, these data suggest that the 
expected marginal harm from offending is increasing in time (which is also reflected by the increases in 
estimated costs of crime to victims). This may result from more serious average victimization, or may 
result from a change in taste for crime. That is, as the American population ages (the average age in the US 
has increased from about 30 in 1980 to almost 37 in 2007) and grows wealthier (real per capita income 
increased 70% in this period), the relative price of crime may rise if citizens are risk averse in crime. 
 6
 
from the Bureau of Justice Statistics, and costs to crime victim data from the four most 
commonly cited studies:  Cohen?s (1988) and Miller et al. (1996) using jury awards, 
Rajkumar and French (1997) and McCollister (2004) jury award studies, and the Cohen 
et al. (2005) contingent valuation study (labeled CV).  
 
Figure 1. Trends in Estimated Social Costs of Crime (1982-2003). 
 
  
 
 
$0
$50,000
$100,000
$150,000
$200,000
$250,000
$300,000
$350,000
$400,000
$450,000
$500,000
1982 1984 1986 1988 1990 1992 1994 1996 1998 2000 2002
Millio
n
s
Cohen
CV
McCollister
Miller, Cohen et al.
Rajkumar and French
Inflation and Population
Real Increase
 
 
 
Source: The estimates of the cost of public crime control expenditures are developed from the Bureau of Justice 
Statistics Justice Expenditure and Employment Extracts Series, using data from the Census Bureau's Annual 
Government Finance Survey and Annual Survey of Public Employment (1983-2003).  Data describing victim costs 
are developed from two sources: 1) the Federal Bureau of Investigation?s Uniform Crime Reports (1983-2003) were 
used to develop crime trends, and 2) estimates of the monetized value of harms were taken from Cohen (1988),  
Miller et al. (1996), Rajkumar and French (1997), McCollister (2003) and Cohen et al (2005).  Bureau of Labor 
Statistics Consumer Price Index data were used to calculate changes in real spending. 
 
 
As shown in Figure 1, there is substantial variation across the cost of crime to 
victim?s estimates, even when dollar values are standardized. This suggests that extant 
estimates of the price of crime are not robust with respect to the estimation strategy 
(contingent valuation studies consistently return higher estimates than willingness to 
accept estimates), nor are they robust within method (as older studies return lower 
 7
 
estimates than more recent studies). Overall, the Cohen et al., (2005) contingent valuation 
study returns the highest values in each year, followed by the McCollister study. The 
earlier jury award studies (Cohen, 1988; Miller, at al., 1996) returns the lowest values.  
Together they tell a provocative story where the price of crime is actually increasing over 
time. As the average American is both older and wealthier at the end of this series than at 
the beginning, this may well have some merit. Conversely, this may simply be an artifact 
of changes in study design. Nevertheless, these changes over time suggest the potential 
value of robust estimates in informing large-scale policy formulation. 
Importantly, these estimates also exclude several types of crime that may have large 
costs to society. Extant estimates of victim?s costs are generally limited to the Federal 
Bureau of Investigation?s (FBI) list of index crime. White collar crime is estimated by 
Anderson (1999) to cost almost $700 billion annually, once direct costs to victims of 
burglary, theft and larceny are excluded.  Using the same data as Anderson (1999), 
Cohen (2005) arrives at a similar estimate of the cost of white collar crime/fraud. 
Computer crime, which is not included in these estimates of white collar crime, is 
estimated to add another $70 billion to total crime costs (FBI, 2005). Anderson (1999) 
and Ludwig (2006) estimate that lost productivity due to criminal activity totals $260 
billion. Private protection measures total $64 billion (Anderson, 1999) and costs of 
avoidance behavior (private precautions revealed by changes in routine activities, see 
Clotfelter and Seeley, 1979) total $108 billion.  Other unmeasured costs include losses 
from drug abuse excluding direct crime costs ($50 billion (Swan, 1998)), private crime 
prevention purchases total $20 billion (Clotfelter and Seeley, 1979), and alcohol-related 
motor vehicle crashes ($20 billion (Rice, 1993). Other costs of crime may difficult to 
 8
 
measure, such as the unmeasured costs from crime from urban decay (Taylor, 1995). In 
addition to the cost of crimes to victims, there are substantial public crime control 
expenditures to investigate arrest, prosecute and incarcerate offenders. In 2003, the most 
recent year data were available, total governmental spending on crime control programs 
was $205.6 billion (Figure 1).  In nominal dollars, total crime control expenditures 
increased more than five-fold from $36 billion in 1982 to $185 billion.  
 
Research Applying Cost of Crime Estimates 
There is a large literature describing the economic foundations of criminal behavior. 
Economic analyses of crime control policies tend to focus on relationships between social 
policies and offending that are theoretically predictive of crime. The relationships 
between the incapacitation and deterrent effects of prison and crime and the value of 
human capital acquisition have been the topic of many studies (Becker, 1968; Ehrlich, 
1973; Ehrlich, 1981; Ehrlich, 1996; Freeman, 1996; Grogger, 1998; Levitt, 1996; 1997; 
Lochner and Moretti, 2004; Piehl and DiIulio, 1995; Raphael and Winter-Ebner, 2001).  
While the early literature in this area focused mainly on theory, more recent research 
have used estimates of the price of crime to victims to more clearly identify the 
implications of changing the scale of criminal justice institutions. Recently, applied 
studies of the economics of crime, in the form of cost-benefit modeling of anti-crime 
interventions, have become more prevalent.  These studies tend to link observational data 
on the local average treatment effect for a discrete sample, and explicitly link those 
outcomes with price data to estimate economic efficiency (Cartwright, 2000; Cohen, 
2000).   
 9
 
The two key challenges in applied studies are 1) the resolution of statistical and 
identification problems that confound causal inference (Dehejia and Wahba, 2002; 
Heckman, et al., 1997; 1998; 2001; Imbens and Angrist, 1994; LaLonde, 1986; Manski, 
1995; Raphael and Stoll, 2006; Rosenbaum and Rubin, 1983; Rubin, 1974; Smith and 
Todd, 2005, and 2) the development of robust estimates of prices of criminal 
victimization in the absence of market data (Cohen, 1998; Cohen et al., 1994; Miller, et 
al., 1993; Miller, et al., 1996; Miller, et al., 2001; Rajkumar and French, 1997). The 
scholarly literature on issues of causal inference with observational data is far more 
extensive than the price literature, and this is reflected in the focus of economic 
scholarship on theoretical questions with recalcitrant identification problems (Evans and 
Owens, 2007; Kessler and Levitt, 1997; Knowles, Persico and Todd, 2001; Levitt, 1996; 
1997; 1998; Ludwig and Kling, 2007; Raphael and Winter-Ebner, 2001; Waldfogel, 
1993).  Overall, studies have generally followed one tradition or the other and there are 
few?if any?studies that treat inference problems and pricing problems with equal 
weight. 
 
Limitations of Strategies to Estimate the Costs of Crime to Victims 
While most of the extant estimates of the price of crime use jury award data to 
estimate social costs, more recent work has used contingent valuation methods to develop 
estimates. In addition, Quality-Adjusted Life Years (QALY?s) can be used to estimate 
prices for crime victims, as can hedonic pricing techniques. However, each approach has 
some substantial limitations. This section briefly describes the strengths and weaknesses 
of each approach, with a more thorough discussion in the Chapter 2.  
 10
 
The first cost of crime to victim?s studies used hedonic pricing to estimate market 
prices by observing revealed preferences for the components of a good, usually measured 
as heterogeneity in real estate prices or wages due to differential risk of crime (Thaler, 
1978; Thaler and Rosen, 1975, Clark and Cosgrove, 1990).  The hedonic approach is 
strictly defined as a willingness-to-pay (WTP) method, using ex ante measures of price to 
estimate equivalent variation.  Thaler (1978) used a random sample of single family 
homes from Rochester, New York to estimate the price of property crime. Clark and 
Cosgrove (1990) use data on wages, structural features of the home, and individual 
attributes to estimate the relationship of rental values and safety.  The hedonic pricing 
approach is criticized on the grounds that prices and crime are endogenously determined, 
and that results are aggregated individual estimates and not equivalent to social costs. 
With respect to the former issue, Manski (1995:6) calls the use of equilibrium price data 
to infer demand behavior of consumers and supply behavior of producers ?a classic 
identification problem.? On the latter issue, critics note that society?s willingness to pay 
for a policy is different from the sum of individual preferences, due to community-level 
preferences (Cook and Ludwig, 2000:56-57)). 
Recently, studies of the costs of crime to victims have estimated equivalent variation 
functions, which measure ex ante willingness to pay (WTP) to avoid crime using 
contingent valuation survey techniques (Cook and Ludwig, 2000; Cohen, et al., 2004). 
The contingent valuation method uses stated preferences as the proxy for market 
behavior.  The general approach is to use a referendum-based approach following the 
recommendations of the NOAA Panel on Contingent Valuation to solicit prices 
respondents would be willing to pay to reduce their (or their communities) risk of 
 11
 
victimization policy (Arrow, et al., 1995). While the Cohen studies cited above adhere 
closely to the NOAA recommendations, critics of the approach suggest that even those 
strict standards do not compensate for structural limitations in the method (Carson et al., 
1999). Most importantly, the contingent valuation approach elicits stated preferences 
rather than observing behavior in a binding market transaction. Thus, contingent 
valuation tends to overestimate willingness to pay (Diamond and Hausman, 1994; 
Portney, 1994; but see Schelling, 1968; Cook and Ludwig, 2000).  
A third approach, QALY?s (Quality-Adjusted Life Years) has been used extensively 
among UK researchers to value the costs of crime to victims (DuBourg and Hamed, 
2005) and internationally for the study of health interventions (Grossman, 1972). In 
health studies, health capital is the product of the sum of discounted health status over 
time and the value of a year of perfect health (Cutler and Richardson, 1998). In crime 
studies, the general strategy is to rank-order utility states anchored by high disutility from 
a criminal event to no disutility from a criminal event. These estimates, drawn from 
surveys or expert rankings of ex ante expectation of harm from crime, are then used to 
rank-order the harms from victimization across crime type (Dolan and Peasgood, 2005). 
Since the intangible costs of crime to be estimated are mainly psychic, a key 
disadvantage of this approach is that there are no extant estimates of QALY in the 
presence of heterogeneity of mental health states (Zaric, Barnett and Brandeau, 
2000:1104). 
The final approach values compensating variations to estimate ex-post willingness to 
accept (WTA) crime by estimating the amount of compensation necessary to return an 
individual to their original level of utility (Cohen, 2000). WTA usually combines jury 
 12
 
award data and cost-of-illness data based on ex post estimates of harm from 
victimization. The general strategy in developing price estimates of victim harms is to 
observe the distribution of injuries in jury-adjudicated civil cases and use those data to 
estimate indirect costs of crime. The approach has been widely criticized, on the grounds 
that estimates are ex post rather than ex ante and that the estimates are aggregated 
individual losses rather than social cost (Cook and Ludwig, 2000).  Most of the studies 
use a blended cost-of-illness approach and jury compensation strategy (Rajkumar and 
French, 1997).  While the cost-of-illness approach clearly suffers from these limitations, 
the jury compensation seeks to approximate an ex ante estimation of equivalent variation, 
and thus is less susceptible to these criticisms. 
Of the four approaches, the jury award approach is most amenable to further 
research to create more robust estimates of crime, mainly due to the limits of the other 
approaches. The contingent valuation approach has been used with increasing frequency; 
however, the limitation of using stated rather than revealed preferences appears to be 
insurmountable, as is the endogeneity problem in hedonic pricing. Research has yet to 
show that QALYs produce robust estimates of harms to victims. By contrast, the main 
limitation of the jury award method (in addition to the problem of ex post estimation) has 
been the limitations of the data. With new data sources such as NIBRS, a re-estimation of 
harms to victims may yield more robust estimates.  
 
Limitations of the Jury Award Method 
Apart from the theoretical criticisms, the main analytic challenge to this approach 
has been that while micro-level data relating injuries to prices are available, micro-level 
 13
 
data relating injuries to crime were not available in the past.  Thus, in past research, the 
two main sources of information about the harms from criminal victimization cannot be 
linked at the micro-level. As a result extant price estimates are indirect estimates of harm.  
One contribution from this dissertation is that the analysis will directly link data at the 
micro-level.  
To address this problem, data from multiple sources are mapped together to describe 
the relationship between jury awards and crime.  Typically, the research first develops an 
estimate of the association between injury and civil jury award, to estimate psychic 
losses. Next, health service utilization data is used to estimate the costs associated with 
crime-related injuries. Next, the prices from the crime-related injuries are weighted 
according to the distribution of injuries in criminal populations. From these estimates, an 
award per injury is estimated.  Those estimates are then mapped onto data describing the 
distribution of injuries in all crimes to arrive at estimates of the direct and indirect costs 
of crime (Cohen, 1988; Miller, Cohen and Wiersma, 1995; Rajkumar and French, 1997; 
Cohen and Miller, 1999; Cohen, 2000; Cohen and Miller, 2003; McCollister, 2004).  
Most econometric studies that include an estimate of the social costs of crime rely on 
WTA jury award data (see Waldfogel, 1993; Levitt, 1996; Lochner and Moretti, 2004). 
The main empirical criticism of the WTA approach is that it undercounts losses by 
excluding income taxes, but may overestimate losses if jurors anticipate legal fees 
(Rajkumar and French, 1997). There is also a concern that civil cases include an 
unrepresentative sample of criminal victims (Cook and Ludwig, 2000)  
Thus, the policy challenge can be summarized as follows. Neoclassical economics 
theory requires estimates of the price of crime to victims in order to develop models that 
 14
 
predict optimal crime control expenditures. Four strategies are available to develop these 
estimates, but all face theoretical or empirical objections that have not been resolved in 
the literature. The fourth approach (WTA) is subject to theoretical critiques on the 
grounds that estimates are ex post, but estimates developed using this technique are cited 
more often than estimates from other approaches. However, because past studies have not 
been able to link micro-level jury award data and micro-level crime data, the results have 
not been robust to study design. The next section describes prior research using jury 
awards to estimate crime prices, and the sections that follow propose a strategy for 
resolving those objections. 
 
The Cohen, Miller Literature Using Jury Awards to Estimate Victim Costs 
The WTA approach generally uses several data sets to generate estimates of the 
harms from crime: civil jury award data that describes the relationship between injuries 
and jury awards for both economic and non-economic damages and data that links 
injuries to specific types of crime.  In response to concerns (especially during the 1990s) 
that jury awards were increasing in size and were therefore out of proportion with the real 
harms suffered by victims, a large literature emerged to evaluate the validity of jury 
awards (this literature is discussed in Chapter 3).  The general conclusion of that 
literature is that juries are credible arbiters of civil claims, and that the factors that cause 
juries to make awards beyond the specific claims of the plaintiff can generally be 
observed in jury data.  Because jury award data are more readily available than are data 
for other estimation strategies (such as hedonic pricing), most of the estimates of the 
price of crime are developed from jury data.  
 15
 
Still, early efforts to assemble civil jury awards in a single dataset yielded limited 
results.  There was?and continues to be?no national reporting data source that 
aggregates information about cases processed in the civil court system.  Data on civil 
awards is primarily collected by private entities that collect and aggregate award data.  
Prior to about 1985, the principal jury data aggregators did not use representative 
sampling strategies. Rather, cases were sporadically collected and data collection was 
focused on unusual cases (often cases with the largest verdicts).  Thus, the samples were 
therefore a non-representative sample of jury verdict awards, and research using those 
data faced almost insurmountable identification issues. Since 1985, civil jury award data 
have been collected using stratified, random sampling.  The number of jurisdictions 
included in the sampling frame has increased as well reducing the severity of 
identification problems associated with the use of these data
4
.  
The main challenge to research using civil jury awards is that few of the awards can 
be directly linked to a criminal event (for a thorough discussion of this issue, please see 
Chapter 3). For example, in the first study to use jury award data to estimate intangible 
costs, Viscusi (1986) was limited to a sample of 159 awards. In two recent studies Miller 
and Cohen use a national jury award dataset from 1980-1991 was used that included over 
100,000 cases. However, for one paper, they can identify only 1,467 intentional injury 
cases, including 1,106 physical assaults and 361 sexual assaults (Cohen and Miller, 1999) 
and for the other 514 physical (non-sexual) assaults (Cohen and Miller, 2003). It is also 
difficult to identify property crime cases.  It should be noted, however, that it is likely 
that many additional civil cases result from criminal behavior, but it is difficult to identify 
                                                 
4
  This history of the jury award data is developed from a series of conversations with Nick Pace, a long-
tenured social scientist at the RAND Institute for Civil Justice.   
 16
 
those claimants in the available data. As a result, most published estimates of the price of 
crime (or costs to victims) are limited to civil cases involving Part I crimes.  
Prior research has been concerned with two issues related to these data. First, that 
the cases in the sample over-represent the most serious crimes.  A second and related 
issue is that the crimes that can be directly observed may over-represent the most serious 
crimes within each crime category.  The general strategy to work around this problem has 
been to use the jury award data only to assess indirect losses (such as pain and suffering) 
and to use other data sources to observe direct losses (such as property loss, lost wages 
and health care expenses). Typically, some combination of data from a cost-of-illness 
source is sued to value the physical harms from a criminal event, and an additional source 
(generally the National Crime Victimization Surveys) is used to value the other direct 
harms from crime (such as property loss and lost wages). This analytic strategy is limited 
by the lack of case-level data that includes information on both the type of crime 
committed and the harms from the criminal event.  Thus, researchers have had to 
indirectly observe the relationship between injury and crime.  
In a series of widely cited articles over the last two decades, Vanderbilt economist 
Mark Cohen writing alone (Cohen, 1988; 1990; 2000; 2005) and with Ted Miller (Cohen 
and Miller, 1994; 2003; Cohen, et al., 1995; Miller, et al., 1996) has used jury award 
verdicts to predict the cost of crimes to victims. The studies are among the most cited in 
the law and economics literature. According to Google Scholar, the Miller, Cohen and 
Wiersema study published in 1996 has been cited slightly more often than a well-
regarded article published the same year by Levitt, who estimates the effects of prison on 
crime rates. In these studies, Miller and Cohen use jury award data to estimate an 
 17
 
expected award for combinations of victim and injury attributes and use prevalence of  
injuries in the population of crime victims (from the National Crime Victimization 
Survey) to re-weight the data and calculated the average loss across crime categories.  
The approach has several limitations. The approach relies on relatively small 
samples of data (generally a few hundred observations) and price estimates are generated 
for only a few, broad categories of crime.  The re-weighting is accomplished using a 
regression analysis that has substantial limitations, in particular, that estimates are 
derived from non-significant parameters, In addition, because the articles describing the 
work have mainly appeared in publications for general audiences rather than scholarly 
journals, the method has not be transparently presented and thus is difficult to replicate. 
 
Modifying the Jury Award Method to Develop New Estimate of Costs to Crime Victims 
There are now two sets of data available to update the jury award estimates that 
should allow for more direct estimation of victim costs than were available to MC. First, 
the RAND Institute of Civil Justice has collected jury award data over a long series 
(1985-2000) across a large number of jurisdictions, representing about one-quarter of the 
US population. The data were collected according to a more consistent protocol than was 
used in the first Cohen studies
5
.  Second, data from the National Incident Based 
Reporting System (NIBRS) allow for estimates to be developed about the generalizability 
of jury award data, by comparing the prevalence of crimes resulting in jury awards to a 
broader sample of all crimes. In this paper, the RAND data and the NIBRS data are 
                                                 
5
 Personal communication with Nick Pace, Principal Investigator of the jury award study at the RAND 
Institute of Civil Justice.  He notes that the data from 1980-1985 were collected haphazardly by jury 
reporting services, and cautions against using those data for analysis (RAND collected data from this 
period in Phase II of their study). Data in the study are therefore limited to Phases III-V (1986-2000). 
 18
 
joined to generate direct estimates of the costs of crime to victim. The main advantage of 
this approach is that the costs of crime can be directly estimated from these two sources, 
without requiring the use of health data as a middle step to join the data.  
Jury Data 
Data from the RAND Institute for Civil Justice on the size of civil jury verdicts to 
estimate the monetary harms associated with criminal victimization will be the 
foundation for developing estimates of the costs of crime to victims. In total, there are 
38,141 cases in the combined jury award database. Data are available from 1985 to 1999, 
and the number of cases increases gradually over time from 1,971 in 1985 to 2,723 in 
1999, with a peak of 3,443 in 1997.  The data include all jury awards in the states of 
California (14,803) and New York (10,416), and the cities and surrounding counties of 
Chicago, IL (4,332), Houston, TX (4,410), Seattle, WA (1,207) and St. Louis, MO 
(2,973). The data were coded by RAND researchers from trade publications (?jury verdict 
reporters?) that report the outcomes of civil proceedings. Cases in the file include any 
civil case resulting in a verdict that was adjudicated by a jury in the project period. Cases 
closed by settlement, hung jury, or cases heard by a judge are not included in the RAND 
dataset. The plaintiff won in 47.5% of cases, and only these cases are used in this 
analysis. There is substantial variation in awards in these cases, with a mean of $1.22 
million and a mean of $147,000. One percent of cases have an award greater than $10 
million, and one percent has an award under $1,000.  
As noted earlier, the jury data are not coded in a way that allows for direct 
observation of an underlying criminal act. Only about ten percent of the cases involve an 
intentional tort and can thus be affirmatively coded as a civil case resulting from a 
 19
 
criminal act. However, as is discussed in Chapter 3, there are certainly other criminal 
cases in the data set, particularly among the negligence and auto liability. However, these 
cannot be affirmatively coded as having resulted from a criminal incident. Thus, the 
preferred strategy is to use the co-variation between case attributes and an affirmative 
coding of a case as having resulted from crime to give more weight to cases that resemble 
?crime? cases and less to those cases that do not.  
NIBRS Data 
NIBRS data is a product developed by the FBI and the Bureau of Justice Statistics to 
capture detailed characteristics of criminal events. Unlike the FBI Uniform Crime 
Reports which captured aggregate monthly statistics on the number of offenses, NIBRS 
data is reported at the incident-level. Data include information about the offense (type of 
weapon, completed or not), the offender (age, race and gender), the victim (age, race, 
gender, ethnicity and type of injury), type of property stolen or damage (including value), 
and arrestee data (age, race, gender, ethnicity, age and type of arrest).  As described 
below, an analogue to some of these measures is contained in the jury award data. Data in 
NIBRS are available for ten states (Colorado, Idaho, Iowa, Massachusetts, Michigan, 
North Dakota, South Carolina, Utah, Vermont, Virginia) between 1998 and 2003, where 
more than half of the population in a given state is covered by NIBRS reporting.  
Prior research in this area was performed prior to the development of NIBRS. 
NIBRS offers some advantages over NCVS, which has been used more often in prior 
studies to create weights to adjust for the prevalence of crimes in the general population. 
Most importantly, NIBRS includes far more observations, and thus more observations of 
the rarest, but most serious crime. Since the small number of serious person crimes 
 20
 
explain most of the total cost of crime, access to these data are critical to the development 
of price estimates. In addition, some studies have shown that NIBRS data are more 
reliable on some measures than NCVS. Chilton and Jarvis (1999) find that that some 
differences are observed between NCVS and NIBRS, especially on victim and defendant 
attributes. They note that NIBRS data closely resemble data on Supplemental Homicide 
Reports, suggesting that NIBRS data may be more reliable overall. In addition, NIBRS 
includes events linked to individuals excluded from NCVS, including military personnel, 
the homeless, the incarcerated, and itinerant guests, a group that likely includes many 
recently released ex-prisoners (Maxfield 1999). And, commercial businesses are 
excluded from NCVS, and thus some victims of ?robbery, burglary, arson, larceny-theft, 
motor vehicle theft and vandalism? may be excluded (Maxfield, 1999:128). In addition, 
victimless crimes are not included in NCVS but are recorded n NIBRS. Finally, NCVS 
explicitly excludes victims under 12 years of age, who are included in the NIBRS data. 
 The NIBRS data for 2000 include 3.8 million observations for which data are not 
missing for the victim and the type of crime. Almost 97% of crimes in NIBRS were 
completed. The average direct loss from crime in NIBRS was $1,432 and the median loss 
was $100. Data are also available on recovered items for 325,000 cases, with an average 
recovery of $3,075 and a median recovery of $90. Subtracting recovered losses from all 
losses does not substantively change the mean or median direct loss.  Automobiles 
(10.3%) are the only type of property lost for more than 10% of cases. 
 21
 
 
Methods 
 The general estimation strategy is to predict the cost of crime to victims for as 
many different types of crimes as possible. The general model is regress jury awards on 
crimes, controlling for confounding explanations, according to: 
JURYAWARD= ?(CRIME
i
) + Xi??+ ?   (1) 
where the JURYAWARD is the total award for a case (including general awards, specials 
and punitive damages), CRIME is a vector of criminal event types, and X is a vector of 
theoretical attributes associated with non-claimant related jury awards. The parameter on 
CRIME is the average award for an additional crime of each type, which is interpreted as 
the cost to a victim of that type of crime. There are three significant issues with this 
model as specified. 
However, (1) cannot be directly estimated since there are few observations within 
the RAND data set that directly link a jury award to a criminal act. As noted, only about 
10% of the observations in the RAND data are intentional tort cases. Some other victims 
of crime can be identified by the type of injury suffered (sexual assault or gunshot, for 
instance), but for most cases the underlying criminality of the event that lead to the civil 
case is not observable. As a result, the RAND jury award data are not sufficient to 
directly estimate the average costs of crime to victims.  This problem can be resolved by 
specifying a different model that exploits all of the observations in the RAND data set. In 
the RAND data set, virtually all of the observations include some type of physical harm, 
and data are available to describe those harms. The RAND data could be used to estimate 
direct costs of victimization and indirect damages such as the harms from pain and 
 22
 
suffering as a function of different injuries. Since comparable victim injury data are 
available in both the RAND and NIBRS data sets, the combined dataset would contain 
information about both crime and damages.  NIBRS data categorizes injuries as broken 
bones, possible internal injury, severe laceration, apparent minor injury, loss of teeth, 
unconsciousness, other major injury and no injury. RAND data includes much finer 
injury descriptions that can be aggregated to match the NIBRS coding. Since injury data 
are available for all cases in the RAND data, using injury data as the variable used to link 
the RAND data would increase the number of incidents in NIBRS (and the number of 
CRIME?s) that could be matched to a jury award. Once the jury award data associated 
with different types of injuries (and victim age and gender) are computed, these data can 
be interpolated onto the NIBRS data to predict awards for criminal acts. These awards 
can then be interpreted as the cost of crimes to victims.  
The analysis will be conducted using three samples from RAND. First, all cases in 
the RAND data will be used to estimate crime prices. The main advantage of the RAND 
dataset over alternatives used in past studies is that the data include a much larger sample 
of jury awards. Prior studies have focused only the crimes that are directly observable in 
jury data, and this has limited the studies estimates of costs of crime to victims to a small 
number of crimes. Because the RAND data include more than 12,000 observations, it is 
possible to identify more cross combinations of attributes, and to estimate the price of 
crime for a larger number of crimes. Thus, one set of estimates from this study will use 
all of the observations in RAND to develop price estimates.  
 Second, prior studies have focused only on those jury cases that can be directly 
identified as having resulted from a crime. That is, only those cases that can be 
 23
 
affirmatively coded as having resulted from a criminal act are included in the data. 
However, as will be discussed in Chapter 3, this means that some criminal cases will be 
excluded. Nevertheless, it seems prudent to include estimates of the price of crime that 
are limited to those observations that are known to result from a crime.  
Third, a propensity score analysis will be conducted to generate weights that balance 
across those observations that can be affirmatively coded as crimes and those that cannot. 
Theoretically, this should not be an issue. Juries are instructed to make awards only as a 
condition of the actual harms suffered by a victim and not the facts that led to that injury, 
excluding these studies may unnecessarily limit the power of the analysis. However, 
when aggregating across types of claim, if the cause of the injury (such as medical 
malpractice), and not just the characteristics of the injury, were correlated with the size of 
the jury award than the estimator would be biased. To address this potential selection 
problem, propensity score models will be used to model the likelihood that the 
characteristics of an injury reduce bias from selection on observables following the 
propensity score approach described in Rosenbaum and Rubin (1983). Propensity score 
matching is a statistical algorithm that matches treated and untreated participants in the 
presence of multiple determinants of treatment status (Heckman, et al., 1997).  While the 
propensity score approach is preferred ex ante, all three models will be reported. 
A major concern with this study (and past studies) is that the jury data are not 
representative of all criminal victims, and thus selection effects may bias the 
interpretation of crime prices that are estimated from jury awards.  Potential sources of 
bias include heterogeneity in awards by type of civil claim, greater severity in criminal 
cases that result in civil jury award, and heterogeneity in the prevalence of victim 
 24
 
attributes and injuries. Unfortunately, this study is limited in the extent to which 
empirical tests can be conducted to determine whether the RAND data are representative 
of all crimes. A limited number of empirical tests of this question are discussed in 
Chapter 4. A discussion of the potential implications of this issue is discussed in 
Appendix A.2. 
 
Interpolating the RAND data onto NIBRS 
 The next step in the analysis is to map the data in the RAND dataset onto the 
NIBRS dataset. By combining NIBRS and RAND data, a much larger set of observations 
can be used to estimate the costs of crimes to victims. This approach requires two 
assumptions. First, that the observed jury award associated with any injury in the RAND 
data set would be the same as an unobserved jury award for an identical crime observed 
in the NIBRS data. And second that the observations are comparable, even though the 
two data sets describe different populations. There is no geographical overlap between 
the two groups, and the time periods covered by the two data sets only coincide for two 
years. Finally, since there are no common observations the data cannot simply be merged. 
The RAND data also cannot be appended to the NIBRS data, since the dependent 
variable is not observed in the NIBRS data.  However, the two data sets do contain data 
on variables that are consistent across the two groups, and those similarities can be 
exploited to create a unified data set. 
First, common elements are identified between the two sources. These include: 
? Victim age (20-29, 30-39, 40-49, 50 and older); 
? Victim Gender (Male of Female); 
 25
 
? Type of injury (broken bones, possible internal injury, severe 
laceration, apparent minor injury, loss of teeth, unconsciousness, other 
major injury and no injury); 
? Urban, rural or suburban; 
 
Next, a variable is created designating each cross combination of attributes and a 
value is assigned to each observation in both RAND and NIBRS. Within each cross-
combination, a distribution of awards is created. For each identical cross combination in 
NIBRS, the mean of the cross-combination in RAND is interpolated onto all the 
observations in NIBRS with that cross-combination of attributes.  Data in NIBRS are 
then re-ordered within crime categories, instead of within injury categories, allowing 
calculations of mean and median victim harms within each crime category. Estimates will 
therefore be generated for 31 crime categories.  
Two adjustments are then made to the above method. First, it should be noted that 
the support space in RAND and NIBRS do not perfectly overlap. Thus, there are cross-
combinations of attributes that are observable in NIBRS that are not observable in 
RAND.  To account for this, prior to running the selection models, only those 
observations that fall into a cross-combination that is observable in both datasets is 
selected. In practice, this has the effect of excluding some NIBRS observations (about 
29%) from the final analysis.  
The analysis described above is not performed for every type of crime in the NIBRS 
dataset. In the extant literature, serious person crimes are often assigned both an indirect 
and a direct loss. This study follows that precedent and assigns all jury award values to 
serious crimes, which are defined as those cases that are likely to have property losses, 
other direct losses and indirect losses. However, many?if not all?other types of crimes 
likely have a psychic component as well.  To account for this, a regression analysis is 
 26
 
conducted on the logged jury award to predict the ratio of direct to indirect losses in those 
cases where both values are observable in RAND. This ratio is then used as a multiplier 
in the NIBRS datasets for crimes that fall within the same strata as crimes that have 
previously been assigned indirect losses. In a somewhat arbitrary decision this indirect 
cost multiplier is applied to cases that are likely to have only property losses and no other 
direct losses.  For consistency, the ratio of indirect and direct losses is therefore 
calculated only for those RAND cases where there were no or minor injuries.  For the 
other ?minor? crimes, victim harms are calculated only as the property losses reported to 
police. 
Structure of the Dissertation 
The dissertation is divided into four chapters. The second chapter describes the 
foundations of neoclassical theory that informs the development of cost-benefit analysis, 
and describes the evolution of cost of crime estimates, including the literature on the 
meaning and interpretation of jury awards that motivates the analysis, with particular 
attention to the adaptation of this method in the work of Miller and Cohen. The third 
chapter describes the first stage of the analysis, describes the data, explains the propensity 
score models and culminates in the estimate of the expected jury award by injury type. 
The fourth chapter describes the interpolation models used to impute values for crime 
victim profiles observable in the NIBRS and the RAND data, the results of those models, 
and the final results of models that use the interpolated and observed jury award values to 
estimate the costs of crime to victims. The fifth chapter describes the policy and research 
implications with particular attention to two issues: the opportunity for these estimates to 
be used to create more efficient use of public safety resources, and, the challenge of 
 27
 
implementing efficient policies where those who pay the costs are different from those 
who receive the benefits.  
 28
 
Chapter Two: Review of Prior Research on the Price of Crime 
 
The motivation for studying the costs of crime to victims is straightforward.  Most 
theorists posit that potential offenders that implicitly measure the costs and benefits of 
committing a crime before acting. Costs of crime include the risk of detection and the 
severity of punishment. While this supply model of offending is well developed, the 
demand side of the equation is less clearly articulated. Ehrlich (1996) proposes a demand 
model where demand for crime is derived from the supply of offenses function. Thus, the 
potential losses from crime (the analog of the benefits to offenders) determine the amount 
of public and private crime precaution. It is therefore assumed that the amount of harm 
experienced by victims of crime can be compared to the costs of detecting and 
responding to crime to make efficient allocations of scarce anti-crime resources. More 
intuitively, this model posits that the costs of a program or policy designed to reduce 
crime should be less than the benefits that are measured as reductions in harm. 
 This model has been widely applied. Levitt (1996) compares the costs of 
deterrence from incarceration to the benefits of averted crimes from incarceration in 
evaluating the efficiency of prison. Lochner and Moretti (2003: 23) estimate ?the social 
savings from crime reduction resulting from a 1% increase in high school graduation 
rates? using this approach. Lott and Mustard (1997) use this approach to value the 
savings from increasing gun possession and Ludwig and Cook (1999; Cook and Ludwig, 
2000) use this approach to show the savings from decreasing gun ownership. The 
approach is widely used to evaluate the savings from early interventions with children 
(Olds, Henderson, Chamberlin, and Tatelbaum, 1992; Schweinhart, Montie, Xiang, 
 29
 
Barnett, Belfield, and Nores, 2005). More recently, a large literature has begun to emerge 
the measures the costs and benefits of various anti-crime strategies where the benefits are 
understood in this way. 
 Controversy surrounds the choice of method to estimate costs of crime to victims. 
The challenge to developing robust estimate of harms to victims emerges from the lack of 
a true market for the exchange of crime, as there is obviously no market place where 
private actors voluntarily exchange and thus all of the effects of crime are externalities.  
The various strategies all fall under the general rubric of contingent valuation studies 
which use secondary markets to price unobservable events. Contingent valuation methods 
can apply an ex ante approach, where stated preferences are used to estimate harms, a 
revealed preferences approach where choices about job or home selection are parsed to 
estimate preferences for crime risk, or a reimbursement approach, where neutral parties 
estimation of the inflicted harms are applied.  
By far the most widely cited method is the third-party valuation approach. In a 
series of widely cited articles over the last two decades, Vanderbilt economist Mark 
Cohen writing alone (Cohen, 1988; 1990; 2000; 2005) and with Pacific Institute of 
Research and Evaluation economist Ted Miller (Cohen and Miller, 1994; 1999; 2003; 
Cohen, Miller, and Rossman, 1995; Miller, Cohen and Wiersma, 1996) have used jury 
award verdicts to predict the cost of crimes to victims using a cost of illness model. The 
logic behind this approach is straightforward. As discussed, crime losses to victims are 
external to the crime transaction in the standard supply of offenses models. Some victims 
of criminal acts will seek to have the costs of their harm internalized by the offender (or 
other liable party), and will use the tort system as the means of recovery.  When plaintiffs 
 30
 
win a case, compensatory awards are made in two domains - 1) an award for the recovery 
of direct costs to victims and 2) an award for the recovery of intangible (fear, pain and 
suffering) costs.  Awards in a third category?punitive?are generally excluded from 
calculations of the true harms to victims. Reductions in awards due to shared negligence 
are also excluded from calculations of victim harm on the grounds that harms are a 
function of loss rather than culpability. Thus, victim losses are measured as the sum of 
observed harms resulting from a criminal incident. 
 The cost of illness approach is just one of a class of contingent valuation 
techniques used to develop estimates of the value of a resource using data from secondary 
or theoretical markets when there is no market place for the exchange of that good. While 
the term ?contingent valuation? is often used as short-hand to refer to stated preference 
surveys, contingent valuation methods can be divided into both those approaches that rely 
on revealed preferences and those that rely on stated preferences.  Most recent work has 
applied willingness to pay methodologies where stated preferences are used to estimate 
prices and quantities for unobservable markets. This includes estimates to understand the 
costs of gun violence (Ludwig and Cook, 1999; Cook and Ludwig, 2000) and estimates 
of the costs of crime across broad categories of harm (Cohen et al., 2004). However, the 
revealed preference approach to estimate harms dominates the cost of crime literature and 
most econometric studies, such as the efficiency of deterrence and the effectiveness of 
improving high school graduation rates, relies on the third party approach. The two 
strains of contingent valuation can be generalized as follows:  
? Willingness-to-pay estimates (WTP) are based on the price an individual would 
be willing to pay to avoid harms, such as death or disability, resulting from crime. 
 31
 
Methods of estimating willingness to pay include:  
? Required compensation, which estimates the price that would have to be paid 
to an individual in order for that individual to be indifferent about exposure to 
a dangerous event;  
? Hedonic pricing, where differences in the risk of criminal victimization are 
observed as a component of property values or wages from which estimates of 
the amount individuals would pay to avoid being victimized can be inferred; 
and, 
? Quality-of-life (often expressed as Quality of Life Years or QALYs), which 
estimates costs according to degrees of disability. 
 
? Victim-compensation or willingness to accept (WTA), is the converse of 
willingness to pay, and is the aggregated amount that would have to be paid to a 
victim to make them whole after criminal victimization. Methods of estimating 
willingness to accept include: 
? Jury compensation, which values victim costs including health care, lost 
productivity, and intangible costs such as pain and suffering at the rate juries 
compensate victims of crime;  
? Discounted future earnings estimates, which are based solely on the costs (or 
averted costs) of lost productivity due to an incident; and,  
? Cost of illness, which uses survey data to aggregate the tangible cost of crime 
(including health and productivity). 
 
 Both strategies have limitations. The main criticism of Willingness to Accept 
models is that estimates of the cost of victimization are estimated ex post rather than ex 
ante. Thus, WTA violates a fundamental assumption from price theory that choices about 
the use of scarce are based on expectations of utility and thus precede the transaction. 
WTA is in effect an instrument estimating how an individual would have behaved in the 
market had they been presented with a choice. Since there is no way to measure the 
correlation between how a pre-transaction choice to the necessary compensation to make 
a victim whole, the strength of this instrument cannot be evaluated. In addition, WTA 
relies heavily on an individual's current context to determine appropriate compensation. 
 32
 
If an individual is very young, elderly, or not employed, their losses may be 
underestimated. When these estimates are extended to include a longer time frame (e.g. 
discounted future losses are included), these issues will be magnified. 
 The WTP model generally uses a required compensation approach to survey 
individuals about their preferences. The model has been well studied, and most research 
closely follows the methodological recommendations of the NOAA Panel on Contingent 
Valuation (Arrow, Solow, Portney, Leamer, Radner and Schuman, 1993).  In crime 
research, WTP generally involves asking people what they are willing to pay to avoid 
being the victim of crime. Thus the model solves the problem of ex ante decision-making. 
However, the WTP model has two other serious problems. First, as a general rule, it 
overstates revealed references, since people will often express a willingness to pay for 
goods that exceed what they would actually be willing to pay if a real payment was 
required. Thus, research suggests that the dollar value developed in these models 
represents at minimum an upper bound of people's willingness to pay. Second, it is 
difficult for respondents to accurately estimate their willingness to pay in the presence of 
uncertainty about risk. Most serious crimes are rare events as on average Americans have 
a less than 1% chance of experiencing even the most common Part I crime of burglary 
(FBI, 2008).  Risk of victimization is heterogeneous with respect to age, wealth and many 
socio-economic factors (Tonry and Farrington, 2002), and risk aversion with respect to 
crime is similarly heterogeneous (Becker, 1968; Ehrlich, 1973). 
 This chapter is ordered as follows. The chapter begins with a brief review of the 
neo-classical economics literature on supply and demand of offending focusing on the 
development of market-based models that incorporate a demand function. Next, the 
 33
 
literature comparing the strengths and weaknesses of the WTA and WTP models is 
reviewed with particular attention to the three main estimation strategies: hedonic pricing, 
stated preference surveys and third-party compensation. Next, the Miller and Cohen 
studies that have applied jury compensation and cost of illness methods to estimate the 
costs of crime are reviewed. This is followed by a discussion of prior research on jury 
awards, and brief discussions of the issues related to estimating risk of death. 
 
Economic Models of Crime  
Development of accurate estimates of the value of harms experienced by crime 
victims plays a central role in the development of policy models to optimize the 
allocation of crime resources. Incorporation of these values into theoretical models of 
offending is particularly evident in the economics literature.  In general, there are two 
strains of economic theory about crime. The first, and by far the most dominant, is based 
on the pioneering work of Becker. Becker describes a model where offenders are 
suppliers of crime. The model specifies two functions: a supply of offenses function and 
a production function, specifically a social loss function. Offenders maximize their utility 
by comparing the expected gains from offending compared to costs measured as the 
certainty and severity of punishment. If a potential offender perceives that the benefits 
from crime, both pecuniary and psychological, outweigh the expected costs of crime (risk 
of being caught and incarcerated) then the motivated offender will commit a crime. The 
simple static models of Becker were extended by many economists, notably Shavell, 
Polinsky, Witte and Garoupa to accommodate the complex choices inherent in a criminal 
event. Most of the first generation of the economics of crime literature (Posner, 2005) is 
 34
 
concerned with the appropriate sanction to dissuade offenders from offending. If financial 
penalties, and penalties in the form of a loss of liberty, could be made sufficiently large, 
offenders would not commit crimes. The market described in this literature is a partial 
equilibrium model describing the changes in the supply of offenses from a mix of 
exogenous (public demand) and endogenous (private demand) factors. 
The other strand of economic theory is much less well populated, centered on the 
work of Isaac Ehrlich.  A contemporary of Becker?s, Ehrlich extends Becker?s model to 
include a third function ? that of derived demand for offenses. The model is solved using 
simultaneous equations to derive optimal levels of punishment to minimize social harm 
from offending. Most theorists who follow Becker and Ehrlich, however, focus their 
scholarship on extending the Becker model, to include uncertainty, variance in 
punishment strategies, time, and other complexities. Most of this literature neither 
explicitly includes a demand function, nor an accounting for the endogenous features of 
the supply and production functions. Regardless, the result has been an extremely flexible 
theory that can be used to evaluate the effectiveness of various punishment regimes on 
crime production. 
With the exception of Ehrlich (1981), economic theorists consider the crime 
problem from the perspective of the offender, what Ben-Sharar and Harel call a 
?perpetrator-centered perspective? (1996: 304). In these models, the focus is on changing 
incentives of offenders who supply crime, with only the briefest attention to potential 
victims, who are assumed to have a demand for victimization. The oddness of victims 
demanding crime is acknowledged by its authors: Cook (1986:19) calls it a ?strange-
sounding term,? Shavell accepts that it is ?unintuitive,? and Ehrlich notes that is ?seem[s] 
 35
 
paradoxical? (1981:309) and caveats that potential victims do not necessarily demand 
crime, but rather ?tolerate? it (1996: 49).  In general, economic markets are predicated on 
the idea that goods are exchanged voluntarily. When a market results in costs being 
imposed on an unwilling party, those costs are described as an externality, and are 
counted as a consequence of the exchange of a good, but are not included within the 
private market equilibrium. The analogy is akin to the problem of pollution, where costs 
of production of a good do not include the costs to society from the release of pollutants. 
The solution in the environmental literature is not to consider those costs as external to 
the market, but rather to internalize pollution costs within the production of the pollution 
causing good. Similarly, economic theory of crime considers crime to be an externality, 
and the goal of law enforcement is to cause criminals to internalize those costs. 
Serious investigation by economists on the impacts of crime began only in the late 
1960?s and early 1970?s. Becker (1968) proposed a supply model of crime to explain an 
individual actor?s decision to commit crime.  In Becker?s model, a potential offender?s 
decision to commit an offense can be understood using the standard economic choice 
principal of expected utility.  That is, an individual will decide to commit a crime if the 
expected benefits (minus expected costs) exceed the benefits from alternative activities.  
In this model, the number of crimes an individual commits is a function of the perceived 
risk of offending (e.g., the risk of apprehension (certainty), and if apprehended, the risk 
of punishment (severity)) compared to the perceived rewards/benefits (e.g. income/utility 
received as a result of the crime). Changes in policy that affect the probability of 
conviction and the probability of punishment deter offenders by increasing the expected 
certainty and severity of punishment.  In calculating the total cost of punishment, Becker 
 36
 
includes both costs to offenders (including earnings foregone while incarcerated) as well 
as the cost and/or gain to other members of society. 
Becker extends the model to evaluate optimal penalties for offending.  Applying 
the economic theory of choice to the supply model of offenses, the equilibrium price of 
punishment is in equilibrium when the monetary value of the penalties received equals 
the marginal external harm caused by the crimes (1968).  That is, optimal policy setting 
will equate crime prevention expenditures and the amount needed to compensate or 
minimize the loss to society that results from crime (although it is not necessary that the 
victim is directly compensated). The losses from crime include the sum of social 
damages--including victim losses--as well as the costs of detection, conviction, and 
punishment (Becker, 1968: 207).   
Becker does focus only on incapacitation, and argues instead that fines have 
advantages over other forms of punishments. According to Becker, fines use fewer social 
resources, can be used to compensate victims and society while punishing offenders 
(which is not the case when prison is used), and the adoption of fines simplifies the 
determination of the optimal punishment price.  Accordingly, the optimal amount of a 
fine should be determined based on the total harm caused by the offender.  While both 
fines and prison cause offenders to internalize the costs of offending, neither have a direct 
benefit to the victim. Prison and probation sentences are set equal to the amount of harm 
caused by an offender, but do not directly compensate victims. While fines could be used 
as transfer payments to compensate victims, in practice any transfer occurs in the civil 
rather than criminal justice system.      
 37
 
Becker applies this model to the development of optimal crime policy, asserting 
that the effectiveness of public policies is dependent on the costs of detection (certainty) 
and punishment (severity), and the elasticity?s of offenses to changes in the probabilities 
of apprehension and punishment (Becker, 1968: 205).  Thus, anti-crime investment is 
optimized when the costs of apprehension and conviction are minimized and the 
reduction in offending caused by a change in the probability of apprehension or 
punishment is maximized.  Becker suggests that elasticity?s may vary by type of offense 
with expressive crimes or crimes committed by youth being less responsive to changes in 
the probabilities of detection and punishment than instrumental crimes. Becker notes that 
Ehrlich (1967 in Becker, 1968: 205) did not find the elasticity?s of murder, rape and auto 
theft to be significantly smaller than those for robbery, burglary, and larceny.   
Becker?s supply model of crime explicitly includes private expenditures and 
actions aimed at reducing the number of crimes, such as hiring security guards, operating 
security alarms, or avoiding certain areas at night.  Becker develops a model for the 
optimal allocation of private anti-crime resources, where private expenditures are a 
function of optimal expected individual loss in income in much the same manner as the 
optimal public policy function described above.  Thus, optimal private expenditures and 
actions taken to prevent victimization would equal the expected harm or loss to 
individuals from crime. When the private and public models of optimal crime allocation 
are considered jointly, there is evidence of endogeneity where higher public anti-crime 
expenditures will result in reduced private expenditures.  
Ehrlich (1973) extends Becker?s supply model of offending using a model 
explaining offending as a function of a choice between legal and illegal actions.  Similar 
 38
 
to Becker, the choice to commit crime is based on risk tolerance, and legal and illegal 
opportunities.  As a result of differences in risk tolerance, potential offenders will differ 
in the degree to which the threat of detection and punishment will deter their future 
offending.  Ehrlich then extends his model of individual choice to an aggregated supply 
of offenses, which is the sum of all offenders? choices about whether to commit crimes 
given variation in perceived benefits and varied risk preferences. Those who are risk 
averse will not commit crimes even when penalties are small and potential gains are 
large, and those who are risk tolerant will enter the crime market even if risks are high 
and returns are small. Ehrlich predicts a number of factors will influence this decision 
including the level of assets in the community, as well as the individual?s educational 
attainment and legitimate opportunities. 
In this aggregated formulation, Ehrlich identifies the relationship between 
certainty and severity of punishment and the resulting incidence and prevalence of 
offending.  Thus, for the first time in the economics of crime literature, victims cost of 
crimes become an explicit variable in the offending model.  Ehrlich develops a 
production function of law enforcement where the productivity of increases in law 
enforcement expenditures on law enforcement (i.e. police and courts) is related to the 
level of crime. So, if law enforcement expenditures are constant higher crime rates will 
result in smaller probabilities of apprehension and punishment.  Ehrlich also notes that 
population size and population density are also expected to be negatively related to the 
probability of apprehension and punishment.  
The public demand for law-enforcement activity is described as, ?a negative 
demand for crime or a positive demand for defense against crime? (Ehrlich, 1968: 541). 
 39
 
Although Ehrlich recognizes that potential victims of crime may wish to engage in both 
private and collective self-protection activities, Ehrlich focuses on self-protection in the 
form of law enforcement activity.  Law enforcement activity that reduces the crime rate 
through increases in the probability of apprehension and severity of punishment benefit 
the public by reducing losses to victims.  Thus, Ehrlich introduces the idea that of a trade-
off between the costs of adding police and prison resources and the benefits of reduced 
victim losses. 
In later analyses, Ehrlich (1981) argues that the benefits of incarceration may be 
limited, as criminogenic forces may offset the deterrent effects of incarceration. That is, 
imprisonment may result in a decrease in ?legitimate knowledge and skills? and 
consequently cause an increase in recidivism rates of offenders after they are released.  
Additionally, a ?replacement effect? in which new offenders decide to enter the crime 
market or active offenders decide to increase their participation in criminal activity may 
also offset the incapacitation effect of punishment. Ehrlich (1981: 316, 1996: 62) 
suggests that the benefits of incapacitation should thus be attributed to general rather than 
specific deterrence.  The larger the elasticity of offending with respect to the certainty 
and severity of punishment the larger the general deterrent effect will be, and the smaller 
the specific or incapacitative effect.   
Shavell (1987) develops a model in which it is optimal to incarcerate an offender 
if the offender?s dangerousness (harm done each period if not imprisoned) exceeds the 
cost of imprisonment.  In this model, a prisoner is incarcerated only as long as his 
expected harm to crime victims exceeds the cost of imprisonment. Thus, any decrease in 
expected offending should be considered in assessing the efficiency of continued 
 40
 
incarceration. The Shavell model therefore requires explicit enumeration of the expected 
pattern of offending (commonly referred to as lambda in the criminology literature) 
conditioned on such predictors as age and receipt of rehabilitative services.      
More recently, Ehrlich (1996) extends the economic analysis of crime into a 
market model of crime, which explains the phenomenon of crime through a fully 
specified equilibrium model.  A key assumption of the model is that some level of crime 
is ?socially optimal? or tolerable (Ehrlich, 1996: 51). The supply of offenses and the 
demand for private and public protections from crime are jointly modeled to predict the 
optimal level of crime.  Using this framework, Ehrlich (1981, 1996: 48) expands upon 
Becker?s private expenditures model to derive a ?demand for crime or tolerance for 
crime? function, which is the inverse function of the demand for private protection.  
When aggregated with the supply of offenses model, higher crime rates result in 
increased self-protection efforts by potential victims, which result in reduced gains to 
offenders per offense. Reduced net gains are a result of the increased time and effort 
required to commit an offense when self-protection rates increase.  In the market model, 
offenders, law enforcement, and potential victims are all assumed to behave in 
accordance with the concept of optimal utility, with the distribution of preferences for 
crime and for safety assumed to be fairly stable in the short-term.  With crime defined as 
an external diseconomy, or a direct negative effect on welfare, and law enforcement 
being a ?non-exclusionary public good,? it follows that the main objective of law 
enforcement is the ?maximization of social welfare? (Ehrlich, 1996: 45).  Again, the 
model requires a specific enumeration of victim harms to estimate the equilibrium.  
 41
 
According to Ehrlich, the market model of crime will reach equilibrium when 1) 
the public has made its optimal investment in crime control, 2) offenders have made 
optimal decisions on how many offenses to commit based on perceived risks and 
rewards, and 3) individuals have made their optimal private investment in self-protection 
from crime (1996:51).  The equilibrium level of crime is dependent on the shapes of the 
supply of offenses and the derived demand for crime curves.  Changes in sentencing 
guidelines and court holdings, which impact probabilities of arrest, conviction and 
punishment, will result in long-term shifts in the equilibrium of the crime market.  
According to this model, effective rehabilitation and incapacitation policies should result 
in ?a leftward shift in the aggregate supply-of-offenses,? or a decrease in the number of 
offenses (Ehrlich, 1981: 312).    
The market model therefore allows for the evaluation of the relative efficiency of 
competing policies. For instance, Ehrlich suggests that the effect of rehabilitation 
programs on crime is more complex than typically presented.  Although effective 
rehabilitation programs may reduce offender supply of crime, rehabilitation also offers 
?an implicit subsidy? to potential offenders in the form of ?training and employment 
benefits at public expense? (Ehrlich, 1981: 315).  Ehrlich argues that the rehabilitation 
benefits experienced by offenders post program result in a ?counter-deterrent effect on 
potential offenders,? which could potentially increase the crime rate.   
Ehrlich (1996: 53) also suggests that policies that create ?general incentives? to 
desist from crime must be jointly modeled with policies that create ?specific incentives? 
to desist from crime. ?General incentives? are policies?such as the levels of fines for 
offending?or broader market forces such as the availability of legitimate wages that 
 42
 
impact all citizens including offenders and non-offenders.  By contrast, ?specific 
incentives? such as incapacitation and rehabilitation largely impact convicted offenders 
alone.  Thus, Ehrlich (1996: 53) suggests that it is not sufficient to evaluate the 
effectiveness of specific incentives (i.e. rehabilitation programs) at the individual 
offender level, since he finds that in a broader analysis of the entire crime market these 
programs have a limited impact on the aggregate flow of offenses.  By contrast, ?general 
incentives? which likely have a weaker impact at the individual-level, may be more 
effective at the market-level, since they influence the ?entry and exit of marginal 
offenders? in the crime market (Ehrlich, 1996: 54).      
 The models of crime developed by Becker and Ehrlich have been criticized along 
several dimensions.  Although extended by Ehrlich to include the derived demand for 
crime, the model is focused largely on offender decision-making. The model assumes that 
crime can be deterred, and thus is open to the criticism (originating with Becker) that the 
model is most applicable to crimes involving monetary gains to offenders, and is less able 
to explain non-economic crimes.   Other critics note that the Becker and Ehrlich models 
focus primarily on ?crime?s pecuniary returns and financial costs associated with state 
sanctions,? without directly addressing psychic returns which are more important in 
understanding non-instrumental offending (McCarthy, 2002: 422).   It has also been 
suggested that  ?the economic benefits of crime are so meager that they cannot be 
realistically viewed as incentives,? and that the social costs associated with crimes not 
measured in the model, greatly exceed the costs of state sanctions and lost wages 
(McCarthy, 2002: 426-427; Nagin, 1998). 
 43
 
Additionally, the theoretical variables of the market model are difficult to 
measure, as Ehrlich notes (1996).  A major challenge is isolating the causal effect of law 
enforcement activities on crime rates, while ensuring that the estimated relationship does 
not reverse the true effect (since the crime rate and law enforcement activities are 
endogenous).  The solution is to include exogenous variables in the demand or production 
functions of law enforcement that are excluded from the supply model of crime (Ehrlich, 
1996).  Identifying data that captures such exogenous variables has proved to be 
extremely difficult.  Ehrlich (1996: 60) suggests a promising approach is to, ?quantify 
political or institutional factors that affect either law enforcement budgets or ?rules of the 
game?.?  Applying this strategy, Levitt (1996) uses the instrumental variable of the status 
of state prison overcrowding litigation to estimate the effect of prison populations on 
crime.  Levitt (1996: 348) finds that, ?incarcerating one additional prisoner reduces the 
number of crimes by approximately fifteen per year.? Determining whether the social 
benefits of incarceration are worth the costs is thus entirely dependent upon the price of 
crime of each incident where a criminal victimization was prevented, either due to 
specific deterrence (the incapacitation of expected recidivist) or general deterrence.   
  
Applying the Law and Economics Literature to the Study of Crime 
Clearly, it is necessary to develop accurate estimates of the costs to victims of crime to 
estimate the efficiency of competing crime control policies and programs. The optimal 
model for measuring crime victim?s harms would observe the ex ante amount of 
precaution taken by private citizens, the amount of public anti-crime resources, and the 
resulting risk of victimization at the equilibrium crime rate. The amount of resources 
 44
 
dedicated to crime prevention would then be differenced by the risk of victimization 
yielding the expected cost per type of expected victimization. These values could then be 
applied to estimates of the various crime reduction benefits of competing policies and 
programs to identify more effective approaches. Or, ideally, the estimates could be 
factored into a general equilibrium or simultaneous equations model such as proposed by 
Ehrlich, to identify optimal investment in law enforcement.  
 There are several challenges to this model. First and foremost, there is no true 
private market for the exchange of crime. While individuals may enter a private market to 
exchange crime prevention goods, such as security alarms, the criminal event itself is not 
really a market exchange, since the victim is an involuntary participant. Second, the 
market is a mix of private demand from crime prevention and public crime prevention 
which is a quasi-public good.  Thus, as will be discussed later, the public investment is 
likely to be sub-optimal, since there is an incentive for participants to free ride on the 
investments of others.  And third, as a result of the first two points, it is therefore very 
difficult to develop a true ex ante measure of the amount a potential victim is willing to 
pay to avoid victimization, or conversely, the amount the victim is ex ante willing to 
accept to be made whole after being victimized.  
 
Properties of a Good Price Estimator 
As a result of these challenges, it is difficult to develop a single approach that robustly 
measures price. Before discussing the approaches that are commonly used to estimate 
prices that are not directly observable, it is worthwhile to consider the properties of a 
 45
 
good price estimator. The key conceptual properties of a good estimator include a 
preference for: 
? Ex ante to ex post; 
? Observed behavior in real markets to behavior in shadow markets;  
? Revealed preferences over stated preferences; and, 
? Estimates observed at the societal level, rather than aggregated individual 
preferences. 
Conceptually, the first three issues are discussed at length in the neoclassical economics 
literature. The fourth issue is discussed in the section that follows.  
Two approaches are commonly used in neoclassical (welfare) economics to value 
a policy change (Hicks, 1939).  Compensating variation (willingness to pay, or WTP) is 
the ?the maximum amount of income that could be taken from someone who gains from 
a particular change while still leaving him no worse off than before the change.?  
Equivalent variation (willingness to accept, or WTA) is the ?the minimum amount that 
someone who gains from a particular change would be willing to accept to forego the 
change? (Pearce, 1992: (78), in Leung and Sproule, 2007).  Thus, both of the approaches 
meet all three of the criteria for a good estimator described above: revealed preferences 
are observed ex ante in a functioning marketplace.  Notably, the equivalent variation 
(WTA) approach estimates the amount necessary to make an individual prior to a policy 
change. The jury compensation strategy used in this analysis employs the same logic as 
equivalent variation, but the jury award is rendered post hoc by a third party rather than 
ex ante by the affected individual. Thus, the jury compensation award is a proxy for ex 
ante WTA.  
 46
 
In the economics literature, use of WTP is far more prevalent than WTA. For 
example, Cook and Graham (1977) note that: 
The individual probability of loss in many cases is influenced by public activities 
such as law enforcement, highway design, and medical research. Investments in 
such areas produce a good (reductions in the probability of loss for each of a 
number of individuals) that, from an efficiency point of view, should be valued at 
an amount equal to the sum of the resulting benefits accruing to individuals.  E. 
Mishan points out that the appropriate individual benefit measure in such cases is 
the "compensating variation" in wealth: the reduction in the individual's wealth, 
which, when coupled with a reduction in the probability of loss, leaves him at the 
same (expected) utility level. 
 
Practically, most market transactions are assumed to reflect a WTP strategy. In a choice 
between two otherwise identical homes, different prices that reflect different expected 
safety from crime reflect differences in willingness to pay to avoid victimization rather 
than differences in willingness to accept being victimized.  
While WTP is more prevalent in the literature, historically economists have 
assumed little consequence between the choice between equivalent and compensating 
variation.  Brookshire, Randall and Stoll (1980) note that with a change in quantity, WTP 
represents the maximum price a buyer is willing to pay and WTA is the reservation price 
of the seller, or the minimum price the seller is willing to accept for a good.  Under 
perfect competition, the price should be equivalent.  In a recent paper challenging the 
conventional wisdom in using WTP in Slutsky equations, Leung and Sproule (2007:4) 
test whether WTA and WTP result in different valuations, and find that ?[t]he dominance 
of one vantage point over the other is arbitrary and? potentially misleading.?  However, 
recent empirical studies have found that WTA tends to produce larger estimates in 
applied research (although the theoretical explanation for the difference is unclear).  This 
difference in the size of estimates is a criticism of the jury compensation method which 
 47
 
tends to produce larger estimates than a WTP estimate would (though this may be due to 
the ex post nature of the jury award rather than the WTA approach) (Cook and Ludwig, 
2000).  
Costs to Society 
A key goal of any willingness to pay strategy is to generate an estimate that can be used 
to measure changes in net social welfare.  Ultimately, the goal of policy analysis is to 
determine if the net social welfare change from one policy exceeds the net social welfare 
change from a competing approach.  In a market with perfect competition, those 
estimates can be derived in a straightforward manner. Since each individual actor in the 
market maximizes their utility, the sum of the costs and benefits to each individual in 
response to a change in price is equivalent to the change in net social welfare.  Under 
those market conditions, the assumption that the jury compensation is equivalent to the 
equivalent variation is relatively modest.  Hanneman (1991) finds that CV and EV are 
equal when the good in question has a perfect market substitute (Cook and Graham 
(1977) however suggest safety is an irreplaceable commodity and thus there is no 
substitute).  If it can be shown that juries are instructed to make an individual whole after 
they experience some loss, then a case can be made that the jury award is a relatively 
strong instrument for the equivalent variation.   
A review of a sample of state guidance on instructions to juries about how 
damage?s should be calculated suggests that the jury is told to make an award that is 
 48
 
sufficient to make a defendant whole after a loss. The following is an example of 
guidance to judge?s in charging a jury drawn from Connecticut
6
: 
The rule of damages is as follows.  Insofar as money can do it, the plaintiff is to 
receive fair, just and reasonable compensation for all injuries and losses, past 
and future, which are proximately caused by the defendant's proven negligence.  
Under this rule, the purpose of an award of damages is not to punish or penalize 
the defendant for (his/her) negligence, but to compensate the plaintiff for 
(his/her) resulting injuries and losses.  You must attempt to put the plaintiff in 
the same position, as far as money can do it, that (he/she) would have been in 
had the defendant not been negligent. 
 
Thus, it can be argued that jury awards are a strong proxy for an estimate of equivalent 
variation, though somewhat weaker than an ex ante estimation. In a market with perfect 
competition, the assumption that the aggregated individual damages are equivalent to 
social cost is relatively weak. 
In the case of a price change where there is substantial governmental involvement 
in the market, e.g. where the good in question is a quasi-public good, that assumption is 
stronger.   In the case of crime prevention, the government plays a substantial role in 
setting the price.  Police, prosecution and corrections activities that affect the supply of 
crime are public goods. These goods are non-rival (use by one does not preclude use by 
another) and non-exclusive (no individual can be excluded from their use).   
In practice, the crime prevention market has both a quasi-public good element and 
a competitive market element.  Society makes an investment in crime prevention in the 
form of police, courts and corrections. Individuals then evaluate whether to make 
additional investments in crime prevention, in the form of private police, and other 
                                                 
6
 Civil Jury Instructions, State of Connecticut Judicial Branch. Retrieved March 14, 2009 from 
http://www.jud.ct.gov/JI/civil/part3/3.4-1.htm.  
 49
 
private crime precautions. The two markets are endogenously determined ? an increase in 
public investment is likely to lead to a decrease in private precaution. 
Conceptualizing crime prevention as a quasi-public good has important 
implications for the estimation of prices to victims.  That is, in addition to the other 
properties of a good price estimator, it must also be the case that the price estimate (the 
sum of the product of prices and prevalence) must be equal to society?s willingness to 
pay for those goods. Willingness-to-Pay approaches can employ either a micro- or a 
macro- approach to valuing costs to society (as is discussed later, hedonic pricing 
approaches tend to estimate social costs by aggregating micro-observations).  Crime 
control studies applying neoclassical economic theory prefer a macro approach (Cook 
and Ludwig, 2000; Cohen, Rust, Steen and Tidd, 2004) where costs to society are valued 
at the societal level. Cook and Ludwig estimate the social costs of gun violence using a 
WTP approach, where survey respondents are asked (103): 
Suppose that you were asked to vote for or against a new program in your state 
to reduce gun thefts and illegal gun dealers. This program would make it more 
difficult for criminals and delinquents to obtain guns. It would reduce gun 
injuries by about 30% but taxes would have to be increased to pay for it. If it 
would cost you an extra [$50/$100/$200] in annual taxes would you vote for or 
against this new program?? 
 
The approach is ?macro? in nature since the reduction in crime (and social costs) is 
observed at the societal, rather than individual level.  Thus, the approach measures public 
safety, rather than aggregated individual harm.  
By contrast, the cost-of-illness and jury award approaches estimate social cost 
from aggregated individual-level data, and thus the approach can be described as a micro-
level study.  Calculation of crime prices from jury awards applies a relatively 
straightforward algorithm, where average treatment effects are transformed into a 
 50
 
monetized value. Thus, if one year of prison deters 15 future offenses, then the sum of the 
price of each of those 15 offenses is the estimate of the total benefit from prison (Levitt, 
1996).  Jury awards are used to estimate the price of each of those prevented crimes, and 
the total cost is the sum of these individual-level prices.  
But, since prison is a quasi-public good, summing micro-level benefits may yield 
a total social benefit that is not equal to society?s valuation of those benefits. In practice, 
it is likely that ?society? puts a relatively higher value on that reduction in harm. Since the 
expected victim of a crime cannot be known in advance, and since the average citizen 
does not experience any felony victimizations in a given year, it is reasonable to presume 
that the typical citizen will place a higher value on the benefit of that reduction in 
victimization than would be developed from an ex post estimate of victim losses. The 
main reasoning behind this assumption is that in addition to a willingness to pay to 
prevent their own losses, the average citizen would also seek to limit the losses of others 
including friends and neighbors. Thus, a willingness to pay survey is likely to elicit a 
higher valuation of the benefits of reducing crime than would be derived from a WTA 
estimate using the jury award method.  
Thus, two problems emerge. The first is the problem related to the endogeneity.  
Since the macro-approach tends to lead to smaller investments in crime prevention 
through the mechanisms described above, those individuals who are more risk averse in 
crime may choose to increase their investment in crime prevention.  However, as noted 
above, it may well be that the individuals at greatest risk of crime may have the fewest 
means to privately protect, and thus the change in private crime prevention may well be 
smaller than a utility maximizing model may predict. 
 51
 
A more serious problem is that of free riders and a resulting under-investment in 
the quasi-public good.  A well known phenomenon in welfare economics, the free rider 
problem emerges because individuals choose to sub-optimally investment in public goods 
in expectation that others will make up the difference. Thus, the macro-WTP faces this 
threat?if survey respondents observe that they can free ride, they will respond to the 
survey with a lower willingness to pay than if the good was competitively exchanged. 
This problem is addressed in contingent valuation that use a referendum method, but 
remains in studies that do not. Finally, the criticism remains that individuals may state 
preferences that are larger than their revealed preferences.   
The jury compensation method thus has some attributes that make it relatively 
attractive in evaluating prices of the crime market.  Since the micro-WTP tends to 
overestimate harms, and the macro-WTP underestimates due to free riders, a third party 
ex ante estimate may fall somewhere in the middle. There is little empirical research to 
support or refute this claim. However, jury awards are almost always less than the 
specials (damages) claimed by civil plaintiffs which is at least suggestive that the awards 
would be less than an ex ante solicitation of compensating variation.  A similar analysis 
cannot be undertaken comparing jury awards to macro-WTP estimates, but given that 
there is no free rider problem in jury awards, it seems reasonable to conclude that the jury 
awards will be somewhat greater than the macro-WTP estimates. 
 There is a substantial research literature that describes estimates of crime-related 
goods using all three of the methods described above ? hedonic pricing, contingent 
valuation and jury compensation (cost of illness). The section that follows reviews those 
 52
 
studies, with particular attention to jury compensation approaches to estimating the price 
of crime. 
Hedonic Pricing 
Economic theory posits that the price of any good or service that is exchanged in a 
competitive market is a function of the attributes of that product. A consumer in the 
market to purchase a television will likely choose a product based on a series of attributes 
related to price. Some are easily observed: what is the size of the monitor? Is it analog, 
digital, high definition or plasma? What is the depth of the screen? What is the wattage of 
the speakers? How long is the warranty? Others are harder to quantify: what color of 
casing does the consumer prefer? Is the supplier perceived as having a high quality brand 
name? The consumers' willingness to pay the market price will be based on both sets of 
preferences, and many others.  
In the study of crime, it has been observed that perceived risk of crime is included 
in this calculation - the hedonic price function - for many goods and services (Clark and 
Cosgrove, 1990; Thaler and Rosen, 1975; Thaler, 1978). Two in particular have received 
significant research: differences in property values due to risk of crime and compensating 
differentials in wages. Both approaches are used to develop estimates of the social costs 
of crime.  
The most common application of hedonic pricing is the study of differences in 
property values.  The general strategy is to compare the property values of two 
comparable neighborhoods or houses, and control for all observable differences: the size 
of houses, number of bathrooms, type of structure, proximity to urban areas, etc. The 
remaining differences in property values can be at least partially attributed to 
 53
 
unobservable attributes, including crime rates, on the assumption that ceteris paribus 
higher crime rates are associated with lower property values. The alternative approach, 
compensating wage differentials, applies the same concept, but compares differences in 
wages where the same job is being performed in high and low crime areas. 
The approach satisfies three of the four attributes of a good price estimator. 
Estimates are ex ante, expressed as revealed preferences, and the good is exchanged in a 
private marketplace. If successfully implemented, price estimates will approximate 
revealed preferences making them preferable to willingness-to-pay surveys (Clark and 
Cosgrove, 1990).  Generally, the estimates for social cost are estimated as the sum of 
individual choices rather than as society-level valuations, but as previously discussed; the 
exchange of the good in a competitive market reduces the importance of this assumption. 
Another benefit to the hedonic market approach include is that all of the attributes of 
criminal victimization as the method ?incorporates psychic costs associated with actual 
and potential victimization? (Clark and Cosgrove, 1990: 106).  While Becker (1968) and 
Ehrlich (1973) described a framework for understanding hedonic crime and crime control 
markets, few hedonic market studies have been undertaken.  A small number of studies 
have observed changes in housing prices or wages to infer the demand for public safety 
(Thaler, 1978; Thaler and Rosen, 1976, Clark and Cosgrove, 1990). 
Using the hedonic pricing approach, Thaler (1978) seeks to estimates consumers? 
willingness to pay for lower crime rates by estimating the effect of crimes on property 
values, and then inferring homeowners? preferences from these estimates.  Thaler (1978) 
used property crime data from Rochester, New York in 1971 on a random sample of 398 
single-family homes sold in the City of Rochester during 1971 (from Maser, S., Riker, 
 54
 
W. & R. Rosett, 1997) in combination with a census geo-coding program to calculate the 
per capita crime by census tract.  Thaler finds that ?an increase of one standard deviation 
in C (property crimes per capita ? probability of an individual being victimized by a 
property crime) decreases the price per acre by $3,847 or roughly $430 per house,? which 
represents, ?about 3% of the average price per home in the sample? (Thaler, 1978: 142).  
Thaler estimates the cost of an average property crime to be about $500 (about $1,600 in 
2008 dollars), with the caveat that the estimates are based on a small sample from a 
single jurisdiction.    
Clark and Cosgrove (1990) estimate household demand for public safety using a 
two-stage intercity hedonic model that extends the Roback (1982) and Hoehn, Berger, 
and Blomquist (1987) models that estimate an inverse demand function for public safety.  
Data in the study are developed from the Public Use Microdata Sample (PUMS) of the 
1990 Census of Population and Housing and include wages, structural features of homes, 
and individual characteristics.  Clark and Cosgrove (115) estimate the level of public 
safety as, ?the inverse of the predicted murder rate at each location,? and argue that 
individuals can choose, ?any level of public safety by choosing the appropriate location 
within a given city or by moving between cities within the same region.? They specify a 
hedonic-rent equation to estimate the implicit price of public safety and estimate a crime-
rent elasticity of -0.13.   
In the second stage of the model, an ex-ante willingness-to-pay function is 
derived from the first-stage hedonic function in order to estimate revealed preferences for 
public safety.  Clark and Cosgrove find that demand for public safety is relatively price 
inelastic, and that the demand for public safety with respect to income approaches one.  
 55
 
Other significant findings include that, 1) married couples? willingness to pay is 
significantly higher than that of single individuals, 2) the effect of education is positive 
and significant, 3) residents in central cities are less willing to pay than their suburban 
neighbors, and an interesting finding that 4) ?willingness to pay is minimized at a city 
size of 1.7 million persons? (120).   
There have been few attempts to use the hedonic pricing method to estimate the 
prices of specific crime types.   The primary application of hedonic pricing is to estimate 
the value society places on saving a ?statistical life?.  Rather than housing data, this 
literature relies on labor market data on wage rate differentials for heterogeneously risky 
jobs (Viscusi, 1993).  Individual attitudes toward risk (willingness to accept risk and the 
marginal willingness to pay for greater safety) are inferred from observed wage-risk 
tradeoffs made by a worker?s choice of employment.  Reasonable estimates of the 
?statistical value? of a human life range from $3 million to $7 million (Viscusi, 1993). 
Some have chosen to interpret the meaning of a statistical life as the monetary amount 
that society is willing to pay in order to change the ?fatal risks faced by a group of 
people,? rather than ?saving the life of an identified person? (Kenkel, 1998: 797, see 
Shelling, 1968).  However, since the approach uses aggregated individual data, it appears 
that existing estimates are better interpreted as the latter meaning.  
The primary limitation of the use of the hedonic market pricing approach in the 
evaluation of crime control interventions is that these studies have a high noise-to-signal 
ratio.  The Thaler study, for example, estimates that crime accounts for about 3% of the 
value of a home. If there is unobserved heterogeneity in housing prices (such as different 
tastes for aesthetics) that explains more than a small fraction of the value of a home, as it 
 56
 
almost certainly does, then that statistical noise will make recovery of the small crime 
signal difficult.   And, assigning values to crime rather than some other attribute (such as 
clear air or clean water) is often difficult to empirically support.  
As a result of data limitations, hedonic market property value studies have been 
unable to isolate the costs of any individual crime type (Cohen, 2000). Additional 
limitations to property value studies are their reliance on assumptions about housing 
market competitiveness and consumers? knowledge of neighborhood crime rates (Cohen, 
2000).  Although a few studies have investigated the impact of crime on both property 
values and wages (see Clark and Cosgrove, 1990; Hoehn, Berger, & Blomquiest, 1987), 
it does not appear that any studies have gone so far as to incorporate the two models in 
order to explain the interaction between housing prices and wages.   
 
Contingent Valuation 
Contingent valuation methods are generally applied to policy questions in situations 
where there are no competitive market data. Contingent valuation estimates are generally 
conducted as surveys of consumers of a good to elicit estimates of the amount they would 
be willing to pay for public good being studied.  The CV methodology was developed in 
the environmental economics literature, and has used to measure non-market goods such 
as clean air and saving endangered species (Cohen et al., 2004).   The CV methodology is 
also known as ?hypothetical valuation? since survey respondents are asked how much 
they would be willing to pay for some good in a hypothetical situation (Boardman, 2001: 
358).  Although CV has been frequently used in other fields, particularly environmental 
 57
 
economics, this methodology has not been commonly used in criminal justice research 
(Cohen et al., 2004).   
 The CV approach has been extensively studied. In 1993, the NOAA Panel on 
Contingent Valuation released a report that included recommendations for future CV 
studies. The report (5) also succinctly describes the strengths and weaknesses of CV: 
The CV technique is the subject of great controversy. Its detractors argue that 
respondents give answers that are inconsistent with the tenets of rational choice, 
that these respondents do not understand what it is they are being asked to value 
(and, thus, that stated values reflect more than that which they are being asked to 
value), that   respondents fail to take CV questions seriously because the results 
of the surveys are not binding, and raise other objections as well. Proponents of 
the CV technique acknowledge that its early (and even some current) 
applications suffered from many of the problems critics have noted, but believe 
that more recent and comprehensive studies have already or soon will be able to 
deal with these objections.  
 
The CV methodology, as applied to crime control research, directly surveys the 
public to estimate ex ante willingness to pay for crime reduction (Cohen, 2000: 286.)   
Ludwig and Cook (1999) conducted a nationally representative survey of 1,204 adults in 
1998 to estimate the demand for crime reduction.  Because they interpret the CV survey 
responses as representing household willingness to pay, Cook & Ludwig (1999:12) 
include household-level covariates in their maximium-likelihood estimate model. They 
find that the mean WTP per household for a 30 percent reduction in handgun injuries 
equals $239.  At the aggregate level, ?a 30 percent reduction in gun violence is worth 
$23.8 billion to the American public in 1998 dollars, around $750,000 per injury? 
(Ludwig & Cook, 1999: 15).   Similar to the wage-risk tradeoff estimates of a statistical 
life by Viscusi (1993), the estimates of Ludwig & Cook (1999: 15) indicate a range 
between $4.05 and $6.25 million value per statistical life.   
 58
 
Zarkin, Cates and Bala (2000) conducted a study using the CV survey 
methodology to estimate the social benefits of drug treatment programs. Using a mall-
intercept approach, 393 respondents in Triad, North Carolina and Brooklyn, NY were 
surveyed about their willingness to pay for expansions of existing drug abuse treatment 
programs.  The survey also contained questions on attitudes toward drug abuse treatment 
and familiarity/exposure to the substance abuse problem.  Respondents in each 
community were asked about their willingness to pay for expansion of a treatment 
program that targets all drug users as well as one that treats only women drug users. Two 
versions of the survey were developed in order to estimate the effect of size increase on 
WTP estimates, with one version estimating the treatment of 100 additional individuals 
and the other version estimating the treatment of 500 additional individuals.  The two 
WTP questions were each preceded by a two-paragraph description of the drug abuse 
problem and the benefits of successful drug treatment. A ?payment card? CV question 
format was used where the respondent was given a series of dollar amounts and asked to 
choose the amount that represents his maximum willingness to pay.  Zarkin et al. found a 
mean WTP for a substance abuse treatment program that successfully treats 500 drug 
users of $30.90.  The mean WTP for a substance abuse treatment program that treated 
500 women drug users was $41. However the difference between this estimate and the 
estimate for the program targeting all drug users was not statistically significant (Zarkin, 
Cates & Bala (2000).    While the Zarkin study retains many of the advantages of WTP, 
the use of a number of program recipients rather than a percentage, means the study is 
micro-WTP and subject to the criticisms about the use of the results to generate social 
costs. 
 59
 
Cohen et al. (2004) used the CV methodology to estimate the public?s willingness 
to pay for crime control programs. Telephone interviews were conducted with a 
nationally representative sample of 1,300 individuals. Respondents were asked, ?if they 
would be willing to vote for a proposal requiring each household in their community to 
pay a certain amount to be used to prevent one in ten crimes in their community.? 
Respondents were asked about three of five crimes, including 1) burglary, 2) serious 
assault, 3) armed robbery, 4) rape or sexual assault, and 5) murder, and the amounts of 
money they were asked if they would be willing to pay were randomized in $25 dollar 
increments between $25 and $225.   Results of the study indicated that, ?the typical 
household would be willing to pay between $100 and $150 per year for crime prevention 
programs that reduced specific crimes by 10 percent in their communities, with the 
amount increasing with crime seriousness? (105).   
 Aggregate estimates from the survey, ?imply a marginal willingness-to pay to 
prevent crime of about $25,000 per burglary, $70,000 per serious assault, $232,000 per 
armed robbery, $237,000 per rape and sexual assault, and $9.7 million per murder? (ibid).  
Interestingly, while jury awards are hypothesized to be greater than estimates from WTP, 
the Cohen et al, estimates are 1.5 to 10 times higher than prior estimates of victim costs 
from jury awards by Miller, Cohen and Wiersema (1996).   Cohen et al. note that their 
estimates are consistent with those of Cook and Ludwig (2000) who found an average 
household willingness-to-pay to reduce handgun violence of about $200 per year, with an 
aggregate estimate of about $1 million per gunshot injury.  
Although Cohen (2000) suggests that properly conducted CV surveys have the 
potential to be ?useful policy tools,? he also cautions that ?any method that asks the 
 60
 
public their willingness to pay for reduced crime inherently must confront the fact that 
the public might be misinformed about the risk and severity of crime.?  Finally, Zerbe 
(1998:439) suggests that this technique may be subject to aggregation bias, ?which arises 
because the value reported as the WTP by respondents varies inversely with the number 
of items presented for valuation.?   
 
Jury Awards 
As noted in Chapter 1, the costs of crime to victims literature is dominated by the 
work of Cohen and Miller, although there are a handful of other papers by other authors 
(notably Rajkumar and French, 1997)  The logic behind the jury award approach is 
straightforward. Some victims of criminal acts will seek to have the costs of their harm 
internalized by the offender (or other liable party), and will use the tort system as the 
means of recovery. When plaintiffs win a case, compensatory awards are made in two 
domains:  1) an award for the recovery of direct costs to victims and 2) an award for the 
recovery of intangible (pain and suffering) costs.  While data are available about both 
direct and indirect harms to crime victims, the Miller and Cohen literature generally uses 
the indirect harms as a way to weight direct costs of crime, which they tend to draw from 
other secondary, macro-level data.   
The first study of the costs of crime to victims was conducted by Cohen (1988). In 
the study, Cohen did not directly acquire jury award data, but rather used the parameter 
on the ratio of direct to indirect costs to use as a weight in the analysis of other secondary 
data. The data used in this study was drawn from data provided by Jury Verdict Research 
(JVR, which is the source of jury data for the other Miller, Cohen studies).  JVR collected 
 61
 
data on more than one hundred thousand civil cases involving a personal injury, where 
most of the plaintiffs were not injured in the commission of a crime. Since the JVR data 
did not directly link awards to crime types, Cohen used the relationship between direct 
and indirect costs as a means of weighting data from multiple other sources to account for 
pain and suffering. Figure 2 describes the approach used by Cohen. 
 Cohen assumes that the functional relationship between direct and indirect costs for 
all crime victims follows the functional relationship from the JVR parameter. Cohen uses 
the JVR parameter to estimate the intangible award for any case with an injury, and 
combines these data with the injury rates associated with different crime types to estimate 
direct costs. Cohen then estimates direct costs for other types of crime from the National 
Crime Survey (NCS), and calculates a risk of death statistic from FBI data as an added 
weight to the direct and indirect costs. These data are then combined to yield a total cost 
estimate for a variety of crimes.  
 62
 
INSERT FIGURE 2 ABOUT HERE 
Figure 2. Conceptual Map of Cohen (1988)
 63
 
There are several important limitations of the Cohen (1988) approach. First, as with later 
studies, limitations in the data prevent Cohen from directly estimating the direct or 
indirect costs of crime for all crimes. Second, he assumes?but does not test the 
assumption?that awards for non-criminal torts are equivalent to criminal torts. Third, 
Cohen cannot directly observe indirect costs of crime, including fear of crime and risk of 
death from the jury award or personal injury data. Instead, he must rely on several 
additional and unrelated data to make these estimates. As shown graphically in Figure 2, 
this meant linking data from many sources, at different levels of aggregation, often with 
small sizes. Thus, a substantial number of assumptions were required to link these data. 
Fourth, since Cohen uses a single parameter to estimate the relationship between direct 
and indirect harms from crime, he implicitly assumes that individuals all have the same 
relationship of direct to indirect harm.  Thus, while this paper pioneered a new approach 
to estimating the value of harms from crime, the paper itself was empirically limited, and 
much of the MC work of the next decade in this area was devoted to addressing those 
limitations. 
 
Prior Research Modeling Jury Awards 
Miller and Cohen (writing with Wiersema) took a different approach to estimating 
the price of crime for a series of papers culminating with a National Institute of Justice 
report that has been widely cited (1996).  The 1996 paper is written for a general 
audience, and thus contains only a limited description of the method used to obtain the 
results. A later (unpublished) study describes the results of a study to estimate harms to 
victims of sexual assault and assault, and the paper notes that ?[t]his methodology was 
 64
 
used for the purpose of estimating the cost of various types of crimes and injuries in 
Miller Cohen and Wiersema (1996)? (1999:15).  
The method described in that paper is as follows. First, MC note that they are 
missing past losses for about 40 percent of their sample in assault cases. Since they would 
like to include these data in their model predicting jury award, they impute the values for 
missing data by regressing past losses on injury attributes (they note that when 
transformed from logs to dollars, the imputed values were much lower than observed 
values). They repeat the process for sexual assault cases, but are less certain about their 
imputed estimates, as past losses were missing in 65 percent of cases and thus there was 
limited support space for their imputations. 
Having recovered past losses for their sample, MC then test whether their 
regression model explains variance in jury award (the model is described in Chapter 1 as 
equation (1)).  They report that, ?the regression equation does an extremely good job of 
predicting jury awards around the mean level of the independent variables? (14). As 
evidence to support this assertion, they note that the when the mean jury award (the 
dependent variable) from their model is transformed from a logged value back to a 
monetized value it is very close to the unadjusted mean of the entire sample.   
This analysis does not appear to support their conclusion that the regression 
models are a good fit for their data. Basically, MC regress total jury award for each 
individual on the part of the jury award for direct compensation, and a set of covariates 
describing particulars of the case. The regressions are run separately for each crime type, 
so type of crime is not included in the model. Thus, MC do not predict jury award by 
crime type, but rather predict how components of a crime affect the award (although it is 
 65
 
not clear why they would include the award for direct costs on both sides of the 
equation). The usual interpretation of this type of model would be that ? is the expected 
award for any award of this type, ?
1 
is the marginal award for past and future tangible 
losses, and some other coefficient can be interpreted as the marginal award for intangible 
costs, ceteris paribus. They do not, however, include a term for intangible losses. The 
total expected award is estimated as the sum of these marginal awards and the intercept. 
 Miller and Cohen state that the goal of their model is to describe ?the functional 
relationship between jury awards and independent explanatory variables? (14). They 
assume that each of the parameters in the regression is a component of the jury award, 
and that the average jury award can be estimated by summing all of the parameters. As 
they note, ?[b]y multiplying each coefficient in Table 6? by it?s corresponding mean 
value, one can estimate the predicted level of compensation? (14).  In fact, they do not 
appear to do this. Instead they note that the total award (once the data are transformed 
from logarithms back to dollars) is ?$47,908, of which $3,229 is past and future losses? 
(14). However, $3,229 is not the product of the coefficient and the mean values of 
LOSSES, but simply the transformed value of the mean of LOSSES. It should be noted 
that the $47,908 ?predicted? cost of sexual assault/rape is not an estimated value either ? 
it is also more or less just the uncorrected average of all observed jury awards (more on 
this below). In fact, none of the cost of crime estimates presented in MC (1999) are 
regression parameters ? all of them are simply raw average values that have been 
transformed into logs and then transformed back into dollars. 
However, even if they had taken the product of the coefficient and the mean value 
for each variable, it is not clear what to make of their interpretation. In essence, MC has 
 66
 
estimated that the average cost of each crime as the sum of the product of the coefficients 
and means of all RHS variables. If the model is correctly specified for an OLS regression 
then the mean of the error term will be 0 and thus, by construction, the average dependent 
variables will be equal to the sum of the estimated RHS variables. MC notes that this is in 
fact the case for both the models they specify. As a result, their regression results do not 
contribute new information about the dependent variable ? the estimated costs to victims 
of crime are simply the average values of the jury awards.  
The goal of this analysis for MC is to establish a functional relationship between 
jury awards and attributes. Once this is established, estimates can then be generated for 
various subgroups, where subgroups are defined by age, gender and injury.  MC asserts 
that these subgroups do not appear in their data in the same proportion as the subgroups 
appear in the population of crime victims. Thus, once an estimate has been generated of 
the average harms to each subgroup, the prevalence of that population can be re-weighted 
to be nationally representative. Once re-weighted, the representative proportions can be 
summed across subgroups to yield separate estimates for assault and sexual assault (see 
Figure 3 for a graphical representation of the approach).  
 67
 
INSERT FIGURE 3 HERE 
Figure 3. Conceptual Map of Miller and Cohen (1999)
 68
 
Unfortunately, this strategy appears to create more problems than it solves. The intuition 
for the approach is to demonstrate that the regressors explain jury award. But once that is 
established, using the same model to generate estimates to allow for prevalence 
weighting is problematic. First, of the nine independent variables used in the physical 
assault model to create expected sub-group awards, five are non-significant.  In the 
sexual assault model, all nine independent variables are not significant. The appropriate 
interpretation of those variables is therefore that those variables have a value of zero, 
rather than the MC approach which is to ignore the non-significance and multiply the X 
(set to 1) by the coefficient.  
Second, there are problems with the inclusion of claimed losses on the right-hand 
side of the model.  MC includes claimed losses presumably because it was an important 
predictor of variation in harms. But claimed losses co-vary with injuries and other 
attributes, which MC claim they do. Thus, re-weighting based on only injury and age and 
not claimed losses is questionable. In the case of the rape victim described above, MC 
use age and injury to re-weight the sample to be nationally representative.  Since claimed 
losses are included as an independent variable, the effect is to re-weight for the true 
prevalence of victim?s under 12 with internal injuries at the mean of claimed past and 
future losses. The intuition for including claimed losses in the model is that it is a 
mediator that clarifies the relationship between age, injury and damages.  In this case, 
clarifying that relationship will obscure the true effect of re-weighting.  Since only age 
and injury are observable in NCVS, there is no re-weighting that accounts for the co-
variation between age/injury and claimed losses.  If the variables are positively correlated 
(where more serious injuries result in larger claimed losses), then the effect of the re-
 69
 
weighting will correct only for the undercounting of the age and injury attributes, and not 
for the undercounting in claimed losses.  Thus, a more prudent strategy would have 
excluded claimed losses in the regression model.  
Third, MC uses the mean values of JVR data to re-weight their estimates within 
strata.  Thus, if women over 18 with major injuries are X percent of their sample, they 
multiply the expected damage by X. They then sum across each similarly weighted strata. 
However, this approach yields only an estimate of the mean value for each crime. No 
information can be retained about the distribution of harms using this strategy. This 
would be less of a problem if the data were normally distributed. However, since the 
mean is three to ten times the size of the median in the unadjusted data the choice of a 
strategy that only yields means skews toward higher results.   Given that the main 
criticism in the literature is that the cases that progress to civil court are more serious than 
those that do not, it is critical that some effort by used to address the distributional 
properties of the victim harms. 
Finally, while MC re-weights the data to account for the fact that their jury data may 
over- or under-represent some sub-groups, they do not account for the possibility that 
their jury data excludes some populations that are observable in the national population. 
Almost certainly, the small MC sample sizes (270 sexual assaults and 956 physical 
assaults) exclude some subgroups that exist in the population of crime victims.  Thus, if 
there are subgroups that are not included in the JVR data, then MC are assuming that the 
mean value of the awards that are excluded is identical to the mean value of the awards 
that are included.  Given the criticism of these data that jury cases comprise a non-
representative sample of all cases, this assumption is likely incorrect. Thus, a better 
 70
 
strategy would be to not use a regression model to re-weight the data to create nationally 
representative estimates.  
 
Are Juries Objective Arbiters of Victim Losses? 
Even if adjustments to civil jury awards can make those estimates nationally 
representative the question remains whether jurors are competent, objective arbiters of 
victim losses, who fairly weigh the evidence in each case?and only the evidence in the 
case?before making an award.  If, for instance, jurors are not capable of understanding 
issues in complex, or even typical, cases, than their verdicts are not an appropriate source 
of victim costs. In addition, if jury?s award compensation to victims that is unrelated to 
their physical or emotional injuries, then again, those damages are not a fair source of 
data to estimate the price of crime. In response to broader policy concerns that juries do a 
poor job in determining damages?and in particular that jury awards are escalating 
unfairly?a large body of research about jury behavior has emerged in the last two 
decades.   
The general consensus of this literature is that juries do almost as well as judges 
in evaluating complex claims and that jury awards are based on the attributes of the case 
they evaluate.  However there are some potential sources of error in jury awards that must 
be addressed to use jury verdicts to estimate crime prices.  If juries consider factors in 
rendering damages that are unrelated to the actual harms of a victim, than those awards 
will not be representative of the true harms to crime victims. As the review below of 
extant literature on jury behavior suggests, juries may alter an award in the presence of 
certain case attributes that are unrelated to victim harm. In particular, the jury behavior 
 71
 
literature identifies cases where a business is a defendant, where the jury does not have 
the opportunity to award punitive damages, when the victim is female, and when the 
defendant is clearly culpable and/or is unsympathetic as cases where awards may not 
reflect victim losses alone. In addition, prior research has shown that awards vary by 
region and have tended to increase over time.  Thus, the analysis predicting jury award 
from victim injury should also account for these extra-legal awards. In addition, in many 
cases the victim shares some liability with the defendant, and this shared culpability must 
be accounted for as well.  
Prior Research 
 As discussed in the review of extant literature on the costs of harms to victim in 
Chapter 2, the most common method for valuing harms to crime victims is to use civil 
jury awards to approximate true harms (Cohen, 1988; Miller, Cohen and Wiersema, 
1996; Cohen and Miller, 2003). As discussed in Chapter 2, jury valuations of real harms 
to victims have several attributes that makes this an appealing approach to valuing harms 
to crime victims. In particular, juries act as independent arbiters of the true harms 
suffered by a victim. In addition, as ex post observers of harm, juries have more complete 
information about crime losses than ex ante estimates of victim?s willingness to pay to 
avoid harm.  Finally, while ex ante estimates are preferred when estimating market 
prices, ex post estimates may be more reliable when the market is ill-defined, such as is 
the case for the demand for crime.  
Civil jury awards compensate victims in three ways. First, the jury may award 
damages for economic losses, including property loss, medical costs and lost wages. 
Second, juries may award damages for noneconomic losses to compensate victim for 
 72
 
indirect or intangible costs, including fear, lost or diminished quality of life, and pain and 
suffering and lost quality of life
7
.  Some prior research has suggested that non-economic 
costs are the largest component of the cost of most crimes (Miller, Cohen and Wiersema, 
1996: 15; Viscusi, 1988).  In addition, juries may also award punitive damages, which 
generally serve as specific or general deterrents to similar future action. In order to 
estimate harms to victims, only economic and noneconomic losses matter, as punitive 
awards do expressly relate to the actual harms suffered in the tortuous event.  
 In order for civil jury award data to provide reliable estimates of the true harms to 
victims, it must first be demonstrated that juries are capable of consistent and unbiased 
estimates of harms in all types of civil cases. That is, if jury awards vary by the type of 
claim, the attributes of the victim, or the attributes of defendant, then the use of these data 
to estimate crime harms is questionable. And, since intentional torts (criminal acts) are a 
relatively small proportion of all civil claims, it must be the case that juries make awards 
based only on the harms suffered and not the attributes of the event, whether it is an 
intentional tort, malpractice or negligence.  If the type of claim matters, then small 
sample sizes will greatly limit any analysis of harms from crime.  
The consistency of civil jury awards has been the subject of significant prior 
research. In particular, researchers have tested hypotheses that juries are not equipped to 
objectively evaluate civil claims, and that an increasing number of claims (and more 
specious claims) have contributed to an inefficient system becoming increasingly 
ineffective  (Danzon and Lillard, 1983).  The most pointed critiques allege that civil 
                                                 
7
 In the Miller and Cohen literature, economic damages are referred to as ?specials? and noneconomic 
damages are referred to as ?general damages?. In the RAND data, those terms are used to describe claimed 
damages, not actual award. To avoid confusion, this paper follows the conventions in the RAND data. 
 73
 
juries are incompetent and inherently unable to effectively determine liability. Critics 
assert that not only are juries unable to evaluate claims in complex cases, but that they are 
not competent to evaluate claims in relatively simple cases as well (Sugarman, 1985; 
Vidmar, 1989).   
The reliance of a jury of extra-legal factors in making an award is generally 
referred to as hypothesized ?jury incompetence? which may manifest in two ways. First, it 
may be that jury incompetence results in random awards. That is, because juries are 
unable to differentiate a true claim from a false claim (and great harm from small harm), 
jury awards may not be causally related to the facts of the case. Thus, jury awards could 
not be used to draw inferences about the association between harm and awards. Second, 
jury incompetence is hypothesized to result in systematic use of inappropriate criteria to 
make awards (Daniels, 1989: 280-1). These inappropriate criteria are extra-legal factors 
that may cause juries to make awards that are not compensation for actual harms, but 
rather awards made based on the attributes of the plaintiff and defendant that are not 
related to the actual claim. These may include the perceived wealth of the defendant 
(which is hypothesized to lead to awards in excess of actual losses), awards for female 
plaintiffs that do not fully compensate them for their losses, higher awards (relative to 
actual losses) in certain time periods or in certain regions of the country, and awards in 
excess of actual losses in cases where the defendant is particularly reprehensible.  As 
Vidmar notes, if researchers who use these awards ?ignore or underestimate the 
conceptual and methodological problems in these data sets? they will ?build on a 
questionable foundation? (1993:265).   
 74
 
The section that follows reports on studies that tests these hypotheses about jury 
behavior. These perceived deficiencies include the general competency of juries to 
evaluate civil claims, an evaluation of whether jury verdicts are random, and an 
assessment of the sources of extra-legal jury awards. If either of the first two critiques 
(competency and randomness) is affirmed, then jury awards cannot be used to estimate 
harms from crime. With respect to jury awards based on extra-legal criteria, if there is 
some evidence that juries use extra-legal criteria, then the data can still be used to 
estimate harms, if exogenous variables can be identified to control for those criteria.   
The Competency of the Civil Jury 
If jury?s are competent, objective arbiters of the facts of a case, then their awards 
will be causally related to the facts of the case (MC implicitly test for this in the 1999 
study discussed in Chapter 2). On the other hand, if jury?s are not competent then civil 
juries are capricious and the civil jury award system is a random ?bizarre lottery? of sorts 
(Daniels, 1989: 280).  If true, then the absence of a causal relationship between case facts 
and case disposition would invalidate jury award data as a tool for estimating the cost of 
crime to victims.  Despite the persistence of this assertion from members of the business 
community, insurance companies and national trade associations, (Daniels, 1989) and the 
media (Bailis and MacCoun, 1996), the overwhelming consensus in the scholarly 
literature is that civil juries are competent and allegations of award randomness are 
unfounded.     
Evaluating jury competency is not a straightforward enterprise.  The idea of 
competency is that jury?s make correct decisions, and that the ?correct? decision is 
observable. Thus, researchers assume that there is an objective level of competency and 
 75
 
that there exists an instrument by which that competency can be measured, weighed and 
gauged.  Multiple issues are involved in assessing jury competence and multiple 
standards of competency can be applied when studying these issues (Vidmar, 1989: 2).  
For example, competency could be measured by whether the jury gets the question of 
causality correct, or by the jury?s ability to assess negligence and scientific evidence and 
/or correctly assess damages.  Competency could be compared to an absolute standard or 
to the conclusions of experts, such decisions by judge s or some other tribunal, or an 
expert jury created to test the claim of competency. Absent a generally accepted legal 
framework for approaching these issues (Viscusi, 1988: 204), researchers have compared 
jury verdicts to the verdicts judges would have rendered (Broeder, 1959; Kalven, 1964; 
Kalven and Zeisel, 1966), and compared jury verdicts to  verdicts rendered by a panel of 
experts (Vidmar, 1992).  
The University of Chicago Jury Project (Broeder, 1959) analyzed jury verdicts 
from 1,500 criminal cases and 1,500 personal injury cases in the U.S.  After hearing a 
case, but before a verdict was rendered, judges were asked the verdict they would have 
rendered had there been no jury trial.  For criminal cases, judge-jury agreement was 81 
percent and judges were more likely to convict.  For personal injury cases, judge-jury 
agreement was 83 percent.  However, in terms of awarding damages, the study found that 
juries awarded two to thirty percent higher awards, without controlling for other factors.   
A subsequent summary of the Project?s findings (Kalven, 1964) updated 
Broeder?s (1959) preliminary results.  Judge and jury agreement was 80 percent in 
criminal cases.  For personal liability cases, agreement was 79 percent and jury awards 
average 20 percent higher than those of the judge.  Judges were also asked to rate each 
 76
 
case as ?difficult to understand? or ?easy? to test the hypothesis that judge-jury 
agreement increases with the ease of a case (1066).  Kalven (1964) found no association 
between case difficulty and case outcomes, and concluded judge-jury disagreement 
results from the application of different values in deciding the case, rather than 
competency.     
 More recent research has compared civil jury verdicts to verdicts rendered by 
?expert? juries.  Vidmar and Rice (1992) (summarized in Vidmar, 1992) present the same 
malpractice case to a cohort of twenty-one senior lawyers and judges and a cohort of 89 
jurors and compare the resulting damage awards. They found no significant differences in 
awards size, although the median expert award ($57,000) was greater than the median 
civilian jury award ($47,850) by about 20 percent (Vidmar, 1992: 123).  Although the 
jurors deliberated as individuals rather than as a panel, the study indicates jurors 
performed well compared to allegedly more qualified individuals.  
Jury Competency in Highly Complex Cases 
While the evidence appears to support the notion that juries are competent to 
assess damages in the average case, civil and criminal cases are becoming increasingly 
complex in the presence of advanced technologies, new sources of evidence emerge, and 
lawyers presenting increasingly sophisticated cases (Vidmar, 1989:4).  These 
developments have motivated concerns about the limits of the civil jury?s ability to 
evaluate statistical evidence (Thompson, 1989), and to evaluate the claims in highly 
technical cases, such as toxic torts (Drazan, 1989; Foster, Bernstein and Huber, 1993).  
Complex cases, which are generally thought to comprise a small minority of total civil 
cases, have created sufficient concerns in the court system that procedural innovations 
 77
 
have been implemented to assist jury?s in evaluating evidence (Horowitz and Bordens, 
1990).    
There is limited evidence about civil jury performance in complex civil cases. 
Most research on the topic of jury behavior in complex cases has studied complex 
criminal cases and mass torts, particularly toxic torts. Thompson (1989) examined the 
ability of the criminal jury to comprehend statistical evidence, particularly base rates and 
error rates, presented in criminal trials. In particular, Thompson tested whether juries 
over-estimated the value of statistical and forensic evidence.  He concludes that jurors 
generally do not overvalue statistical evidence.  However, when jurors fail to ?take into 
account the unreliability and partial redundancy of forensic evidence? overvaluation of 
statistical evidence does take place (41).  Drazan (1989) argues the complex scientific 
and medical evidence of toxic tort litigation is beyond the grasp of jurors and should 
instead be decided by special juries of experts.  Toxic tort cases are particularly 
challenging because ?the tortuous behavior and resulting injury are never 
contemporaneous? (294) as in the case of cancers that manifest years after exposure to a 
carcinogen. However, while juries may struggle with cases involving complicated 
scientific evidence, judges may fare no better (Drazan, 1989: 296).  Other scholars 
(Foster, Bernstein and Huber, 1993) argue for improved standards of scientific evidence 
presented in court and for improved guidelines for judges to enhance civil jury outcomes.  
Are Jury Award?s for Damages Commensurate with the Facts of a Case? 
As noted, some researchers have hypothesized that civil jury awards may not be 
associated with the real economic and non-economic loss in cases they adjudicate.  
However, a large body of research (e.g. Bovbjerg, Sloan and Blumstein, 1989; Peterson, 
 78
 
1984; Viscusi, 1988; Wissler et al., 1997; Sloan and Hsieh, 1990; Cohen and Miller, 
2003) documents the association between awards and economic and noneconomic loss.  
A landmark study by the RAND Corporation (Peterson, 1984) analyzed civil jury 
verdicts in Cook County (Chicago), Illinois using multiple regression analysis.
8
  Petersen 
found that variation in awards was predicted by the plaintiff?s medical expenses and lost 
income, severity of injuries, and disability. Petersen found that the number and type of 
injuries alone explained nearly 40 percent of the variation in award size.  An empirical 
study of 859 product liability cases (Rodgers, 1993) supports these results, concluding 
?pain and suffering awards are systematically related to economic losses and to the type 
and severity of injury? (252).   
Viscusi (1988) analyzed pain and suffering awards in a sample of over 10,000 
product liability cases and concluded that ?pain and suffering compensation varies by 
injury class, with the nature of the effects being broadly consistent with general 
perceptions regarding injury severity? (217).  Wissler et al. (1997) used mock jurors in 
two controlled experiments and find ?half to three-fourths of the variance in log awards 
for pain and suffering was accounted for by perceptions of the amount and duration of 
mental suffering, disability, pain and disfigurement associated with the injuries? (202-3).   
Similar to the concerns about juror?s ability to accurately assess guilt and liability 
in complex cases, some researchers have hypothesized that jury?s are not able to 
accurately assess the victim?s true harms in complex cases (Ostrom, Rottman and Goerdt, 
1996).  Again, most extant research finds that civil jury awards are explained primarily 
by the plaintiff?s economic and non-economic loss, despite some variation.  Rodgers 
                                                 
8
 The data set used by Petersen is an earlier iteration of the data used in this analysis. 
 79
 
(1993) finds that most heterogeneous component of awards?pain and suffering?are 
?nonetheless a function of variables we can specify? (Rodgers, 1993: 261).  Some of the 
unexplained variation may be due to differing values plaintiffs place on their own lives as 
evidenced by riskier behavior and partial responsibility in the plaintiffs own victimization 
(Cohen and Miller, 2003, 174).  Ultimately, ?since society has chosen the civil court 
system as a means of redressing victims, jury awards are a logical way to approximate 
society?s assessment of the pain and suffering incurred by victims? (Cohen, 1988:541).   
Extra-Legal Factors in Jury Awards 
The preponderance of prior research suggests that civil juries are competent to understand 
the facts of civil cases and civil jury awards are causally related to the facts of a case.  
However, there is also a substantial literature that finds use of extra-legal factors by civil 
juries to evaluate civil claims.  Thus, awards are biased when compared to true damages.  
Five key extra-legal factors are indicated by prior research: 1) case type, 2) geographical 
and temporal factors, 3) defendant wealth effects, 4) plaintiff gender, and 5) defendant 
culpability and availability of punitive awards.  
Extra-Legal Considerations by Case Type 
In theory, the value of a specific injury should not vary by the type of civil case.  That is, 
if a plaintiff loses the use of their hand, the value of that loss should be the same 
regardless of how that loss occurred. The damage award should be identical regardless of 
whether the case was an automobile accident, product liability, malpractice or a tort.  
Unfortunately, while there is some evidence that juror awards vary based on the type of 
case, it is very difficult to causally show bias in jury behavior. Because juries make 
decisions in secret, and because no independent, objective counterfactual can be 
 80
 
observed, extant research in this area is marked by serious identification problems 
(MacCoun, 1993). While MacCoun (1993) notes that mock juror experiments, where 
independent variables are systematically varied across research subjects, control for the 
effect of extra-legal factors. By contrast, the research on the association between case 
type and damages mainly uses archival data, with limited covariates.  So, while several 
studies (Goodman, Greene and Loftus, 1989; Daniels and Martin, 1986; Peterson and 
Priest, 1982) find variation in award amounts across different case types, the studies fail 
to account for alternative explanations, namely injury severity.  Nevertheless, extant 
research does offer some guidance on the importance of case type, as described below. 
Goodman, Green and Loftus (1989: 295) find that the highest mean and median 
awards are for liability cases, followed by automobile negligence cases and medical 
malpractice cases, respectively.  Daniels and Martin (1986) find product liability cases 
and medical malpractice cases have higher awards than vehicular accident cases, street 
hazard cases and premises liability cases.  A study of Cook County jury verdicts 
(Peterson and Priest, 1982), pre-dating Peterson (1984), found substantial variation in 
award amounts across different types of lawsuits but did not control for injury type or 
economic damages.  Not surprisingly, the types of lawsuits that brought the largest 
awards involved more seriously injured plaintiffs (Peterson, 1984: 32).   
Peterson?s (1984) multiple regression analysis of Cook County civil jury awards 
empirically controls for injury severity and case type to test whether case type or injury 
severity most explains higher awards.  Most differences in awards resulted from injury 
severity rather than case type?two-thirds of the differences in awards for work injury 
and automobile accident claims are explained by injury severity.  Still, plaintiffs in work 
 81
 
injury, malpractice and product liability cases receive awards that are two to four times 
greater than for similarly injured plaintiffs in other types of cases?street hazard, injury 
on property, dramshop, intentional tort, common carrier and automobile accident cases 
(35-7).  Thus, there appears to be a premium for work-related injury, malpractice and 
product liability plaintiffs compared to injuries in other types of cases. 
While the results are relatively consistent across these extant studies, it is difficult 
to judge how robust the findings are. Few studies examining award variation by case type 
have empirically controlled for confounding variables, such as injury severity and 
plaintiff income.  The extant research suggests awards with similar fact patterns vary by 
case type, but the impact of extra-legal factors is not known because confounding 
explanations are not modeled.  Peterson (1984) is the prominent exception, but even there 
the study controls are limited to case type, injury severity and large lost income.  Despite 
these limitations, case type appears to be an important predictor of damages because 
plaintiff success rates vary by case type (Daniels and Martin, 1986), and compositions of 
case types vary across geographical jurisdictions (Peterson, 1987: 39-41).   
Geographical and Temporal Factors 
Many studies hypothesize that similar jury awards may vary over time and space. 
Research suggests geographical heterogeneity in awards, and, temporal heterogeneity 
associated with changes in wealth and legal standards. Unfortunately, most archival 
studies of civil jury awards are confined to only one or two jurisdictions (Hans and 
Lofquist, 1992; Peterson, 1984; Chin and Peterson, 1985; Hammit, Carroll and Relles, 
1985).  Jurisdictional differences in ?legal cultures? raise problems of generalizability 
and hinder cross-county comparisons (Vidmar, 1993: 229).  Moreover, state legislative 
 82
 
reforms to the civil tort system introduced in the 1970s varied in number, stringency, and 
timing (Danzon, 1984: 140).  Thus, an archival study of civil jury awards that accounts 
for temporal and spatial attributes of cases would be more informative than one that did 
not. 
Danzon and Lillard (1983) conduct an empirical analysis of medical malpractice 
claims, controlling for the possibility that California is particularly pro-plaintiff relative 
to other states.  They find no evidence that awards in California, where one-third of the 
claims in their sample originate, are different from the frequency-weighted mean for 
other states (361).  Peterson?s (1987) analysis of civil jury verdicts in Cook County 
(Illinois) and San Francisco (California) indicates the two jurisdictions shared nearly 
identical trends in the per capita number of trials throughout the 1960s and 1970s.  
However, the trends diverged in the 1980s due to changes in settlement practices (i.e. an 
increasing tendency to settle) or in changes in legal procedures that reduced the number 
of jury trials in San Francisco and increased the number of trials in Cook County (8-9).  
These changes caused the average award to fall in Cook County and to climb in San 
Francisco (Saks, 1992: 1249).  Daniels and Martin?s (1986) survey of jury verdicts and 
awards in 43 counties in ten states finds considerable variation in plaintiff success rates 
and the size of awards, perhaps attributable to differences in state law (Daniels and 
Martin, 1986: 329) or local legal culture (Daniels and Martin, 1986: 332-3; Saks, 1992: 
1252).  Tabarrok and Helland (1999) find that in states with an elected judge, awards are 
larger for out of state defendants and larger in general than in states that do not elect 
judges.  
 83
 
The finding that awards vary across states and over time has two important 
implications. First, this variation may reduce the generalizability of a jurisdiction-specific 
study to other jurisdictions or to other time periods.  Second, these findings suggest 
caution should be taken interpreting results from multi-state data analyses that do not 
control for jurisdiction-level variation (a common problem).  Legal and procedural 
variations might mean, ceteris paribus, a leg is worth twice as much in Florida as it is in 
Michigan.  Notably, Cohen and Miller (2003) include legal and institutional control 
variables (to control, for example, damage award caps in some states) in their most recent 
estimates of the implied value of life from jury awards (175). 
 Defendant Wealth Effects and the ?Deep Pockets? Hypothesis  
MacCoun (1996) summarizes one of the most widely held beliefs about civil litigation, 
noting ?there is a widespread perception that America's tort system is biased against so-
called deep-pocket defendants?defendants with extensive financial resources like 
corporations, governments, and wealthy individuals? (123).  This view suggests that 
when juries perceive that a defendant has the ability to pay a larger damage award, ?juries 
are more likely to find liability, and award more money? (ibid.).  Such a bias would be a 
departure from legal standards since the law dictates that compensatory damage awards 
?be independent of the defendant?s wealth, moral culpability, and other attributes? 
(Hammit, Carroll and Relles, 1985: 754).  Much research has addressed the deep-pockets 
hypothesis.  
A report by the RAND Corporation (Peterson, 1984), discussed above, finds 
evidence that plaintiffs in work injury, malpractice and product liability cases receive 
higher awards than plaintiffs with similar injuries and economic loss in other types of 
 84
 
cases.  The authors posit this may be because ?juries may tend to sympathize more with 
certain plaintiffs more than defendants? (37).  A follow-up report (Chin and Peterson, 
1985), the first serious empirical inquiry into defendant wealth effects, analyzes the same 
dataset of over 9,000 civil jury trials in Cook County (Chicago), Illinois between 1959 
and 1979.  Building on two previous studies examining civil jury trials in Cook County, 
the authors find verdicts are ?generally less favorable? for deep-pocket defendants, even 
after accounting for injuries and case types (58).  While the differences between 
individual and corporate defendants and the differences between individual and 
government defendants were ?not as large as one might have expected?, the analyses 
reveal much greater differences for trials involving severely injured plaintiffs (60).  
Specifically, ?corporate defendants paid awards to severely injured plaintiffs that were 
over four times as much as awards against individuals and three times as much as awards 
against government agencies? (60).  Unfortunately, the analyses exclude information 
about liability issues (i.e. perceived defendant culpability) that could contribute to award 
divergences.   
Hammit, Carroll and Relles (1985) analyze the same dataset of civil jury verdicts 
used by Chin and Peterson (1985), and add a dataset of civil jury verdicts from San 
Francisco.  The results of the multivariate regression analysis lead the authors to 
conclude, ?the type of defendant appears to influence jury awards.  Defendants who can 
be presumed to be wealthy, heavily insured, or able to distribute the costs of awards 
among their customers or shareholders are forced to pay larger awards? (754).  Corporate 
defendants pay 34 percent larger awards than individuals, after controlling for plaintiffs? 
injuries and type of legal case.  Government defendants also pay substantially more than 
 85
 
individuals, especially when plaintiffs? injuries are severe.   Schmit, Pritchett and Fields 
(1988), in their regression analysis of a sample of cases in which punitive damages were 
assessed against corporations, find punitive damages reflect the total assets of the 
defendant, but total assets are a poor predictor of the amount awarded (464).   
As noted above, the datasets commonly used in these archival studies had 
substantial limitations, not the least of which was that civil cases were not randomly 
sampled for inclusion in the dataset?rather, the database tended to be populated with 
novel cases.   Alternatively, quantitative studies analyzing different datasets (Daniels and 
Martin, 1986; Sloan and Hsieh, 1990) and qualitative studies employing mock juror or 
post hoc interview methodologies (Hans and Ermann, 1989; MacCoun, 1996; Vidmar, 
1993; Hans and Lofquist, 1992) find evidence contradicting the deep-pockets hypothesis.  
Daniels and Martin (1986), collected data from local jury verdict reporters, survey 
state court jury verdicts and awards in 43 counties in ten states.  The study only reports 
summary statistics that compare award amounts by case type. Nevertheless, Daniels and 
martin dispute the deep-pockets hypothesis, concluding, ?awards for some kinds of cases, 
such as product liability and medical malpractice, may be high in comparison to those 
involving other causes of action, but these types of cases comprise a small proportion of 
all verdicts and plaintiffs are less likely to win in these lawsuits? (347-8).  Sloan and 
Hsieh (1990) analyze a dataset comprised of closed medical malpractice claims in Florida 
and samples of jury cases from jury verdict reporters in California, Illinois, Florida, 
Missouri and Kansas (using RAND data on the malpractice cases for California and 
Chicago Peterson, 1984; Chin and Peterson, 1985).  Sloan and Hsieh?s multiple 
regression analyses also contradict the deep-pockets hypothesis and the findings of Chin 
 86
 
and Peterson (1985).  Even though hospitals, the most common deep-pocket defendant, 
have greater financial assets, the plaintiff received a lower award when a hospital was the 
defendant (1027).   
The other common method for evaluating the ?deep pockets? hypothesis is to use 
a mock jury, where civilians and/or experts are asked to evaluate claims in a simulated 
case.  Hans and Ermann (1989) apply a juror simulation methodology, soliciting 
responses from 202 university students for two hypothetical cases.  In the first case, the 
defendant was an individual and, in the second, a corporation.  When the corporation was 
a defendant, the relationship between financial resources and judgments of wrongdoing 
was negative, contradicting the deep-pockets hypothesis (160-1).  When the defendant 
was an individual, perceived financial resources explained only four percent of award 
variation (160). The authors suggest that respondents varied award and liability 
assessments based primarily on perceived ?recklessness within the specific context of 
individual or corporate misbehavior? (161).  
Also using the mock jury method, MacCoun (1996) experimentally controls for 
confounding variables, namely defendant wealth.  He finds jurors? verdicts were 
?insensitive to reliable differences in perceived defendant wealth?, although 
?corporations were indeed treated differently? (140).  That is, MacCoun finds evidence 
that it is the ?corporate identity? of the victim that matters, not their wealth.  Vidmar 
(1993) uses a sample of 147 citizens waiting to be called for jury selection in the Raleigh, 
North Carolina state court.  The experiment, ?yielded no support for the deep pockets 
hypothesis or the psychological dynamics that are posited to be behind it? (225). 
Alternatively, Hans and Lofquist (1992) use interview methods to investigate post hoc 
 87
 
the decision-making process of tort jurors in business cases.  They find that, contradictory 
to the deep-pockets hypothesis, most jurors held the position that a corporation?s assets 
?should not be and were not relevant? to award decisions (106).  Moreover, ?at the level 
of the case, jurors rarely demonstrated the scrutiny or expressed the negativity toward 
corporations that they showed toward individual plaintiffs? (110).   
While early studies analyzing civil jury verdicts find some evidence of the deep-
pockets hypothesis, ?we cannot say, one way or the other, whether it is wrong on the 
basis of available data? (Vidmar, 1993: 240).  However, most research indicates juries 
treat corporations differently, though not necessarily because they have deeper pockets. 
Hans notes that ?juries may also be respond to other differences between corporations 
and individuals besides their financial resources? (1989: 195).  MacCoun (1996: 140-1) 
posits juries may treat corporations less well because of: 1) a general distrust of 
commercial actors, 2) the impersonal nature of corporations and 3) the expectation of 
higher standards for corporations.  Nonetheless, recent work analyzing civil jury verdicts 
(Cohen and Miller, 2003) controls for deep-pocket effects.  Thus, the literature suggests 
that identification on corporate identity is more effective at reducing bias than controlling 
for defendant wealth. 
Plaintiff Gender  
Several studies have hypothesized a link between plaintiff gender and civil jury awards. 
In his analysis of compensatory awards using Jury Verdict Research data, Rodgers (1993) 
controls for injury severity and finds that gender is not a significant predictor of award.  
In their analysis of Jury Verdict Research data for Cleveland, Ohio, Nagel and Weitzman 
(1972) find plaintiff gender does not significantly affect the determination of liability.  
 88
 
However, mostly male jury?s award more to male plaintiffs than to female plaintiffs, and 
mostly female juries favor women, though to a lesser extent than male dominated juries 
favor men.  The authors posit greater severity of injury to males in the sample and the 
differential earning power of men and women may explain these differences (109).   
Goodman, Greene and Loftus (1989: 290) correctly note that Nagel and 
Weitzman (1972) fail to sufficiently account for strength of evidence or type of injury.  
Applying a mock juror methodology to wrongful death cases, Goodman, Green and 
Loftus (1989) experimentally control for liability and test whether the gender of the 
decedent affects award level.  They find statistically significant increases in awards for 
male plaintiffs in product liability cases and automobile negligence cases, but not in 
medical malpractice cases (295-6).  Mock jurors were also dramatically less likely to 
consider exponential factors that would escalate awards, such as expected salary 
increases, when the decedent was female (300).  A later study of wrongful death cases 
using a similar mock jury methodology (Goodman, Loftus, Miller and Greene, 1991) 
produced similar results.  Fewer jurors said they considered the financial loss to the 
surviving spouse (57 percent vs. 75 percent) when the surviving spouse was male than 
when she was female; twice as many jurors considered exponential factors when the 
decedent was male (281).  The authors posit that much of the gender effect may result 
from the emphasis on lost wages in determining awards.  Since the value of a female 
homemaker?s productive activities are not assigned a market value, female plaintiffs are 
most likely to be disadvantaged (282).   
 89
 
Defendant Culpability/Reprehensibility 
Awards are intended to compensate the plaintiff for his or her loss independent of the 
defendant?s moral culpability (Greene, 1989: 232).  However, limited research suggests 
civil juries may take into account defendant culpability or reprehensibility when 
awarding compensatory damages (Kalven, 1958; Broeder, 1959; Hans and Ermann, 
1989; Horowitz and Bordens, 1990; Wissler, Rector and Saks, 2001).  Such extralegal 
considerations would increase awards for defendants perceived as particularly 
reprehensible, all else being equal.   
Kalven?s (1958) descriptive study of the civil jury posits that, other factors held 
constant, juries will vary awards on the basis of varying degrees of defendant liability.  
Broeder (1959), discussed above, experimentally tests this notion using a mock jury 
model with two treatments?doubtful defendant liability and very clear defendant 
liability.  The average award of all verdicts with clear liability was $41,000, compared to 
$34,000 where liability was ambiguous (754).  MacCoun (1996) finds similar results?
mock jurors assess higher compensatory awards when defendant liability is clear.  Hans 
and Ermann (1989), also discussed above, provide an alternative explanation for the 
?deep pockets? hypothesis.  The authors hypothesize that, if juries hold corporations to 
higher standards of responsibility, corporations may be perceived more negatively than 
individuals committing the same actions (154).  Applying a mock juror methodology, the 
authors find mock jurors deem corporations more reckless, morally wrong and deserving 
of punishment as compared to an individual, despite identical actions (158).  They posit 
perceptions of greater culpability motivate mock jurors to assess higher total awards 
(161).   
 90
 
Wissler, Rector and Saks (2001) address a similar question of liability spillover 
into damages decisions.  They find jurors assess higher awards when defendant liability 
was clear. Special instructions not to inflate awards to punish careless defendants reduced 
the effects of the defendants? conduct on awards (136).  Another study using a mock jury 
methodology by Anderson and MacCoun (1999) investigates the ability of jurors to 
effectively compartmentalize liability verdicts from compensatory damage judgments.  
Responses from 91 participants indicated jurors inflate compensatory awards when they 
do not have the option to award punitive damages.  Specifically, jurors inflate the most 
flexible and variable component of awards?the pain and suffering component.  
Horowitz and Borden?s (1990) tangentially related study of variations on trial 
structures (unitary, bifurcated or trifurcated) and order of decisions (liability or causation 
first) using 768 mock jurors finds similar results.  The average compensatory award was 
lower when liability was presented first than if general causation was presented first 
(278).  The authors conjecture that in trials where juries first assessed causation, jurors 
may have developed a pro-plaintiff bias, leading them to assess higher awards against the 
defendant (283).    
  On the other hand, Cather, Greene and Durham (1996) studied 80 jurors who had 
just completed jury service and find no evidence to support the hypothesis that the 
defendant?s reprehensibility affected the damage award.  Employing a mock jury method 
to determine the effect of defendant reprehensibility on compensatory awards, the authors 
assigned participants to low reprehensibility and high reprehensibility conditions 
(reflected in the trial summaries).  They find the defendant?s conduct did not affect the 
awards assessed by jurors.   
 91
 
Race and Socio-Economic Status 
In the criminal law literature, there is substantial evidence that the defendant?s race, and 
socio-economic indicators affect jury decision-making (see Sommers and Ellsworth, 
2000 for a thorough review).  In particular, it has been shown that cases with white 
victims and black defendants are more likely to result in death sentences in capital cases 
(Paternoster and Brame, 2008). The civil jury literature is more ambivalent about the 
affect of race and socio-economic status on outcomes. Hastie, Schkade and Payne (1998 
find that jurors race and education only weakly associate with case outcomes. There 
appears to be little literature on the effect of the defendant?s or plaintiff?s race and 
ethnicity on civil jury awards, although Bornstein and Rajki (1994: 129) note that 
?although little research has been done on SES and civil verdicts, there appears to be little 
systematic relationship.? 
 It is not surprising that there has been little research on this topic, given that many 
defendants in civil cases, particularly in civil cases that result from a criminal act, are not 
the same individual who committed the tortuous act. Thus, much of the effect of race on 
outcomes, if there is any, is mediated by the presence of a business as defendant. The 
effect of socio-economic status is much more difficult to assess. On one hand, there is 
little scholarly evidence to suggest that there is a relationship between the SES of the jury 
and awards, or the defendant or plaintiff race and awards. On the other hand, this may be 
due in part because defendants with relatively low SES status are unlikely to appear as 
defendants in civil cases. The potential implication of this issue is addressed in the 
limitations section in Chapter 4. 
 92
 
Counting Property Losses 
The extant literature is ambiguous on the issue of whether property losses should be 
counted in the estimation of the price of crime. The foundational work in the field draws 
largely from the University of Chicago Program on Law and Economics who advocate 
not counting property losses in price of crime calculations (Becker, 1968; Polinsky and 
Shavell, 1979; Shavell, 1987). As Rajkumar and French note, ?In the case of stolen 
property, unless it is damaged or destroyed, it is typically not counted as a social loss 
because it is transferred to another member of society, namely, the criminal (Becker, 
1968; in Rajkumar and French, 1997: 294).  The choice of whether to include property 
losses has been framed by Cohen (2000) as a choice between adopting a social cost 
approach or an external cost approach. Social costs, described in detail in Chapter 2, are 
the sum of society?s welfare. Thus, since crime is merely an (involuntary) transfer of 
ownership, property that is transferred to an offender but not damaged or destroyed 
should not be counted as a component of the price of crime.  Cohen describes external 
costs, by contrast, as costs involuntarily imposed by one member of society on another 
(271-273).  
While the Law and Economics tradition advocates not counting property losses, 
the tradition in the price of victimization literature is to include these costs.  The issue is 
one of standing, that is, determining whose preferences should be counted, particularly in 
cost-benefit analysis (Whittington and MacRae, 1986). Trumbull (1990: 202) asks, ?How 
should the reduction in theft be treated - as a social benefit or a mere transfer??  Becker 
(1968:170) describes crime as an economically important activity and advocates counting 
criminal gains from crime as well as lost criminal opportunity from law enforcement. 
 93
 
Stigler (1970) disagrees, arguing the society has explicitly labeled criminal activity as 
illicit and thus assigns crime no positive social value.  Others argue that the decision 
about whether to include criminal gains as part of the cost-benefit equation should be left 
to the analyst to determine whether society gains from a criminal transaction 
(Whittington and MacRae, 1986; Shavell, 1985). Shavell (1985: 1234; in Trumbull, 
1990) states that, ?[a]llowing for a divergence between social and private benefits gives 
the analyst greater freedom to describe society's values.? 
Trumbull (1990: 211) disagrees, arguing that, ?allowing the analyst the freedom 
to describe society's values is not consistent with the notion that the evaluation be based 
solely on economic criteria given the physical and social constraints that exist.? Trumbull 
distinguishes between tolerant institutions (like markets) and absolute institutions (like 
criminal laws).  An absolute institution "fixes the level of an activity which the individual 
may not exceed, or fall below as the case may be. . ." [Roberts, 1973: 392]? in (Trumbull, 
1990: 211). Trumbull (212) criticizes those who fail to understand this distinction, 
stating, ?[m]issing from these models is the realization that society has a purpose when it 
labels certain acts criminal; the label communicates that these acts will not be tolerated or 
counted in the social weal.? 
The approach in this paper is to include property losses as a component of the 
price of harms. As been discussed in Chapter 2, crime is an involuntary transaction. Due 
to its involuntary nature, criminal activity violates a fundamental attribute of a 
competitive market. Thus, it seems reasonable to consider the question of standing from a 
broader perspective (rather than a market-based perspective which would clearly require 
that these losses are excluded).  Broader social institutions, including criminal law, 
 94
 
advocate that participation in criminal activity directly leads to a general loss of standing. 
It would therefore be incongruous to give criminals standing in estimating the magnitude 
of harms associated with their criminal activity when that activity otherwise leads to a 
complete loss in standing in every other aspect of their social status. 
Risk of Death 
Prior research on the cost of crime to victims has taken two different approaches 
to dealing with cases that result in the death of the victim. In the earliest literature, the 
cost of a homicide was valued according to extant estimates of the value of a life. In 
subsequent studies, homicides costs were not directly estimated. Rather, the risk of death 
was associated with the underlying offense that led to a homicide (assault, robbery, rape, 
etc.).  Generally, this was necessitated by the use of aggregated data as researchers could 
not directly observe whether a particular robbery was part of a homicide.  
In this study, homicide is observable in the data, although it is a rare event. Thus, 
it is fair to ask whether a risk of death calculation should be included in the analysis. 
Traditionally, researchers count the probability that a crime will become a homicide as an 
additional component of the price of harms to victims. Hypothetically, if a burglary has a 
1 in 1,000 chance of becoming a homicide (that is, a homicide occurs in every 1,000 
burglaries) and the value of a statistical life is $7,000,000 than the product of that 
probability (0.1 percent) and that value means that there is an additional $7,000 in costs 
associated with a burglary, in addition to direct and indirect losses.   
The approach was originally used to overcome data limitations, where researchers 
were unable to directly observe homicides in jury data (Phillips and Votey, 1981; Cohen, 
1988; 2005).  More recent work has also incorporated a risk of death component into 
 95
 
price estimates (Miller, Cohen and Wiersma, 1995) Cohen and Miller, 1999; Rajkumar 
and French, 1997). It is fair, however, to question whether this tradition has some 
intrinsic value in cases where data are available (as well as in cases where data are too 
limited to directly observe homicide). 
There are two main objections to using risk of death measures. First, including 
risk of death appears to be double-counting in many instances. In any study that relies on 
ex post measures of changes in criminal offending, the number of homicides (and other 
criminal events) is known. Thus, if a policy or program reduces burglary and homicide, 
counting a reduction in risk of death as a social benefit for the burglary cases is double-
counting. Even in cases where there is an ex ante estimate of crime reduction including 
risk of death is double-counting. Consider the finding from Levitt (1996) that each year 
of incarceration prevents 15 felonies.  Levitt calculates the benefit from those prevented 
crimes by assuming a distribution of offending and assigning a value to each offense. 
Again, the number of each type of crime is known (albeit via assumption). Counting the 
value of reductions in homicide and the reductions of risk of death in burglaries that did 
not become homicides is double-counting. 
Second, it is fair to ask why death is special. Every criminal event carries with it a 
risk that it will escalate into a more serious criminal event, or, expand to include other 
less serious criminal events.  It is obvious that felony person and property crimes carry a 
risk that they will become a homicide, but it should also be obvious that other less serious 
crimes do as well. A weapons offense, for example, clearly has a risk of escalating into a 
homicide.  Similarly, driving under the influence could become a homicide. But it also 
may be the case that drunk drivers are more likely to illegally take a weapon in a vehicle 
 96
 
than sober drivers, and thus each drunken driving incident has a risk of becoming a 
weapons event.  Similarly, each burglary carries with it the risk that the burglar will 
vandalize the property, and thus a risk of vandalism price component should be added to 
all burglaries.  Obviously, this approach adds enormous computational costs to any cost-
benefit analysis that includes the price of harms to victims.
9
But the entire approach appears to be unnecessary. If it is known whether a 
burglary also had less serious crimes associated with it, and that it did not lead to more 
serious crimes, than including the risk of other events is double-counting.  Even in cases 
where the prices are applied to the study of future events, the distribution of offending is 
assumed from some known distribution of prior offending, as is the case in the Levitt 
(1996) example. Further, this issue identifies a practical advantage of this approach over 
contingent valuation.  Since each incident carries with it a probability of escalation or 
expansion, it must be assumed that respondents to contingent valuation surveys are aware 
of those probabilities and include them in their calculus. Thus, when Cohen et al (2004) 
query respondents about their willingness to pay for a reduction in burglaries, it must be 
assumed that they include in their calculation the risks of both homicide and vandalism.  
                                                 
9
 A third very weak criticism can be leveled against the risk of death calculation. Risk of death is at its core 
an ex ante measure. The intuition is that when a burglary is about to transpire there is some risk that 
someone may be in the residence and the crime will escalate to homicide.  Thus, a priori, it cannot be 
known whether the criminal event that is about to take place will be a burglary or a homicide. Therefore, it 
is appropriate to include that risk in the calculation. However, this ex ante approach is inconsistent when 
incorporated into jury studies (where measures are not ex ante) or cost-of-illness studies (where measures 
are explicitly ex post).  While some may view this as strengthening those methods, it is nevertheless an 
inconsistency that affects the interpretability of the study, and perhaps the credibility: if ex ante measures 
are the best way to measure this component of price, especially in cost of illness studies, should they not be 
used to measure other components? 
 
 97
 
Since homicides can be directly observed in the NIBRS data, estimates for 
homicide are created as a separate crime category
10
. As a result, the cost estimates here 
are not directly comparable to extant estimates. For instance, while past estimates of 
robbery include the chance that a robbery may become a homicide, here, robberies that 
become homicides are valued as homicides. The interpretation of the estimate of on 
robbery in this study is the harm to the victim of a robbery that did not escalate to a more 
serious crime. 
 
Summary of Prior Research 
The available evidence suggests that civil jury outcomes are not random lotteries. 
Although they are subject to substantial variation, awards ?are nonetheless a function of 
variables we can specify? (Rodgers, 1993: 261).  The overwhelming consensus in the 
literature contends awards vary in a manner consistent with expectations of economic and 
non-economic loss (Viscusi, 1988).  However, there are several potential extra-legal 
factors that may lead a jury to make an award based on factors that are not directly 
related to actual plaintiff harms. Studies of award variation across case type, though 
econometrically limited, suggest work injury, malpractice and product liability awards 
are higher than awards in other types of cases.  There is also some evidence that 
geographical variations in legal culture and legal procedure account for differences in 
awards that are not directly related to victim harm.  Defendant wealth does not appear to 
be associated with higher awards, although the presence of a corporation as the defendant 
                                                 
10
  MC report that in their data homicides occurring in the commission of a robbery were reported to the 
FBI as a robbery. In NIBRS data, the top three charges associated with a single event are reported.  As 
discussed later, the NIBRS data were ordered with homicide as the most serious crime, and thus this was 
not an issue in this analysis. 
 98
 
may.  Male defendants appear to receive higher awards than women.  And finally, the 
evidence indicates the jury?s perception of defendant culpability or reprehensibility may 
inflate compensatory awards, particularly when the jury does not have the option to 
assess punitive awards.   
 
 99
 
Chapter Three: Damages Awarded by Jury in Civil Cases 
 
The goal of this analysis is to estimate the average harms to crime victims by crime type. 
A model with full information would directly predict harms from crime, by type of crime, 
Y= ?+X
1
?+ X
2
?+? (3) where Y is the estimated total harms from crime, X
1 
is a vector of 
victim,  offender and case attributes, and X
2
 is a vector of crime types. The coefficient on 
X
2 
is the mean marginal harm by crime type and total harm for each crime type is Y|X. 
Since harms vary by case attributes, the analysis requires incident-level crime data and 
incident-level data on the value of the losses to the victim.   
As discussed in Chapter 2, in past studies of the cost of crimes to victims, 
incident-level data were not available that described both criminal incidents and 
associated harms to victims. Beginning in 1998, a national data source for incident-level 
crime data?the National Incident-Based Reporting System (NIBRS)?became available. 
NIBRS remains the only incident-level crime data currently available that includes data 
from multiple states (data on a representative sample of crime victims is available from 
NCVS and the relative advantages of NIBRS over NCVS is discussed later in this 
chapter).  However, the NIBRS data does not record all data necessary to populate model 
(1).  While NIBRS does report case attributes (including victim attributes and injuries) 
and property losses, NIBRS records data on only one component of losses from crime 
(property loss). The other components of harms from crime--direct economic losses from 
crime (such as medical bills and lost wages) and indirect economic losses (including fear 
and pain and suffering)--are not collected.  Thus, Y cannot be modeled in (3) using only 
data from NIBRS. 
 100
 
To overcome this limitation, several prior research studies have modeled the costs 
of crime to victims using case-level civil jury award data to associate the harms from 
offending to specific types of victimization. The intuition is straightforward. The 
identifying assumption is that jury awards yield an unbiased estimate of harms from 
criminal victimization. Juries are assumed to be independent arbiters of liability.  Thus, 
the total jury award is a reasonable proxy for the total harm resulting from a criminal 
event. While the harms are not valued ex ante, they approximate the true value of losses. 
A substantial literature has emerged (and is described below) that assesses this 
assumption. The general conclusion from this research is that juries render appropriate 
judgments based on case facts, albeit with some bias in the size of awards?particularly 
for non-economic losses?in the presence of certain case attributes.  
Therefore, jury award data could be used to estimate harms to victims from crime, 
conditional on case attributes and crime type.  It should be noted that there are two 
limitations to using these data to estimate harms to victims.  First, it may be that the 
crimes that result in a civil award are not representative of all crimes.  If civil cases are, 
on average, more serious than the average criminal case, than the estimates from these 
data will be upwardly biased.  Second, it is difficult to clearly identify which civil cases 
result from a criminal event in the data. Two types of cases?physical assault and sexual 
assault?are relatively easy to pick out, and thus have been the focus of prior work in the 
field.  However, only a small number of these cases result in a civil jury award which 
creates analytic problems (as described in Chapter 2). Therefore, adjustments have to be 
made to account for both the potential non-representativeness of jury data and the limited 
 101
 
number of clearly identifiable criminal cases in order to create estimates for a more 
comprehensive list of all criminal cases.  
Case-level jury award data are publicly available from only one source, the 
RAND Institute of Civil Justice. RAND collects data on jury awards using a stratified 
random sample of verdicts from a non-representative sample of U.S. counties between 
1985 and 1999.  As in past studies, it is difficult to easily distinguish those claims which 
result from a criminal act from those claims that do not. In a database of more than 
40,000 records there are less than 1,500 cases that could reasonably be coded as being the 
result of a crime-related incident. As with prior studies, the observable criminal cases are 
limited to intentional torts, rape and a few property crimes.  However, it is important to 
note that there are certainly more than 1,500 crime-related civil cases in the RAND data. 
For example, auto liability cases are the modal case type in the RAND data, and many of 
these cases could have resulted from a criminal event, such as an inebriated or reckless 
driver, a stolen vehicle or an escape.  However, these underlying criminal events cannot 
be discerned in the data.  
In prior studies, the general solution to this problem has been to model expected 
award (including non-economic damages) for each combination of injuries, identify the 
prevalence of injury types within broad crime categories and estimate the expected total 
harm for these crime categories. Thus, this approach first predicts model (3) to estimate 
the expected damages to the victim conditional on socio-demographic attributes and 
injury severity for each combination of injuries.  The expected harm per injury type is 
subsequently linked to data which associates injuries to crime type to observe the 
prevalence of injury types in specific crime categories, and the average of the jury awards 
 102
 
for each crime type, conditional on the distribution of injuries within each crime type, is 
calculated. In some prior research, estimates are generated only for non-economic awards 
with economic damages being developed from other secondary data.   
While the results of these studies are widely cited, there is a disconcerting amount 
of variation in the estimates across the main studies in the field, as shown in Figure 1. 
One source of the variation is the number of strong assumptions that have been made in 
these studies to overcome limitations in the data.  In particular, because prior research did 
not have access to micro-level data on both jury awards and micro-level crime data, the 
studies have reported a single point estimate for each broad crime category. Since nothing 
is known about the distribution of harms within crime categories, it is impossible to 
determine if all prior studies are reporting estimates within the same confidence interval, 
or are in fact generating widely divergent estimates. 
With case-level crime data in NIBRS becoming available beginning in 1998, 
more direct estimation of the hams from crime is possible.  The approach has two 
substantial advantages over earlier studies. First, it avoids reliance on secondary non-
crime data to estimate the prevalence of injuries within crime data, since injuries are 
directly observable in NIBRS. Given that some of the samples used to relate injuries and 
crime type are quite small (less than 10 for rape in Cohen, 1988 for example), using 
NIBRS data with more than two million records per year to estimate the relationship 
should yield more robust estimates. Second, it avoids errors due aggregation bias. That is, 
since prior studies rely on aggregate data relating injuries to crimes, they calculate 
average harm per crime type. They do not, however, estimate the expected harm per 
victim. If, for example, robbery victims are likely to experience either very serious 
 103
 
physical injuries or no physical injury at all, the average harm within the crime type will 
not reflect the actual experience of any victim.  Linking individual data on injury and 
crime will therefore identify these strata, but will also allow for the creation of 
confidence intervals to reflect the reliability of estimates.  
These data can also, at least partially, overcome the two challenges defined at the 
beginning of this chapter: potential non-representativeness in civil data, and small sample 
sizes. The first challenge can be overcome by linking expected jury award to subgroups 
comprised of combinations of victim attributes and injuries (as has been done in previous 
research) but then only estimating harms for subgroups that are observable in both 
datasets. This obviates the need for the strong assumption made in past research that 
subgroups that exist in the general population but that are not observable in the jury data 
have the same distribution of harms as the subgroups that are observable in both.  The 
second challenge can by making the assumption that juries award based on the attributes 
of a case, and not the type of case. Thus, all cases in RAND, regardless of their origin, 
can be used in the analysis. To weaken this assumption, propensity scores can be used to 
balance crime and non-crime civil cases across observable attributes and thus minimize 
differences between the two groups.  
This research does require the relatively strong assumption that harms are 
similarly distributed within subgroups across the jury and crime data. If harms are 
distributed differently within subgroups in the two data sets, particularly if serious harms 
are more common in the subgroups in the jury data than in the criminal data, then harms 
will be overestimated. This issue is discussed again in the limitations section. Still, it is 
reasonable to believe that this is the less serious of the two challenges. 
 104
 
Analysis Discussed in Chapter Three 
Chapter 3 mainly describes the preparation of the data for interpolation onto the 
NIBRS data set. Results of that interpolation are described in Chapter 4. The general 
approach is straightforward. The rest of the chapter proceeds as follows. First, the RAND 
data is described with particular attention to the construction of the dependent variable 
and the identification of cases as crime or not crime cases. The section that follows 
describes analysis, including the propensity score analysis, to estimate mean harms per 
subgroup. Additional analyses are reported in Chapter 4. 
Data  
Data from the RAND Institute of Civil Justice were collected in two datasets, an 
extract of data from 1985-1994 (series 1), and an extract of data from 1995-2000 (series 
2). Series 1 contained a total of 24,180 observations and 680 variables. Series 2 contained 
16,005 observations and 1,013 variables. There were substantial differences in the types 
of data that were contained in the two data sets and how information was coded 
describing each case. A single research database was created by creating consistent 
variables across the two databases. Decisions about which records to exclude are 
described below. 
Before any other data preparation, independent variables were identified that were 
consistently reported across both the RAND and the NIBRS datasets. Since fewer 
variables were recorded in NIBRS overall, data from NIBRS was examined to select 
independent variables that would be available for the final analysis across the two 
datasets (and are used to construct the profiles). The variables included: 
? Plaintiff (offender) attributes: (age, gender); 
 105
 
? Plaintiff injuries (none, minor injury, broken bones, internal injury, other major 
injury, loss of teeth, severe laceration, unconsciousness, death)); 
? Jurisdictional attributes (county population). 
 
Variables describing these attributes were then constructed from the two RAND series. 
Additional variables were constructed for the RAND data analysis to adjust for 
theoretical sources of bias.  
Definitions 
In the RAND data, there are six different terms to describe damages.  The definitions of 
terms are described below. It should be noted that these definitions following the 
definitions used in the RAND Codebook, and may be slightly different from the 
definitions that appear in other public literature on this topic.  
Specials.  In many jurisdictions, economic damages claimed by a plaintiff, especially in 
personal injury cases, are described as ?special?, although the terms ?damages,? 
?general damages? or ?special damages? may be used on occasion. Specials are 
defined here as  direct economic losses, including medical costs, including disability, 
and other costs, including lost wages, lost time, property damage, expenses (for 
example, transportation) and any other damage not specifically classified as medical 
(RAND 2000: 84)
11
.   
 
General Awards. General damages include all awards for unobserved economic losses, 
what are usually referred to as intangible losses in the cost-benefit literature. These 
include pain and suffering and emotional distress (85). 
 
Punitive Awards. Any award that is made for the purpose of punishing or deterring future 
tortuous activity.  This is sometimes referred to as an exemplary award (85).  
 
RAND Data Reduction 
Cases were dropped from the analysis for several reasons. First, cases were dropped 
where the plaintiff lost.  The logic for excluding these cases in similarly 
                                                 
11
  This coding scheme follows the instructions given by RAND to those coding the data contained in the 
jury victim reports. RAND Corporation ? Institute for Civil Justice (2000). Jury Verdict Update Project 
Coding Handbook.   
 106
 
straightforward?plaintiffs may lose a case because there was no harm from the tort, or, 
because the defendant in the case did not commit those harms. If the reason why the 
plaintiff lost was observable, it would be instructive to keep cases where a plaintiff 
claimed harm but the jury did not accept that claim. One criticism of the NIBRS data 
(and the National Crime Victimization Survey data) is that it may over-estimate the true 
number of crimes, since reporting crimes is relatively costless. If these data could be used 
to identify those events where a crime was reported, but in reality no crime was 
committed, this would allow for corrections for over-reporting. However, in the RAND 
data, it is not possible to observe why the plaintiff lost, so cases where the jury believed 
no tort occurred can be distinguished from cases where a tort did occur, but was not due 
to the actions of the defendant in the case. Thus, cases where the defendant was not found 
liable contribute no additional information and were deleted.  
Next, cases where the plaintiff was not an individual (alive or decedent) were 
dropped, including cases with a plaintiff who was a business, a government, another 
institution or not reported/missing. The logic of excluding these cases is simply that 
harms suffered by institutions are not analogous to injuries suffered by individuals 
because these crimes are likely to include white collar crimes. In Series 1, 1,898 (7.9 
percent) cases were dropped, including: business (1,744), government (37), another 
institution (34) or not reported/missing (85)
12
 with a total of 22,290 cases remaining. In 
Series 2, 1,103 (6.89 percent) cases were dropped, including: business (788), government 
                                                 
12
  Allison (2001) suggests that if fewer than 5 percent of data are missing for an item, than the data are 
ignorable and that threshold is used throughout this paper. In Series 1, missing totaled 0.35 percent of the 
sample.  
 107
 
(65), another institution (247) or not reported/missing (3) with a total of 14, 902 cases 
remaining.   
In Series 1 covering the period 1985 through 1994, there were a total of 22,290 cases. 
Of these, there were 11,120 cases where an adjusted award was observed, where adjusted 
award was the total of economic, non-economic and punitive awards, and this total was 
adjusted for comparative negligence. In addition, there were 744 cases where liability 
was observed but the aggregated adjusted award was missing. Total award is coded in the 
RAND data in several ways, so other variables describing awards were investigated to 
determine total award. In 344 of these cases, the adjusted award was calculated by 
summing observed damages awarded to the defendant if available, or adjusted plaintiff 
awards if available (there were no cases were these two items conflicted).  In 400 cases 
(3.69 percent of the remaining cases in Series 1), no award was observed on any 
indicator, and these cases were dropped. As a check, there were no cases where an award 
was observed but no liability was observed in Series 1. Finally, two cases were identified 
as class action lawsuits and were deleted, and six appeared to have gaps in defendant data 
and were also deleted. Thus, 11,456 cases remained in Series 1. 
Series 2 data were coded in a slightly different manner and thus a different set of 
adjustments were used to obtain the final dataset. In Series 2 covering the period 1995 
through 1999 there were a total of 14,902 cases. Of these cases, an adjusted award greater 
than 0 dollars was observed in 6,589 cases.  This total includes 66 cases where an 
adjusted award was observed, but liability was not recoded. These cases were classified 
as a plaintiff win and included in the dataset. In addition there were 8,313 cases with a $0 
award. In 277 of these cases at least one defendant was observed to have liability with an 
 108
 
adjusted award value of $0.  However, in some cases defendants may have been coded 
with a $0 value when there was no individual-level $0 award on the plaintiff sides. To 
differentiate these cases, cases were coded as having a $0 award when any of the 
defendants were coded as receiving $0 (122 cases or 1.79 percent). In 155 cases (1.79 
percent) there was an indication of defendant liability, but no indication of a finding of 
liability or an award on the plaintiff side. These cases were thus determined to have 
ambiguous outcomes and were dropped. Thus, a total of 6,711 cases remained.  
 Once the data were combined, cases were dropped if they were missing the 
independent variables that will be used to link the RAND and NIBRS data. Almost 3,000 
records were missing age of the plaintiff and were dropped.  Values for gender were 
missing in about 50 cases, and values were missing for injury (or were coded as 
?unknown?) and about 1,500 additional cases were dropped. As is described in the section 
below, some 170 cases were dropped because missing data on the distribution of 
economic and non-economic awards could not be calculated or imputed. Eleven other 
cases were dropped because the sum of economic, non-economic, punitive and shared 
negligence was not equal to total award, and these discrepancies could not be resolved. 
Thus, the final dataset contains 12,918 observations and all contained a valid 
award for damages. These cases are a stratified sample of all civil jury awards in the 
sampled jurisdictions between 1985 and 1999. Treatment of the weights in this analysis is 
discussed below. (Some additional coding was required to fix missing values for 
economic and non-economic damages (described in Appendix A.1)). 
 109
 
Adjustments to the Dependent Variable 
 Several adjustments to this variable were necessary before the data were analyzed. 
The total jury award has four components:  
? An award for economic loss, also referred to as direct losses, including lost 
property, lost wages, and health related costs; 
? An award for non-economic losses, also referred to as indirect losses, which 
include fear, lost or diminished quality of life, and pain and suffering; 
? Punitive awards, and  
? Adjustments for shared negligence.  
As is discussed below, valid data must be available for punitive awards in order to adjust 
those awards for each observation (the punitive award is removed before analyses are 
conducted). A ratio of economic to non-economic awards is required to compute a weight 
to adjust damages in cases with both property losses (but no other direct losses) and 
indirect losses. With respect to shared negligence, these reductions were ultimately not 
included in the final analysis. However, it is worth noting the potential impact these 
reductions may have on the final estimates.  Finally, the stratified sampling procedures 
used by RAND researchers to identify cases require that weights are applied to all 
subsequent analysis.  
Table 3.1 describes the number of cases in each state in each year, and the 
percentage of all cases that appear in a given state-year. In general, there is a trend toward 
more cases in the later years. Cases from Illinois and California make up a larger 
percentage of the sample in the later years as compared to the beginning of the series.  
 110
 
 
Table 3.1. Variation in the number of cases by state/region and year 
  State/Region 
Year 
 
California  Illinois Washington Texas Missouri  
New 
York  Total 
1985 
 
640 
(1.81%) 
 
86 
(0.24%)
90 
(0.25%) 
202 
(0.57%)
232 
(0.66%) 
 815 
(2.30%) 
 2,065 
(5.1%) 
1986  
914 
(2.58) 
 
253 
(0.71%)
91 
(0.26) 
234 
(0.66) 
195 
(0.55) 
 559 
(1.58) 
 2,246 
(5.6) 
1987  
1,005 
(2.84) 
 
297 
(0.84) 
86 
(0.24) 
273 
(0.77) 
225 
(0.64) 
 408 
(1.15) 
 2,294 
(5.7) 
1988  
831 
(2.35) 
 
232 
(0.66) 
110 
(0.31) 
239 
(0.68) 
237 
(0.67) 
 442 
(1.25) 
 2,091 
(5.2) 
1989  
906 
(2.56) 
 
272 
(0.77) 
129 
(0.36) 
309 
(0.87) 
206 
(0.58) 
 511 
(1.44) 
 2,333 
(5.8) 
1990  
1,074 
(3.03) 
 
279 
(0.79) 
124 
(0.35) 
285 
(0.81) 
187 
(0.53) 
 639 
(1.81) 
 2,558 
(6.4) 
1991  
1,124 
(3.18) 
 
378 
(1.07) 
71 
(0.20) 
310 
(0.88) 
206 
(0.58) 
 735 
(2.08) 
 2,824 
(7.0) 
1992  
1,191 
(3.36) 
 
263 
(0.74) 
80 
(0.23) 
311 
(0.88) 
241 
(0.68) 
 554 
(1.57) 
 2,640 
(6.6) 
1993  
1,135 
(3.21) 
 
286 
(0.81) 
79 
(0.22) 
352 
(0.99) 
208 
(0.59) 
 702 
(1.98) 
 2,762 
(6.9) 
1994  
962 
(2.72) 
 
245 
(0.69) 
63 
(0.18) 
286 
(0.81) 
141 
(0.40) 
 648 
(1.83) 
 2,345 
(5.8) 
1995  
1,066 
(3.01) 
 
421 
(1.19) 
57 
(0.16) 
462 
(1.31) 
329 
(0.93) 
 748 
(2.11) 
 3,083 
(7.7) 
1996  
1,051 
(2.97) 
 
379 
(1.07) 
56 
(0.16) 
470 
(1.33) 
272 
(0.77) 
 811 
(2.29) 
 3,039 
(7.6) 
1997  
1,518 
(4.29) 
 
380 
(1.07) 
70 
(0.20) 
435 
(1.23) 
300 
(0.85) 
 967 
(2.73) 
 3,670 
(9.1) 
1998  
1,302 
(3.68) 
 
371 
(1.05) 
57 
(0.16) 
324 
(0.92) 
179 
(0.51) 
 1,036 
(2.93) 
 3,269 
(8.1) 
1999  
1,132 
(3.20) 
 
393 
(1.11) 
46 
(0.13) 
307 
(0.87) 
76 
(0.21) 
 990 
(2.80) 
 2,944 
(7.3) 
Total  15,850  4,535 1,209 4,799 3,234  10,564  40,191 
Source: Data provided by the RAND Institute of Civil Justice. Two data sets were extracted, covering 
the periods 1985-1994 and 1995-1999.  Percentages of all observations in each state-year 
combination are shown in parenthesis.  
 
 111
 
Very few cases can be affirmatively coded as having resulted from a criminal 
incident. By category, there are 162 homicides, 168 sexual assaults, 971 physical 
assaults, 260 property (burglary) cases, and 194 theft (most of the rest of the intentional 
torts, 1,740, involve civil rights issues). In the few cases where the type of crime can 
clearly be distinguished in the data, there is even greater variability in award size, for 
instance, the mean award is about $1 million for a plaintiff who was assaulted, and the 
median is $6,520.  
Table 3.2. Variation in the probability of an award for the plaintiff by state/region and year 
  State/Region 
Year 
 California 
(n=15,850)  
Illinois 
(n=4,535)
Washington
(n=1,209) 
Texas 
(n=4,799)
Missouri 
(n=3,234)
New York 
(n=10,564) 
 Total (YR)
(n=40,191)
1985  52.7%  58.1% 60.0% 48.5% 64.7% 51.4  53.7 
1986 48.8 60.9 57.1 44.9 52.8 49.2 50.5 
1987  52.0  54.6 50.0 46.2 59.6 51.4  52.2 
1988 51.6 60.8 60.9 39.3 57.4 54.5 53.0 
1989  48.8  53.3 52.7 42.1 61.1 53.2  50.7 
1990 51.2 55.6 58.1 41.4 61.0 49.6 51.2 
1991  47.7  50.8 56.3 40.3 61.7 48.6  48.8 
1992 48.8 56.7 62.5 46.0 57.7 47.3 50.2 
1993  50.0  57.3 44.3 40.3 55.8 48.6  49.4 
1994 50.6 55.1 57.1 45.1 56.7 45.5 49.5 
1995  50.4  50.1 54.4 40.7 51.4 45.4  47.9 
1996 41.5 47.2 55.4 42.3 52.2 48.8 45.5 
1997  40.7  42.1 52.9 43.7 54.3 46.0  44.0 
1998 43.6 47.4 56.1 41.7 58.7 45.4 45.5 
1999  42.8  52.9 50.0 45.9 52.6 44.4  45.4 
Total 
(State) 
 47.6  52.5 55.5 43.0 57.2 48.1 
 
48.7 
Source: Data provided by the RAND Institute of Civil Justice. Two data sets were extracted, covering the 
periods1985-1994 and 1995-1999.  
 
The probability that a plaintiff won their case follows the opposite pattern of the 
number of cases. While Table 3.1 shows that the number of cases tends to increase over 
time, the probability of a plaintiff victory declines by the end of the series. While the 
overall probability of a plaintiff victory is 48.7%, the first year in the series (1985) had 
the highest probability of a plaintiff win (53.7%) and the final year in the series had the 
 112
 
second lowest (45.4%). The same pattern generally appears within each state?s data as 
well.  
The data appear to include all major categories of crime ? intentional torts include 
assault and battery; conversion/theft include property crimes; dram shop include alcohol 
related crimes; and other economic crimes, such as fraud, are included as well. However, 
while the data sets appears to include a broad spectrum of criminal related activity, there 
are few variables that can be used to directly link a crime to a civil case. Data include 
awards for actual damages (including property loss, lost wages, and health care costs), 
general damages (pain and suffering) and punitive damages (for specific and general 
deterrence).  The data also include substantial information about both the plaintiff and the 
defendant (age and gender), the facts surrounding the criminal event and harms (injuries) 
inflicted on the victim.  
 
Distribution of the Dependent Variable 
Table 3.3 describes the variation in jury award across the states for each of the 15 
years included in the series. There is variation in awards across time and across states, 
however the general pattern of awards is relatively stable. Overall, awards increase over 
time (even after adjusting for inflation). This result is not surprising given the data in 
Table 3.1 that shows increasing numbers of cases and Table 3.2 showing reduced 
likelihood of a plaintiff win suggests that the increase in award in Table 3.3 incentivizes 
more plaintiffs, with less convincing cases to pursue a civil award.  
 
 
 113
 
Table 3.3. Variation in the mean jury award by state and year (unadjusted) 
  State 
Year  California  Illinois Washington Texas Missouri  New York Total 
1985  
1,189,060    
(20,827,980) 
 
284,944   
(1,029,157) 
114,005 
(607,268) 
52,545,599 
(740,864,568)
99,011 
(555,053) 
 266,067 
(894,931) 
 5,641,545 
(232,003,373) 
1986  
259,688 
(1,318,840) 
 
432,836 
(2,758,696) 
49,425   
(99,235) 
177,118 
(870,300) 
35,957 
(118,686) 
 
498,820 
(2,974,706) 
 302,163 
(1,965,685) 
1987  
423,881 
(2,816,097) 
 
347,310 
(2,200,070) 
312,418 
(2,107,399) 
220,080 
(1,191,519) 
135,039 
(552,293) 
 
835,799 
(4,904,843) 
 430,467 
(2,962,405) 
1988  
591,671 
(7,047,241) 
 
635,114 
(2,012,277) 
83,332 
(215,743) 
575,284 
(3,592,206) 
75,527 
(230,289) 
 
668,510    
(1,937,040) 
 525,618 
(4,741,406) 
1989  
432,283 
(1,740,771) 
 
505,904 
(1,693,006) 
116,127 
(295,684) 
881,201 
(5,175,058) 
160,264     
(48,5101) 
 
906,401 
(3,753,288) 
 562,671 
(2,867,782) 
1990  
1,078,588 
(8,822,193) 
 
726,691 
(4,911,512) 
147,941 
(808,560) 
479,190 
(3,050,155) 
287,667 
(1,907,185)
 796,643 
(3,776,765) 
 803,790 
6,307,862) 
1991  
619,975 
(5,465,797) 
 
913,125 
(6,909,660) 
77,878 
(275,796) 
458,616 
(2,809,136) 
818,689 
(6,449,117)
 662,914 
(3,198,370) 
 653,543 
(4,982,966) 
1992  
498,166 
(3,240,493) 
 
490,205 
(1,733,136) 
369,929 
(1,623,820) 
1,648,809 
(15,669,879) 
231,041 
(1,573,171)
 656,571 
(3,185,678) 
 637,893 
(6,037,930) 
1993  
973,905 
(13,04,2202) 
 
780,468 
(3,942,395) 
103,015 
(333,058) 
1,868,211    
(17,568,457) 
528,115   
(5,486,344)
 855,372   
(4,891,884) 
 979,242 
(10,917,295) 
1994  
1,073,912 
(8,800,958) 
 
788,593 
(4,043,786) 
225,221 
(875,244) 
861,120 
(4,431,620) 
201,546 
(645,521) 
 716,705 
(3,298,416) 
 844,090 
(6,240,147) 
1995  
667,763 
(3,478,944) 
 
510,872 
(1,713,240) 
212,326 
(574,975) 
712,459 
(3,965,125) 
488,205 
(5,030,231)
 693,700    
(3,247,989) 
 631,748 
(3,492,789) 
1996  
893,818 
(8,671,075) 
 
963,280 
(6,720,538) 
135,233 
(450,770) 
1,377,547 
(13,526,266) 
297,106 
(1,927,602)
 987,690    
(4,408,671) 
 934,958 
(8,090,017) 
1997  
636,140 
(3,893,296) 
 
383,633 
(1,872,903) 
356,019 
(1,426,745) 
458,579 
(2,722,369) 
356,586 
(2,482,507)
 
807,120 
(3,229,372) 
 605,806 
(3,288,999) 
1998  
877,769 
(8,430,958) 
 
606,417 
(2,798,733) 
188,106 
(594,357) 
1,195,341 
(10,052,785) 
241,839 
(808,374) 
 1,052,249. 
(6,961,223) 
 886,898 
(7,390,533) 
1999  
5,181,604 
(146,554,937) 
 
980,717 
(4,514,093) 
225,312 
(849,900) 
959,297 
(6,456,571) 
474,787 
(2,393,368)
 938,005 
(4,681,190) 
 2,555,093 
(90,971,803) 
Total  
1,042,208 
(39,913,405) 
 
650,874 
(3,923,673) 
171,425 
(915,195) 
3,058,724 
(152,231,682)
295,440 
(2,948,880)
 770,398 
(4,084,302) 
 1,081,106 
(58,329,291) 
Source: Data provided by the RAND Institute of Civil Justice. Two data sets were extracted, covering the 
periods 1985-1994 and 1995-1999.  Standard deviation is in parenthesis.  
 
The pattern of awards across states is relatively stable over time. If the outlier award 
is dropped from Texas, then the mean award in Texas is about $913,000. Thus, there are 
two states with relatively high average awards around $1M (Texas and California), two 
states with moderate awards around $700,000 (Illinois and New York) and two states 
 114
 
with relatively small awards (Washington and Missouri). In 9 of the 13 years after 1985, 
New York or Texas has the highest average award. Washington or Missouri have the 
lowest award in every year.  
The mean values reflect the skew generated by the presence of a few very large 
awards. The data in Table 3.3 is consistent with the extant literature which predicts that 
jury awards are significantly skewed with a large number of relatively small awards, and 
a few very large awards. Ostrom, Rottman and Goerdt (1996) provide descriptive 
measures from the Civil Trial Court Network Project, which maintained data on eight key 
indicators of the civil jury in 45 urban state courts in the 1990s.  Again, few cases 
actually go to trial, from a low of 1.9% in automobile tort cases to a high of 8.2% in 
medical malpractice.  Moreover, plaintiff win rates vary by type of case.  These outcomes 
are important because they may define the bargaining range for out-of-court settlements 
(234).   In Ostrom et al., the median jury award is $52,000, but the arithmetic mean award 
is $455,000.  However, a 5% trimmed mean (on both sides) reveals an average award of 
only $159,000 in 1992 dollars (237).   
As was found in virtually every other study that measured jury awards, the data in 
this study are highly skewed.  The mean award ($1,328,677) is almost six times as large 
as the median award ($229,535). The problem has substantial bearing on outcomes. Past 
studies (including the MC series) have reported the costs of crime to victims at the mean, 
thus assigning the value to the average victim, rather than the typical victim which would 
be reported at the median.  In prior studies, researchers have tried to account for these 
differences in mean and median by transforming the dependent variable into a log. 
However, as discussed in Chapter 3, the most prudent approach to estimating the price of 
 115
 
crime to crime victims is to report key moments rather than to specify a regression model, 
which appears to cause more problems in this analysis than it resolves.  
 The alternative approach is to remove outliers that are contributing to the skew. 
On one hand, removing outliers is problematic, since these are actual awards. However, a 
review of the largest awards suggests that these are the cases that appear least to conform 
to the notion that jury?s only use the facts of the case to render a verdict. In these cases, 
the implied value of a life is in the tens or hundreds of millions, far outside the typical 
valuation (Viscusi, 1986). Thus, the approach taken here is to drop those cases that are 
more than three standard deviations from the mean award, or about one percent of cases.  
Given the skew in the data, all of the outliers that are removed from the analysis are at the 
upper end of the award distribution.  
Table 3.4. Distribution of Total Award (Unweighted) 
Category Total Award Punitive 
Total, 
Excluding 
Punitive 
Total, Excluding 
Punitive and Outliers 
All (N=12,918) $1,376,341 $133,036 $1,243,305 $895,091 (N=12,756) 
Crime Indicator     
      Crime (N=895) 1,372,276 257,570 1,114,705 737,251  (N=886) 
      No-Crime (12,023) 1,376,643 123,765 1,252,878   906,872  (N=11,870)
Issue      
     Crime (N=890) 1,372,278 257,570 1,114,705 737,251  (N=886) 
     Malpractice (N=2,219) 2,256,547 67,562 2,188,985  1,631,082   (N=2,194)
     Liability (N=8,500) 1,150,014 69,992 1,080,022   771,039  (N=8,397) 
     Other (N=1,304) 1,356,582 569,920 786,662  555,114  (N=1,279) 
Note: All records include a non-missing value for total award (n=12,918). All values are adjusted for 
inflation and presented in 2003 dollars. The ?Total Award? column includes all awards (before any 
reduction for shared negligence). The ?Total, Excluding Punitive? column is the total award 
without punitive award (before any reduction in shared negligence).  Total, excluding punitive and 
outliers, also removes outliers. Sample sizes are in parentheses.  
 
 116
 
 Before discussing the effect of removing outliers in Table 3.1, the other key 
adjustment in this table is the removal of punitive awards. As noted in Chapter 2, the 
usual approach in this literature is to drop punitive awards from the calculation of costs of 
crime to victims. The logic is straightforward. Punitive awards are designed as a deterrent 
to future negligence, and are not related to the harms experienced by the plaintiff in the 
case at hand. Thus, the punitive award contributes no information about the victim?s 
losses and is differenced out of the award.  
 In total, 162 cases were dropped from the analysis in cases where the total award 
(excluding punitive damages) was more than three standard deviations above the global 
mean. Once outliers were excluded, a total of 9 ?crime? cases (0.6%) and 153 ?no-crime 
cases (1.3%) were dropped from the sample. Within the no-crime category, 25 
malpractice cases (1.1%) were dropped, 103 liability cases (1.2%) and 25 ?other? cases 
(1.9%). Dropping these few cases had a substantial impact on the means. The overall 
average (after removing punitive awards) was reduced from about $1.243M to $895,091 
a reduction of 27.9 percent.   For cases coded as crime, the reduction was 33.9 percent 
while for cases that could not be coded as crime were reduced 27.6 percent (a discussion 
of the approach to coding crime versus non-crime follows in the next section).  Notably, 
only nine of the cases that could be coded as having originated from a criminal act were 
dropped as outliers.  The effect was similarly variable across the types of claims. The 
mean for ?Other? cases was reduced by 29.4 percent and the mean for liability cases was 
reduced by 28.6 percent. The reduction in malpractice awards was the smallest, with a 
25.4 percent reduction in average award. 
 117
 
 
Table 3.5. Mean of Total Awards with and without Outliers (Unweighted). 
  
All Cases Crime Cases Only
Category  Total 
No Outliers 
Total 
No Outliers 
Sample Size 12,918 12,762 895 886 
All Observations 
(Median) 
$1,243,305 
($202,615) 
$895,091 
($194,479) 
$1,114,705 
($111,628) 
$737,251 
($110,827) 
Note: All records include a non-missing value for total award. There are 12,918 in the 
full sample and 11,718 in the sample with the outliers removed. All values are 
adjusted for inflation and presented in 2003 dollars. The means and median values 
are after punitive awards have been removed, but do not include stratification 
weights. Median values are in parentheses. 
 
 Table 3.5 describes the effect of removing outliers. For all cases, the ratio of mean 
damage award to median damage award declines from 6.1:1 to 4.6:1. Within those cases 
coded as being the result of a crime, the mean/median ration declines from 10.0:1 to 
6.3:1. Not surprisingly, there is little effect of removing outliers on the means. Thus, it 
appears that removal of outlier?s more than three standard deviations from the mean 
reduces some of the effect of these observations on the average case, but does little to 
affect estimates for the typical case. 
Identifying Crime and Non-Crime Cases 
 Before making adjustments to the dependent variable, a variable is created that 
identifies whether cases can be coded as resulting from a crime, or not coded as resulting 
from a crime. This variable can be helpful in identifying the impact of adjustments for 
comparative negligence and punitive damages.  The RAND civil jury verdict data that 
will be used to estimate harms to victims of crimes includes many non-crime related civil 
cases. However, the RAND data does not include variables that allow crime-related cases 
to be clearly distinguished from non-crime related cases. Using a combination of 
 118
 
variables, 886 out of 12,756 were identified as resulting from a crime. These cases were 
identified by the type of claim or by the type of plaintiff injury. For example, cases with a 
gunshot wound (N= 95) were assigned to the crime category, as were rapes (N= 26).  
Cases in specific categories (conversion/theft (N= 44), RICO (N= 0) and assault (N= 
731)) were also coded as crimes.  
The indicator variable ?crime? denotes whether a case could be validly coded as 1 
if the case can clearly be identified as crime-related or 0 if the case cannot be 
affirmatively coded as resulting from a crime. This definition is substantively different 
from coding the case as crime or not-crime, which cannot be directly observed.  While 
the crime indicator is a dummy variable, it is important to note that there are not two 
categories of ?crime? cases in the RAND data, but three.  In addition to the cases that can 
be affirmatively labeled as crime case, the cases that cannot be affirmatively labeled as 
crime are of two types:  
? Cases that can validly be labeled as not resulting from a criminal act, and  
? Cases that are the result of a crime, but the underlying criminality of those 
cases cannot be distinguished from the data.  
For example, it is certain that some of the automotive cases were related to criminal acts, 
such as driving while intoxicated or reckless driving.  In addition, it is also certain that 
some of the negligence cases are criminal negligence cases.  Thus, those cases that cannot 
be affirmatively labeled as ?crime? related, cannot simply be labeled as not crime, and 
dropped from the analysis.  
 119
 
 The premise of this research is that injury data and other case attributes are 
unbiased predictors of award regardless of the type of claim.  According to Harcourt, the 
guiding principle of the criminal justice system should be that, "all similarly situated 
persons be treated alike" (2004: 1283). Any variance in award is therefore should be a 
function of the distribution of harms associated with the claim, rather than due to the type 
of claim. The same harms in each category?negligence, malpractice, liability, crime, and 
other?are expected to yield the same award. If these estimates are unbiased, then the 
award for each cross-combination of attributes can reasonably be used to predict awards 
in the NIBRS data.  If this premise does not hold, however, then the resulting NIBRS 
estimates will be biased.  
Returning to the issue of adjustments to the dependent variable, as is described in 
Table 3.1, valid observations for the total award and the punitive awards were available 
for all observations.  There is no difference in expected total award between the 886 
?crime? awards and the 11,870 non-crime awards (p=0.43).  Punitive damages are 
awarded as a means of deterring futures libelous behavior, and thus are awards that seek 
to achieve a goal beyond compensating victims for the harm they suffered. Thus, they are 
not included in the final estimates of harm, and are removed from the total. Although 
punitive awards are twice as large for crime cases as for non-crime cases at the mean, 
across all observations the difference is not significant (p=0.32). Once punitive awards 
have been removed, are significant differences in the expected award between crime and 
non-crime cases (p<0.01).  
 120
 
Comparative Negligence 
As noted in the far right column of Table 3.6, there are many cases where a determination 
is made that there is shared negligence, that is, where the jury determines that the plaintiff 
shares some fault for damages. In these cases, a determination must be made whether the 
full award should be used as the estimate of damages, or whether the reduced award is 
more appropriate since it accounts for the idea that but for the actions of the victim 
(plaintiff) there would not have been a claim. The choice is not trivial: the average total 
award is significantly reduced from $1.24 million to $1.04 million if the reduction due to 
negligence is included.  
One possible approach to resolving this issue might be to consider who a policy is 
directed toward, and calculate the value of harms accordingly. If a policy is intended to 
reduce the supply of crime, and is therefore directed at potential offenders, the full value 
of damages would best capture the magnitude of the harms the policy attempts to affect. 
Alternatively, if a policy is directed at potential victims (e.g., a crime prevention 
initiative) then developing estimates of harm that include reductions for comparative 
negligence is most appropriate. Finally, in the case where the policy is aimed at both 
parties, a mix of the two estimates would seem most appropriate. 
 121
 
 
Table 3.6. Distribution of Total Award (Unweighted) 
Category 
 
Total, Excluding 
Punitive and Outliers
Percent any Shared 
Negligence 
Mean Percentage of 
Shared Negligence 
All Observations (N=12,756) $895,091 25.4% 16.5% 
Crime Indicator    
      Crime (N=886) 737,251 15.9 10.7 
      No-Crime (11,870) 906,872 26.1 16.9 
Issue     
     Crime (N=886) 737,251 15.9 10.7 
     Malpractice (N=2,194) 1,631,082 11.6 7.7 
     Liability (N=8,397) 771,039 31.9 20.6 
     Other (N=1,279) 555,114 13.0 8.7 
      
Note: All records include a non-missing value for total award (n=12,918). All values are adjusted for 
inflation and presented in 2003 dollars. The ?Total Award? column includes all awards (before any 
reduction for shared negligence). The ?Total, Excluding Punitive and Outliers? column is the total 
award without punitive award and with outliers removed (before any reduction in shared negligence). 
?Percent any Shared Negligence? is the percentage of all cases (in that category) that have any 
?comparative? or shared negligence. ?Mean Percentage of Shared Negligence? is the average 
percentage reduction due to ?comparative? or shared negligence.  
 
 
For this paper, I chose to follow Cohen and Miller (2003: 167) who argue that 
?since juries are told to first determine the full level of compensation? the use of the un-
adjusted estimate is most appropriate. That is, since the goal of an estimate of the price of 
harm is to determine what harms were suffered, inclusion of a normative standard that the 
plaintiff can only claim those damages that were not their responsibility seems to only 
cloud the issue. Ultimately, if policy moves in a direction where the victim?s culpability 
is considered in determining the efficacy of a policy choice, then the damages adjusted 
for comparative negligence should be used instead.  
 122
 
Weights 
The RAND data is comprised of probability weighted random samples with unequal 
selection probabilities.  RAND researchers observed the prevalence of a type of case in 
the population of cases resulting in civil jury award. Cases were stratified to conserve 
coding resources. For the majority of cases (56.9 percent) there was no sampling and thus 
cases were assigned a weight of 1. In 9 percent of cases, every second case was selected, 
in 7.7 percent every third case was selected, and in 27.2 percent every fourth case was 
selected. All analysis includes the sampling weight using the FWEIGHT function in 
STATA 10.1 or the weight function in SAS 9.0.  To avoid having the effective sample 
size increase to 26,313 with the inclusion of the weights, the weights are normalized to 
sum to 12,756. The effects of weighting are shown in Table 3.7, which accounts for the 
stratification weights. As shown in Table 3.5, adding the weights to the analysis produces 
several slight differences, mainly a small increase in average award. 
 123
 
 
Table 3.7. Distribution of Total Award (Weighted) 
Category 
 
Total, Excluding Punitive and 
Outliers 
Total, Excluding Punitive and 
Outliers (Weighted) 
All Observations (N=12,756) $895,091 $921,015 
Crime Indicator   
      Crime (N=886) 737,251 768,287 
      No-Crime (11,870) 906,872 934,364 
Issue    
     Crime (N=886) 737,251 768,287 
     Malpractice (N=2,194) 1,631,082 1,590,433 
     Liability (N=8,398) 771,039 786,639 
     Other (N=1,279) 555,114 507,412 
    
Note: All records include a non-missing value for total award (n=12,918). All values are adjusted for 
inflation and presented in 2003 dollars. The ?Total, Excluding Punitive and Outliers? column is the total 
award without punitive award and with outliers removed (before any reduction in shared negligence). 
The ?Total, Excluding Punitive and Outliers (Weighted)? column is the total award without punitive 
award and with outliers removed (before any reduction in shared negligence) and applies the 
stratification weights. 
 
Effect of Adjustments to the Dependent Variable 
Thus, the cumulative effect of all of the adjustments in the data is to reduce the 
award by about 25 percent, while also reducing the standard deviation by about half?the 
mean award (excluding punitive damages) is $1.38 million (SD= $5.9M) in the 
unadjusted data and $1.0M (SD=$3.1) in the data that is weighted and has both the 
punitive awards and the outliers removed. From Table 3.5 it is clear that the adjustments 
had larger effects on particular categories. The crime category has a mean that is about 40 
percent smaller after the adjustments, and the ?other? category, which includes negligence 
cases, is reduced by more than half. The variance is substantially reduced in all 
categories. 
 124
 
Table 3.8. Distribution of Total Award (Weighted). 
Category 
 
Unadjusted Average 
Award 
(N=12,918) 
Total, Excluding Punitive and  
Outliers and Weighted 
(N=12,756) 
All Observations  
$1,376,341 
($5,893,546) 
$921,015  
($2,915.095) 
Crime Indicator   
      Crime  
1,372,278 
(6,101,927) 
768,268 
(2,770,531) 
      No-Crime 
1,376,643 
(5,878,000) 
1,016,258 
(2,924,938) 
Issue    
     Crime  
1,372,278 
(6,101,927) 
768,268 
(2,770,531) 
     Malpractice 
2,256,547 
(8,967,848) 
1,590,433 
(4,957,694) 
     Liability  
1,184,525 
(4,668,991) 
786,639 
(2,212,087) 
     Other 
1,356,582 
(6,167,062) 
507,412 
(1,646,160) 
    
Note: All records include a non-missing value for total award (n=12,918). All values are 
adjusted for inflation and presented in 2003 dollars. The ?Unadjusted Average Award? 
reports the averages before any adjustments. The ?Total, Excluding Punitive and Outliers 
(Weighted)? column is the total award without punitive award and with outliers removed 
(before any reduction in shared negligence) and applies the stratification weights. Standard 
deviations are in parentheses.  
Economic and Non-economic Awards 
While all 12,756 observations contain valid values for most components of the jury 
awards, there is substantial missing data on the distribution of economic and non-
economic awards within the total award.  In order to calculate non-economic damages for 
property crimes (where the economic damages will be calculated from NIBRS), missing 
data in economic and non-economic awards must be calculated whenever possible.  
Appendix A.1 describes the procedures used to recover economic and non-economic 
 125
 
damages. After these adjustments, a total of 5,539 cases had both economic and non-
economic damages and 7,217 did not. 
Selecting the Analytic Samples 
A critical question in this analysis is whether the RAND data are representative of 
all criminal cases.  The RAND data might be un-representative due to two issues. First, it 
may be that claims that end up being settled by a jury award are different from cases that 
are settled out of court, or not pursued in the civil court system at all. A substantial 
literature has emerged addressing this issue, and it is reviewed in Appendix A.2. Chapter 
4 includes a few empirical tests of this proposition, to the extent the data allow. That is, I 
test for whether the NIBRS cases that was matched with the RAND data are different 
from the NIBRS cases that did not match.  If the NIBRS dataset as a whole is 
unrepresentative of all crimes, as some have argued, that bias cannot be tested in this 
analysis. 
This section takes up the issue of whether the RAND data are unrepresentative 
when all cases and not just crime cases are included in the analytic sample. There are 
three possible analytic samples to use in this analysis: all cases, only cases affirmatively 
coded as resulting from a crime, and a sample from both groups that have been 
empirically balanced to control for differences both in case attributes and in variables 
theoretically associated with unrepresentative jury awards. Coding of the ?all case? 
sample and the ?crime? sample is straightforward. The section that follows describes the 
propensity score analysis. 
 126
 
Propensity Score Analysis 
The data presented in Table 3.5 show that there are substantial differences 
between the ?crime only? group, the ?all case? sample and the propensity score sample.  If 
a larger dataset can be retained the analysis would have substantial advantages over prior 
research, in terms of the power of the analysis and the number of types of crime that 
could be valued. In order to do so, it must be demonstrated that the cases that can be 
coded as resulting from a crime are not different from the cases that cannot be coded as 
having resulted from a crime across key theoretical predictors. Initially, there are only 
small differences in total award from crime ($1.372M) and non-crime cases ($1.376M) in 
the raw (but weighted) data in Table 3.4 (p=0.98). Once punitive damages are removed, 
the difference increases, but is still non-significant (p=0.43). However, when the outliers 
are removed, large and significant differences emerge (p<0.01) that persist once the 
stratification weights are added (p<0.05). 
One means of isolating the effect of crime on jury awards is to control for the 
confounding influences of other theoretically relevant covariates via multivariate 
regression (Sampson and Laub, 1990, 1993; Warr, 1998).  However, a substantial body of 
research (Greene, 1981; Heckman, 1977, 1990; Rosenbaum and Rubin, 1983) 
demonstrates that covariates alone are insufficient to attain unbiased estimates, and the 
problem is even more serious in this data as is described below.  Propensity score models 
have been proposed as a viable solution to modeling selection bias (Rosenbaum and 
Rubin, 1983; Heckman Ichimura and Todd, 1997; Dehejia and Wahba, 1999; Caliendo 
and Kopeinig, 2006).  Under certain conditions, propensity score analysis can 
approximate a randomized controlled trial and generate unbiased estimates (Caliendo and 
 127
 
Kopeinig, 2005; Rosenbaum and Rubin, 1983).  Propensity scores are used here to 
address the possibility that there are variables related to both crime and award.  The 
propensity score is the conditional probability of being in the crime category or the not-
crime category, Pr (T
i
 = 1 | X
i
), where T
i
 = 1 if the case is labeled as a crime and | X
i
 is a 
vector of covariates theoretically or empirically linked to the categorization of a case as a 
?crime? case.   
There is little advice in the extant literature about the ideal functional form that a 
propensity score model should take (Smith, 1997). As logit and probit models yield 
similar results for binary measures, I follow Caliendo and Kopeinig (2005) and use a 
logit specification as the logistic distribution has more density mass in the bounds. 
Predicted propensity scores can be sensitive to variable selection and omission of 
important variables in propensity score models can seriously bias the resulting estimates 
(Heckman Ichimura and Todd, 1997; Dehejia and Wahba, 1999).  However, over 
parameterization of propensity score models can decrease the support space of the 
propensity scores and increase the variance and the resulting standard errors (Augurky 
and Schmidt, 2001; Bryson Dorsett and Purdon, 2002).  Ultimately the choice of 
variables should be dictated both by relevant theory and by previous empirical findings 
(Caliendo and Kopeinig, 2005).   
I follow Heckman, Ichimura, Smith and Todd (1997) and begin with a 
parsimonious model containing several theoretically important predictors of selection.  
The model includes all case attributes that can reasonably be expected to have an 
association with whether or not the case was a crime.  The first variables added to the 
model are the variables common to both RAND and NIBRS (the variables that will be 
 128
 
used to create the cross-combination of attributes that will be used predict crime prices in 
NIBRS). These include age, gender, dummies for nine injury types and region. Next, 
variables are added that are theoretically linked to biased jury awards, including a 
business as a defendant (and the type of business), whether there was a punitive award, 
and whether there was shared negligence.
13
  Four variables that co-vary with whether a 
case was coded as a ?crime? or not are also included (population, number of plaintiffs, 
age-squared and number of issues).   Finally, selected interaction terms were added to 
each model (age by gender, gender by region) to ensure a model whose functional form is 
properly specified.  This process yields a propensity score model containing 28 
predictors.  Thus, the general model is a logistic regression model of the following form:  
Log(Y
j
/(1-Y
j
)= ?
 
T
j
 + ?*Z
 j
 + ?   
where Y
j
 is one if case j is coded as a ?crime? case and 0 if case j is coded as a non-crime 
case; T
j
 is the vector of independent variables that are observable in both RAND and 
NIBRS data and Z
 j
 is the vector of independent variables that are only observable in the 
RAND data.  
Tables 3.9, 3.10 and 3.11 describe the independent variables used in this analysis.  
                                                 
13
 The values of independent variables are described later in the chapter. The literature review early in this 
chapter describes five sources of bias in jury awards. These are extralegal factors that may lead juries to 
award plaintiffs more (or less) than they would receive if the jury?s award was strictly limited to the 
objective harms they suffered.  As the literature review at the beginning of this chapter suggests, certain 
types of cases?product liability and medical malpractice in particular?tend to have higher awards. In 
addition, there is substantial variation in awards by state; cases where the defendant is a business may 
receive higher awards; men receive larger awards than women on average; and cases with particularly 
reprehensible defendants have higher awards.  The purpose of including these variables is to balance the 
crime and non-crime cases along these attributes. But, to the extent that these factors may lead to an 
overestimation of the price of crime, they are not controlled for in the analysis. This is discussed in more 
detail in the next section ?Why Propensity Scores are Preferred to Covariates.? 
 129
 
 
Table 3.9. Distribution of Injuries in RAND 
  
Independent Variables Predicting Jury Award - Injury 
Injury Categories 
 All Cases 
(N=12,756)
Not Crime 
(N=12,023)  Crime (N=895)
None 7.8% 8.0% 10.1%** 
Dead 
 
11.0 11.1 9.7 
Broken Bones  23.4 23.5 23.0 
Internal Injuries  7.1 7.3 4.5*** 
Severe Lacerations  6.7 7.0 3.7*** 
Apparent Minor Injuries  27.5 27.0 30.0 
Other Major Injuries  49.0 49.6 42.3*** 
Loss of Teeth  5.3 4.9 10.3*** 
Unconsciousness 5.1 5.0 5.6 
Source: Analysis of data from the RAND Institute of Civil Justice, 12,918 cases from 1985-1999. 
Frequency weights are applied to all analyses. Injuries do not sum to 1 as individuals may report 
more than one injury.  All dollars are calculated as 2003 Dollars. Independent samples t-tests 
results are reported comparing crime and not crime categories. *p<0.05, **p<0.01, ***p<0.001.  
 
Most of the injury categories are significantly different when comparing the crime 
and the non-crime cases. Rates of internal injuries, severe lacerations and other major 
injuries are lower in the cases coded as resulting from crime then in the cases not coded 
as resulting from crime. Rates for loss of teeth and no injury are lower in the crime 
category. There is no difference in rates of death, broken bones, apparent minor injuries 
and unconsciousness. 
Virtually all of the theoretical predictors of jury award bias differ between the two 
groups. Cases in the crime group involve fewer plaintiffs, appear a little earlier in the 
sample and have slightly younger defendants.
14
 A significantly smaller percentage of 
                                                 
14
  In the RAND data, a specific age is observed for all plaintiffs, except those under 18, who are 
categorized as ?under 18?. Since there was no available information to impute those ages, five age 
categories were created: under 18, 19-29, 30-39, 40-49, and over 50. These categories were used as well in 
 130
 
defendant were businesses in the crime group, and there were far more punitive awards 
(as noted in Appendix A.3, if there was a punitive award, it was reverse-coded so there 
was a value=0 for the dummy indicating the opportunity for a punitive award). Females 
were less common in the crime category and cases were significantly more likely to come 
from the west and less likely from the northeast. 
Table 3.10.  Theoretical Predictors of Jury Award Bias 
  
Theoretical Predictors of Jury Award 
Injury Categories 
 All Cases 
(N=12,918)
Not Crime 
(N=12,023)  Crime (N=895)
Number of Plaintiffs  1.29 1.29 1.24** 
Mean Year of Case 
 
1992 1992 1991***
Victim Age  3.58 3.63 3.05*** 
Defendant is a Business  45.0% 45.5 40.0*** 
Punitive Award  4.6 3.2 20.1*** 
Case After 1990  62.2 63.1 52.1*** 
Gender (Female=1)  42.4 43.5 30.9*** 
Region (South)  3.7 3.7 3.1 
Region (Midwest)  25.4 25.4 25.7 
Region (Northeast)  30.0 30.7 21.7*** 
Region (West)  40.9 40.1 49.5*** 
Source: Analysis of data from the RAND Institute of Civil Justice, 12,918 cases from 1985-1999. 
Frequency weights are applied to all analyses. All dollars are calculated as 2003 Dollars. 
Independent samples t-tests results are reported comparing cases categorized as crime to cases 
not categorized as crime within each row. *p<0.05, **p<0.01, ***p<0.001.  
 
The type of claim
15
 also varied significantly across the two groups. In the crime 
category, there were significantly more ?other? malpractice cases, dramshop (alcohol 
outlet) cases, as well as defamation, civil rights, intentional torts, property, 
conversion/theft, and other business cases. There were significantly fewer vehicle/auto 
                                                                                                                                                 
the creation of the cross combination of attributes in the RAND data. Thus, a value of 3.05 suggests the 
average person in the crime category was in their 30?s. 
15
  RAND researchers coded more than one type of claim if appropriate. 
 131
 
liability and common carrier liability cases, as well as fewer medical malpractice, product 
liability and wrongful termination cases.  There was no difference in the prevalence of 
property/premises, insurance/bad faith and other negligence cases. 
Table 3.11.  Types of Claim in Civil Cases 
 
Independent Variables Predicting Jury Award ? Issue 
Injury Categories 
All Cases 
(N=12,918)
Not Crime 
(N=12,023)  Crime (N=895)
Vehicle/Auto Liability  37.2% 40.2% 2.7%*** 
Common Carrier Liability 1.8 1.9 1.0* 
Property/Premises Liability 23.8 23.9 22.5 
Medical Malpractice 17.9 19.3 1.7*** 
Other Malpractice 5.3 4.9 10.0*** 
Product Liability 9.5 10.3 0.9*** 
Dramshop 1.0 0.6 5.0***
Defamation 0.4 0.3 1.0* 
Civil Rights 3.7 2.1 22.6*** 
Intentional Tort 7.5 0 93.8*** 
Other Negligence 5.4 5.4 4.5 
Insurance/Bad Faith 1.5 1.6 0*** 
Wrongful Termination 2.8 2.9 1.2** 
Property Suit 0.2 0.1 1.2*** 
Conversion/Theft 0.4 0 4.7*** 
Other Business 3.0 2.9 4.2* 
Source: Analysis of data from the RAND Institute of Civil Justice, 12,918 cases from 1985-1999. 
Frequency weights are applied to all analyses. There were no RICO cases or shareholder cases. 
RAND researchers coded cases into more than one category.  Independent samples t-tests results 
comparing cases coded as crime and cases coded as not crime are reported. *p<0.05, **p<0.01, 
***p<0.001.  
 
To generate the propensity score, a logistic regression was run where the binary 
dependent variable (crime or not crime) was regressed on the variables in Tables 3.6 and 
 132
 
3.7.
16
 In addition, interaction terms describing the interaction between gender and age 
and region where added to the model, along with a squared age term. In the best fitting 
model, including the propensity score weight,
17
 independent samples t-tests of the 
differences between crime and non-crime cases find that 19 of the 23 attributes are 
significantly different at p<0.05.   
Choice of Weighting or Matching 
The results of the propensity model can be used to generate several different types 
of corrections for group imbalance. One common approach is to match observations 
where the predicted probability is similar, and to delete those observations that are 
outside the range of common support. However, such an approach requires that the 
groups are relatively equivalent in terms of the number of observations in each group. In 
this analysis, the two groups are not equivalent in size ? the crime coded group is about 
one-fifth the size of the non-crime group.  While nearest neighbor matching could still be 
performed using a 5 to 1 match, with replacement, I find little support in the literature for 
that a high a many to one ratio. Instead, I generate inverse probability of treatment 
weights, which are a common correction in the propensity literature. Using the fitted 
values from the propensity score models, I follow Sampson, Laub and Wimer (2006) and 
construct IPTW weights to account for selection into the crime category.  Each case is 
assigned a weight that is the inverse probability of crime receipt conditional upon T
j
 and 
                                                 
16
  The type of claims in Table 3.11 were not added to the model, since the dependent variable was 
constructed from those claim categories, or sub-categories.  
17
  The propensity weight and the stratification weight were combined into a ?super-weight?, as is discussed 
later in the chapter. 
 133
 
Z
j
. Thus, the crime cases that resemble non-crime cases along T
j
 and Z
j
 and the non-
crime cases that resemble crime cases along X
i
 receive the greatest weight in the analysis.  
These weights were then standardized in the same manner as the RAND 
stratification weights. The product of the two weights creates a ?super-weight? for each 
observation in the analysis. This combined weight jointly accounts for an observation?s 
probability of stratification and selection, and these weights are used in all models that 
control for selection. In order to ensure that no single observation had an undue amount 
of influence on outcomes, weights were winsorized at a value of four.  Notably, when 
crime prices are estimated for crime types that do not account for selection (all non-
person crimes); only the stratification weight is used. 
Reducing the Sample to Achieve Better Balance on Covariates 
Thus, the initial propensity score models failed to adequately balance the sample. 
While there is no completely satisfactory means of testing whether a propensity score 
model has created a weight that yields a more balanced model, the goal of the modeling 
is to create groups that are equivalent on attributes that predict assignment.  Thus, there 
should be no more differences in these attributes than is predicted by chance. However, 
the global test of the hypothesis that all coefficients were equal to zero was rejected at 
(p<0.001). While this test is less reliable in large samples, the p-value suggests 
substantial unexplained heterogeneity in the propensity score models.  
One likely source of heterogeneity was the unbalanced distribution of the 
dependent variable (886=1; 11,870=0). The implication of this imbalance is that there 
were types of cases in the non-crime cohort for which there was no similar match in the 
smaller crime cohort.  One solution to this problem is to only include those cases with an 
 134
 
analogue in the other group.  In order to create a more balanced sample, cross-
combinations of all the covariates in the crime and no crime group were created. Only 
those cross-combinations which were observed in both groups were retained.  
Selecting only those observations with common attributes would theoretically 
create a more consistent dataset for analysis. If, for instance, malpractice cases with 
female defendants were not observed in the original dataset, there would be no way to 
control for differential jury verdicts between that group in the crime and not-crime 
conditions. This resulted in a much smaller dataset being available with a total of 5,403 
observations. A total of 603 crime cases (weighted by the stratification weights to 
resemble 585 cases) and 4,800 not-crime cases (weighted to resemble 4,770 not-crime 
cases) were observed. Next, this sample was used to create the new propensity weights. 
The propensity score model was re-run using the original specification, and the inverse of 
the probability condition on crime is calculated.  
When the global test of the hypothesis that all coefficients were equal to zero is 
re-calculated, the hypothesis is again rejected (p<0.001).  In small datasets this might 
indicate a lack of balance. However given the size of this sample, and thus the statistical 
power, failing to reject the null would require close to perfect balance.  To ensure that the 
weights and properly balancing the sample, weighted t-tests were run on the sample of 
5,403 jury cases using the RAND stratification weight alone, and the super-weight.  
These results suggest a substantial improvement in the balance across the two 
samples. Table 3.13 describes t-test results comparing the ?Crime? sub-group to the ?Not 
crime? subgroup on the independent variables (excluding interactions). The statistic 
reported is the difference between the two groups, first adjusting only for the 
 135
 
stratification weights in RAND, and then adjusting for both the stratification and IPTW 
(the ?superweight?). Accept for age, the variables are mean percentages, and thus the 
statistic reported is the percentage difference between crime and not crime.  
Table 3.12.  Propensity Score Diagnostics (N=5,403) 
 
Difference Between ?Crime? Mean and ?Not Crime? Mean  
Independent Variables No Propensity Weight w/Propensity Weight 
Age (1=?Crime?) 0.232*** -0.003  
Gender 0.035+ 0.023 
Region (Midwest) -0.048** 0.024    
Region (West) 0.002 -0.060** 
Region (South) 0.006 0.068 
Defendant a Business 0.026 0.029 
Shared Negligence 0.018* -0.015 
Punitive Award -0.004*** -0.004 
Defendant (Government) -0.125*** -0.06*** 
Defendant (Hospital) 0.08*** 0.077*** 
Defendant (Individual) -0.038+ -0.093*** 
No Injury -0.020+ -0.013 
Dead 0.0053 0.061 
Injuries/Broken Bones -0.060*** -0.020 
Internal Injuries -0.021** 0.001 
Severe Lacerations -0.020** 0.005 
Minor Injuries -0.062*** 0.003* 
Other Major Injuries 0.129*** 0.044 
Loss of Teeth -0.052*** -0.008 
Unconsciousness -0.043*** -0.006
Population 0.034 0.019 
Plaintiff Count 0.024 0.021** 
Number of Issues Adjudicated -0.62*** -0.058 
Source: Analysis of data from the RAND Institute of Civil Justice, 5,403 cases from 1985-1999. 
Frequency weights are applied to all analyses. The final column includes IPTW and thus 
adjusts using the ?superweight?. Independent samples t-tests results comparing cases coded as 
crime and cases coded as not crime are reported. +=p<0.10, *=p<0.05, **=p<0.01, 
***=p<0.001.  
 136
 
Using only the RAND stratification weights, 14 of the 23 independent variables 
had significantly different values for the crime and not-crime cohorts (p<0.05) and three 
others were significant at p<.10.  However, once the super-weights were applied, six of 
the independent variables are significantly different at p<0.05.  Age, whether or not the 
jury had the opportunity to make punitive awards, the number of issues adjudicated, and 
all of the injury categories become non-significant after the super-weight is applied. Of 
the six variables that remain significant, three measure the same construct, whether or not 
the defendant is an individual. Given that one or two variables should be significant by 
chance, it appears the super-weights do a reasonably good job of balancing the two 
samples. Thus, the smaller sample size and super-weights were retained and used in 
subsequent analyses. Some additional discussion of the construction of the independent 
variables can be found in Appendix A.3. 
 Why Propensity Scores are Preferred to Covariates 
The obvious alternative to the propensity score models is simply to use covariates 
to control for those factors that are related to selection into the ?crime? group and those 
factors that are related to theoretical predictors of extralegal jury awards. Taking up the 
latter issue first, the problem with not including variables to control for the effect of 
extralegal factors on jury awards is that the resulting price of crime estimates will include 
these factors when they should not be included in the crime price. Thus, the preferred 
approach would seem to be to model Y= ?+?
1
X
1
+ ?
2
X
2
 +? (3).  In (3) X
2 
is a vector of 
variables that theoretically predict bias in jury awards with respect to actual victim losses. 
The model should yield an unbiased estimate of jury award by crime type, ?+?
1
X
1
.  
 137
 
The problem with this model is that the vector X
2 
is not observable in the NIBRS 
data.  If the awards associated with injury and other attributes in RAND are modeled with 
variables that are not in NIBRS, then the models will implicitly predict values in NIBRS 
as a function of attributes that are not observable in those data, including most of these 
selection factors.  More formally, modeling covariates in the RAND model assumes that 
those covariates have the same mean in the NIBRS data, which is clearly not correct 
since many of the extralegal factors associated with biased jury awards are not observable 
in NIBRS.  
Returning to the issue of using theoretical predictors to control for differences 
between crime and not crime cases, it may be the case that these attributes are 
heterogeneously related to the type of case. Certain factors cause jury?s to award on 
extralegal factors differentially in crime cases than in medical malpractice cases. Thus, it 
is necessary to balance the crime and non-crime cases along this attribute. In this case, 
those differences are accounted for via weight, which effectively re-orders the data, rather 
than by a propensity score covariate, which would incorrectly imply an identical 
propensity score mean in the NIBRS for that observation. Unfortunately, the lack of 
extralegal factors in NIBRS means that any part of the jury award that is due to extralegal 
factors cannot be corrected in the crime price estimates. 
Results 
 Table 3.13 describes the differences in means and medians for the three analytic 
samples: (only cases affirmatively coded as resulting from crime, cases in the propensity 
score models, and all cases). Overall, the estimates are relatively consistent. The largest 
average awards are for those cases in the propensity model, but the average award for 
 138
 
those cases ($981,600) is close to the estimate from all cases ($895,401) and the median 
of the propensity cases and all cases differ by less than $3,000. Awards for those cases 
affirmatively coded as crime cases are lower. Overall, the highest average award was in 
the propensity cases in 4 of the 9 injury categories, in the all cases for three injury 
categories, and in the crime cases for the other two categories.  
Table 3.13. Award Estimates by Type of Injury, RAND Data Only 
  Costs by Injury Category 
 
 
Crime Only (N=886) 
Propensity Model 
(N=5,403) 
 All Cases (N=12,756) 
Injury Type  Mean Median Mean Median  Mean Median 
None  $368,823 $31,876 $423,460 $114,421 $356,614 $100,330 
Dead 
 
1,985,398 911,261 1,854,949 1,146,531 
 
1,645,356 879,604 
Injuries/ Broken Bones  358,638 74,154 708,886 222,316  585,164 165,076 
Internal Injuries  1,482,423 190,622 1,744,959 661,737  798,798 325,917 
Severe Lacerations  1,771,304 1,214,796 1,751,367 1,183,395  1,637,578 758,565 
Apparent Minor Injuries  321,275 34,264 286,735 51,712  361,801 74,284 
Other Major Injuries  844,058 139,350 1,143,109 197,595  1,065,753 216,282 
Loss of Teeth  386,382 63,604 423,308 100,968  472,747 104,966 
Unconsciousness  313,047 101,532 381,595 90,148  497,094 77,747 
Average Award  $737,251 $110,827 $981,600 $197,423  $895,401 $194,479 
Source: Analysis of data from the RAND Institute of Civil Justice, 12,918 cases from 1985-1999. Frequency 
weights are applied to all analyses. All dollars are calculated as 2003 Dollars.  
 
Conclusion 
 The selection of a smaller sample using common cross-combination of attributes 
and the creation of IPTW using propensity score analysis completes the preparation of 
the RAND data for interpolation onto the NIBRS data. Chapter 4 describes the 
interpolation and presents estimates of the costs of crime to victims. Chapter 5 describes 
the implications for policy and research.  
 
 139
 
 
 140
 
Chapter Four: Estimates of the Price of Crime 
 
This chapter describes the analytic strategy to interpolate jury award data onto the NIBRS 
data and reports prices for 31 crime types.  Chapter 3 described how mean values for 
each sub-group (each cross-combination of case attributes) was computed. In Chapter 4, 
the mean value for each cross-combination, or subgroup, from the RAND data is then 
interpolated onto the NIBRS data. Variation in this analysis results from the distribution 
of subgroups across crime categories. One subgroup may be observed in multiple crime 
categories, and multiple subgroups may be observed in each crime category. For 
example, a 30-39 male with major injuries may appear in NIBRS data in assault cases 
and in robbery cases. In addition, within the assault robbery cases in NIBRS there are 
also other combinations of age, gender and injury.  
Thus, the average harm to a victim of a particular crime can be estimated as the 
average of the total harms of all victims of a particular type of crime in that category. 
That is, the total harms are summed across the heterogeneous distribution of injuries and 
victim attributes within that category, and divided by the number of cases.  This process 
is repeated for each of the 31 crime categories for each of the three analytic samples: all 
cases, only cases affirmatively coded as being related to a crime, and the propensity score 
weighted model.  Ex ante, the propensity score model is preferred, since it requires the 
weakest assumption about the generalizability of the RAND data, but results from all 
three analyses are presented.  Notably, the approach described above is only applied to 
data on the most serious person crimes. More direct estimation is used to estimate the 
prices of less serious crimes. 
 141
 
The chapter is structured as follows. First, I address how to deal with cases where 
multiple crimes occur. Next, I describe the types of crimes for which estimates will be 
developed. The analytic strategy for each of those crimes is discussed, followed by a 
description of the price estimates for each category. The chapter concludes with a 
discussion of the differences between the NIBRS cases that were matched to the RAND 
data, and the implications of those differences for the generalizability of the results. 
 
Multiple Victimizations during a Single Event 
If, as is suggested above, the analysis should account not only for the risk that a 
robbery becomes a homicide, but also for the risk that a robbery includes less serious 
crimes. Finally, there is the issue of victims suffering victimization from multiple crimes. 
That is, the estimates generated above are interpretable only as the cost to a victim whose 
only charge is robbery, for instance. The approach taken here is simply to sum up the 
costs for each crime, for each victim. That is, for a robbery victim whose car was stolen, 
the total harm is the sum of the costs of the robbery (conditional on their age, gender and 
injury) and the costs of the stolen vehicle.  The limitation of this approach is that it treats 
each criminal incidence as if the victim was not the same, and thus does not account for 
the fact that some injury patterns may be associated with victimization in more than one 
crime.   
Estimating Losses in Serious Property Crimes 
Crimes are defined as most serious when the crime commonly results in property loss and 
lost wages or health care costs, and the crime results in indirect harms (pain and 
suffering, and/or fear).  As described below, selection of crimes into this category is 
 142
 
based on FBI crime classifications and prior research on the costs of crimes to victims. 
Ten crimes were assigned to this category:  
? Murder/Non-negligent Manslaughter ;  
? Kidnapping/ Abduction;  
? Forcible Rape;  
? Forcible Sodomy;  
? Sexual Assault with Object;  
? Forcible Fondling; 
? Robbery; 
? Aggravated Assault; 
? Simple Assault; 
? Intimidation; 
 
Additionally, the price of crime was estimated for eight crime categories where 
the only direct losses were property losses. These crimes include: 
? Arson; 
? Extortion/ Blackmail; 
? Burglary/ Breaking and Entering; 
? Motor Vehicle Theft; 
? Counterfeiting/ Forgery; 
? Swindle; 
? Credit Card; 
? Impersonation; 
 
For these crimes, an assumption was made that in addition to property loss, victims suffer 
indirect losses. As discussed below, the basis for this assumption was the finding in the 
RAND data that cases in the theft/conversion category generally had an indirect award as 
well as a direct award. For these types of crimes, property losses were observed directly 
from the NIBRS data. In addition, to account for the indirect losses, the cases were 
weighted. Weights were generated from the RAND data as the coefficient of indirect to 
direct losses in cases where there was no injury or only minor injuries. 
 Finally, prices were estimated for an additional 13 crimes where losses were 
assumed to be limited to property loss alone. While it is conceivable that some indirect 
 143
 
harm occurred in these cases as well, there was no empirical justification for the inclusion 
of an indirect loss, and so none was included. Thus, to the extent that there is an indirect 
loss in addition to the property loss, these estimates underestimate the true price of these 
crimes: 
? Pocket-Picking; 
? Purse-Snatching; 
? Shoplifting; 
? Theft from Building; 
? Theft from Coin-Operated Machine; 
? Theft of Motor Vehicle Parts; 
? Theft from Motor Vehicle; 
? All Other Larceny; 
? Welfare Fraud; 
? Wire Fraud; 
? Embezzlement; 
? Stolen Property Offenses; 
? Destruction/ Vandalism; 
 
Results 
Estimating Losses in Serious Person Crimes 
Table 4.1 describes the estimated prices for serious person crimes. Serious person crimes 
can result in economic losses of all three types (direct (wages and health), direct 
(property) and indirect (fear, diminished value of life, pain and suffering).  
 144
 
 
Table 4.1. Estimates of Harms for Serious Injuries (RAND and NIBRS Data) 
  
Crimes with Direct and Indirect Costs 
Crime Only Propensity Model  All Cases 
Crime Type  Mean N Mean N  Mean N 
Murder/Non-negligent 
Manslaughter  
$1,532,342 (N=1,146) $1,445,463 (N=818) $1,466,160 (N=2,369)
Kidnapping/ Abduction 
 
64,358 (6,117) 140,697 (6,115) 161,433 (9,565) 
Forcible Rape  64,774 (11,487) 107,486 (11,486) 190,366 (21,668) 
Forcible Sodomy  103,359 (1,456) 425,168 (1,456) 229,024 (4,207) 
Sexual Assault with Object  55,767 (1,100) 142,261 (1,100) 198,353 (2,585) 
Forcible Fondling  52,958 (7,072) 162,235 (7,071) 195,264 (22,006) 
Robbery 197,741 (31,542) 279,085 (31,524) 236,487 (45,458) 
Aggravated Assault  223,180 (76,256) 283,793 (76,114) 307,768 (120,148) 
Simple Assault  77,008 (342,201) 101,624 (342,201) 127,356 (501,645) 
Intimidation 57,850 (137,362) 117,625 (137,362) 151,726 (175,605)
Source: Analysis of data from the RAND Institute of Civil Justice, 12,918 cases from 1985-1999 and 2000 NIBRS 
data. Frequency weights are applied to all analyses. All dollars are calculated as 2003 Dollars.  
 
 Overall, the propensity results generally predict the highest awards and the cases 
affirmatively coded as resulting from a crime produce the lowest awards.  Crimes 
generally follow the expected pattern with respect to the ranking of crimes by severity. 
Homicides have the highest prices, and simple assaults and intimidation are the lowest.  
The least variation appears in the group of all cases, and the greatest variation appears in 
the crime category. 
 As will be discussed in Chapter 5, when these estimates are compared to extant 
estimates, they appear very similar. The relative ranking is similar in terms of the severity 
of crimes is similar, and the ratio of prices comparing more severe to less severe crimes is 
also similar.  However, it is somewhat difficult to compare these estimates directly. This 
study has many more categories of crime than appear in other studies. Thus a direct 
 145
 
comparison of prices is difficult.  For instance, there are four classifications of rape in the 
present study, and generally only one in other studies.  Similarly, aggravated and simple 
assault are combined in most prior work, but disaggregated in this study. To create a set 
of estimates that are more easily compared to extant estimates, Table 4.2 presents the 
main crime categories presented in past work. The rape category is presented as the 
average of the sub-categories (weighted by the prevalence of each subcategory).  
Table 4.2. Price Estimates for Aggregated Part One Crimes, Propensity Score Models 
  
Crimes with Direct and Indirect Costs 
Crime Type 
 
Mean 90% 75% 
Median  25% 10% 
Murder  
$1,445,463 $2,838,800 $1,782,500
$1,380,246 $848,183 $272,169 
Rape 
 
149,542 238,395 214,449 
18,908 3,524 1,393 
Robbery  279.085 605,225 334,515 88,915 68,326 18,908 
Assault  134,770 334,515 155,270 66,644 13,285 611 
  Agg. Assault  283,794 569,701 294,335 89,815 27,956 1,900 
  Simple Assault  101,623 238,396 87,000 59,083 35,239 600 
Source: Each of the estimates is derived from the study cited. All estimates are presented in 2008 
dollars (Cohen (1988) is in 1985 dollars, Miller et al. (1996) are in 1993 dollars. The rape data in 
this study are a weighted average of forcible rape, forcible sodomy and sexual assault with an 
object.  The assault data from this study includes a weighted average of aggravated assault and 
simple assault, assault data from other studies may include aggravated or attempted assaults. The 
French and McCollister study presents estimates for aggravated assault only.  The larceny/theft 
value in the this study is the weighted average mean of NIBRS categories: Theft From Building, 
Theft From Coin-Operated Machine or Device, Theft From Motor Vehicle, Theft of Motor 
Vehicle Parts/Accessories, All Other Larceny. 
 
The estimates in Table 4.2 suggest that there is a substantial skew in the awards, where a 
small number of cases have exceptionally large awards.  For every serious crime other 
than murder, the mean award is substantially larger than the median, generally two to 
three times larger. It is also important to note that for these crimes it is common for a 
victim to suffer relatively small damages. In every crime but murder, the tenth percentile 
 146
 
of cases experiences damages that are an order of magnitude smaller than the mean 
award.  
Estimating Losses in Less Serious Property Crimes 
As has been noted, not all types of crime are represented in the RAND data. Civil 
juries only hear cases where the expected award is above some unknown threshold of 
opportunity cost. This leads to the hypothesis that jury awards over-sample more serious 
crime and under-sample or exclude less serious crime. While much of the paper is 
concerned with the issue of how to deal with potential over-estimation in the most serious 
crimes, this section addresses the converse ? how to estimate losses from crimes that are 
unlikely to result in physical harms, and thus that are unlikely to be represented in the 
RAND jury data.   
To account for potential bias due to under-representation of crime types, crime 
types were in the RAND data stratified ex ante into two categories ? those crime types 
that were expected to be represented in the RAND data, and those crime types for which 
no analogue in the RAND data was expected. In general, less serious crimes are assumed 
to have damages that are overwhelmingly related to property loss (while most criminal 
incidents fall into this category, including larceny, vandalism and shoplifting, most prior 
research suggests that these crimes account for a small percentage of total harms to 
victims). Thus, for crimes where losses are assumed to be due to property loss and not 
other economic losses or non-economic losses, property losses were calculated directly 
from NIBRS data.  
However, it is reasonable to presume that some crimes that lead only to property 
loss will have an indirect cost to victims. While serious person crimes that involve 
 147
 
property loss have been discussed above, other property crimes, such as burglary have 
been consistently shown to have substantial indirect costs in addition to the property loss 
(Cohen, 1988; Miller et al., 1995; Rajkumar and French, 1997; Cohen et al., 2004; 
McCollister, 2004). In fact, since crime is an involuntary and unwanted transaction, it 
would be reasonable to presume that all criminal events involved some indirect loss. 
However, some of the indirect losses are so small that the variation introduced by 
estimation is likely to outweigh the gains in terms of explanatory power. The challenge is 
to determine which types of property crime should have an indirect element, and which 
should not. The somewhat arbitrary decision in this analysis was to include property 
crimes that could be charged as felonies as crimes that likely have an indirect component, 
and to assume no indirect cost for property crimes that do not have an indirect element.  
The logic behind this assumption is straightforward.  Non-monetary sanctions 
(correctional sentences) reflect society?s evaluation of the harms associated with criminal 
offending (Becker, 1968; Ehrlich, 1973; 1996; Shavell, 1985; 1987a; 1987b; 1991; 1993; 
Polinsky and Shavell, 1992; 1994; 1999).  Thus, it is reasonable to assume that more 
serious offending is associated with longer sentences. In practice, the legal system makes 
a clear distinction between cases that have the potential for one or more years of 
incarceration in state prison, and cases that are eligible for less than one year of 
incarceration, to be served in local jails. The assumption made here is that the distinction 
in severity of punishment is reflected in both direct and indirect losses.   
 In these property crimes cases, the assumption is that direct losses will be entirely 
due to property loss, and not a function of injury, lost wages or other direct economic 
damages. However, the RAND data does not distinguish between property loss and other 
 148
 
economic losses, such as lost wages and medical bills, so this assumption cannot be 
tested.  The analytic strategy here is to use the RAND data that describes the relative 
losses between direct and indirect losses. Once that ratio is computed, the rate of indirect 
to direct losses becomes a weight in the analysis of NIBRS data. In order to do this, it is 
necessary to have substantial data about the relative indirect and direct losses. While a 
valid total loss is observable for all observations in the RAND data, only about 30 percent 
have valid values for both economic and non-economic losses (as described in Appendix 
A.2., additional values are calculable from other information in RAND). Overall, more 
than 5,500 observations were identified that record both direct and indirect losses. 
Among these cases, the ratio of indirect losses to direct losses is 0.7:1.
18
 Thus, the 
estimated losses from the property crimes with the potential for a prison sentence are the 
product of 1.7 and the direct property losses observed in NIBRS. 
Table 4.3. Price Estimates for Aggregated Part One Crimes, Propensity Score Models 
  
Crimes with Direct and Indirect Costs 
Crime Type 
 
Mean 90% 75% 
Median  25% 10% 
Arson (N=5,423 ) 
$16,979 $3,621 $1,096 
$850 $323 $170 
Extortion/ 
Blackmail (220) 
 
3,498 7,700 1,700 
170 0 0 
Burglary/ B&E 
(190,842) 
 4,444 5,279 2,210 782 222 12 
Motor Vehicle 
Theft (135,685) 
 15,175 39,100 17,000 6,800 2,550 41 
Counterfeiting/ 
Forgery (19,338) 
 8,208 1,870 459 34 0 0 
Swindle (29,451)  4,389 7,990 1,771 170 2 0 
Credit Card 
(21,384) 
 973 1,820 617 37 0 0 
                                                 
18
 In most of the published literature, the ratio of direct to indirect losses is about 1 to 1. Since a lower ratio 
of indirect to direct losses results in a smaller additional indirect component in the NIBRS data, this 
assumption appears to be relatively conservative. 
 149
 
Impersonation 
(19,817) 
 955 1,159 5 2 0 0 
Source: Each of the estimates is derived from the study cited. All estimates are presented in 2008 
dollars (Cohen (1988) is in 1985 dollars, Miller et al. (1996) are in 1993 dollars.  
 
Table 4.4 clearly shows the substantial skew that exists in the data. For two categories, 
the mean award is greater than 90 percent of awards, demonstrating that a very small 
number of cases have extreme awards. The mean award exceeds the seventy-fifth 
percentile awards in every category but motor vehicle theft. The median award is an 
order of magnitude smaller than the mean for most cases. It is also important to note that 
many cases result in $0 in harm to the victim.  
Estimating Losses in the Least Serious Property Crimes 
The losses reported in table 4.4 are the mean and median losses from the NIBRS data 
only, on less serious crimes. The assumption associated with these estimates is that there 
is no indirect loss from these crimes (and no direct losses other than property loss). To 
the extent that there are indirect losses, this will tend to underestimate the losses from 
these types of crime.  
Table 4.4. Estimates of Harms for Crimes with Property Losses Only, Plus Indirect Costs 
  Crime Only / Propensity Model / All Cases 
Crime Type  Mean Median 
Pocket-Picking (N=4,235) $408 $90 
Purse-Snatching (5,772) 
 
447 72 
Shoplifting (1,963)  459 60 
Theft from Building (125,141)  6,393 165 
Theft from Coin-Operated Machine (884)  532 140 
Theft of Motor Vehicle Parts (274,937)  408 210 
Theft from Motor Vehicle (274,937)  990 100 
All Other Larceny (367,978)  2,048 150 
 150
 
Welfare Fraud (95)  461 47 
Wire Fraud (2,003)  1,930 275 
Embezzlement (2,210)  9,781 1,633 
Stolen Property Offenses (7,155)  3,341 500 
Destruction/ Vandalism (460,629)  759 170 
Source: Analysis of data from the RAND Institute of Civil Justice, 12,918 cases from 1985-1999 
and 2000 NIBRS data. Frequency weights are applied to all analyses. All dollars are calculated 
as 2000 Dollars.  
 
Testing the Generalizability of the NIBRS Data  
The results in this section depend on the assumption that the NIBRS data that were 
matched to the RAND data are equivalent to the RAND data that do not.  The challenge 
in testing this assumption is that most of the candidate variables for comparison are 
different by construction?those cases that do not match RAND are different from those 
that did, and the lack of a difference is evidence of this difference. However, there is an 
opportunity to test the differences by comparing property loss data in NIBRS cases that 
did and did not match. Two types of crime are particularly amenable to this analysis: 
robberies and burglaries.  
Independent samples t-tests can compare the expected award for cases where the 
economic losses from a crime can be a priori determined to be property only and where 
estimates are available from both sources. A finding of no significant differences 
supports the approach here. There are a total of 256,000 burglaries for which a property 
loss is observable in NIBRS. The mean loss is $2,613 for those that match to the RAND 
data, and $1,587 for those that do not match, however the difference is not statistically 
significant (p=0.33). Property loss is observable in about 40,000 cases. The mean loss in 
 151
 
those cases that are observable in both datasets is $1,510 and the mean loss in those cases 
observable only in NIBRS is $1,221, which is statistically significant at p=0.09.  
 
Study Limitations 
This present study has several advantages of prior work in this field, and these are 
described in the next chapter. There are, however, several limitations to the present work. 
The limitations mainly fall across two issues: the representativeness of the data used in 
the analysis and the theoretical grounds for using jury awards to estimate case outcomes.  
Are the Results Representative of all Crimes? 
First, with respect to empirical matters of representativeness, it cannot be 
demonstrated that the present data are?or are not?representative of the typical criminal 
victim. Data used in this study rely on civil court data, which implicitly assumes that 
cases that make it to civil court are similar to all crimes. In the vast majority of serious 
crimes, there is no law suit.  For a case to proceed to a civil trial there must be a 
defendant ?either the perpetrator or a negligent third party?that has sufficient resources 
to incentivize a lawsuit.  Even in these instances, only a fraction of cases make it all the 
way to a jury trial.  Thus, it is reasonable to question whether these cases, that are 
unlikely to be representative of all cases in terms of the financial attributes of the 
defendant, are representative of the harms suffered by the average victim.  On the other 
hand, it may also be the case that the financial attributes of the defendant (or third-party) 
are orthogonal to the social cost of the victimization (conditional on injury and other 
observable characteristics), and to whether the offender is caught and prosecuted. 
 152
 
There are three specific reasons why the data may not be representative. First, it 
may be that the types of offenders and offenses observed in the jury data are not 
representative of all crime victims. To the extent possible, this study has relied on the 
variation in NIBRS to overcome this issue. The present study matches cross-combination 
of attributes in more than 70 percent of cases between the RAND data and the NIBRS 
data.  This approach of matching micro-level data to micro-level data has real advantages 
over prior work that has used population level prevalence as the means of generating 
weights. Nevertheless, it is certainly possible that the 30 percent of cases that could not 
be matched would lead to different results had they been included.  
Unfortunately, there is no obvious way to broadly test how the matched and 
unmatched NIBRS data differ.  Clearly, the two groups will be different on the main 
attributes of interest, since a lack of overlap on these attributes this is the reason why the 
two data sets could not be matched.  Since the two data sets cannot be matched, there is 
no way to compare mean differences in any measure of victim losses as there is no 
damage in NIBRS to compare to awarded or claimed losses in NIBRS. The one available 
data point for comparison ? comparing observed property losses in cases that do and do 
not match to RAND data?show small and significant differences in robbery and larger, 
but non-significant differences in burglary. This suggests that the approach taken here 
may tend to overestimate losses, perhaps by about 20%.  
The second empirical issue is whether the cases in RAND are more (or less) 
serious within each crime strata. That is, it is possible that two observations with the 
same age, gender and injury may well have unobservable attributes that clearly 
distinguish them.  The criticism is that the cases that lead to a civil verdict are likely to be 
 153
 
more serious than those that do not. The way to overcome this limitation is to include 
more measures of victim and case attributes. This study does make some advances in this 
area, as the number of age categories is increased from three to five, and the number of 
injuries from five to nine. Nevertheless, the study relied on broad injury categories due to 
limitations in the NIBRS data.   
The main threat from this issue is that there may be differences within crime 
categories. That is, it may be that the average rape that matches to RAND is different 
from the average rape that does not. The property loss comparison is instructive, but more 
so for those cases where property loss and indirect losses have relatively equal effect on 
the total award. For cases, like rape and homicide, where the indirect losses would be 
expected to dominate, this comparison is less instructive. Table 4.5 displays the 
percentage of NIBRS cases that match to RAND and the percentage that do not (for those 
crimes that relied wholly or in part on RAND award data to generate the estimate. The 
main finding of this table is that those crimes that have the largest indirect to direct ratio 
are least well matched.  
 
Table 4.5. Percentage of Cases Matched 
 
Percentage of NIBRS cases that match a RAND record 
Crime Type 
Match 
No Match Percentage Matching 
Murder/Non-negligent 
Manslaughter  
818 
1,656 33.1% 
All Rape 
21,113 
29,479 41.7 
   Forcible Rape 11,486 10,241 52.9 
   Forcible Sodomy 1,456 2,757 34.6 
   Sex. Assault w/Object 1,100 1,495 42.4 
   Forcible Fondling 7,071 14,986 32.1 
 154
 
Robbery 31,524 14,244 68.9 
Assault 418,256 204,828 67.1 
   Aggravated Assault 76,114 44,828 62.9 
   Simple Assault 342,201 159,903 68.2 
Burglary 229,486 65,421 78.0 
Motor Vehicle Theft 142,111 36,803 72.1 
Counterfeiting/Forgery 19,338 6,766 79.4 
Swindle 29,451 9,882 74.9 
Credit Card/ATM 21,384 5,718 78.9 
Impersonation 19,817 5,311 78.9 
Total 1,083,282 428,914 71.6 
Source: NIBRS data with harms interpolated from RAND data. 
 
In general, Table 4.5 suggests that other than homicide and rape, the percentage of 
NIBRS cases that match to RAND is close to the overall match rate of 70 percent. The 
lack of a match on homicide and rape suggests much greater caution should be exercised 
in using these numbers than the other numbers in this study. Clearly, there is a greater 
likelihood given this lower match rate that the losses from these crimes are not well 
modeled using this approach. For instance, the NIBRS data suggest that few rape victims 
have a serious injury (slightly more than 70 percent record no injury, and the 
overwhelming majority of the rest report minor injuries) and thus these records will 
match to jury awards for no injury or minor injuries. However, it is reasonable to assume 
that the indirect harms from rape with no injury are far larger than the indirect harms 
from other crimes with no injury. Chapter five discusses the implication for using these 
numbers given that limitation. 
This study did attempt to control for differences between cases within the RAND 
data where there was (or was not) an obvious indicator of an underlying criminal event. 
Prior studies had limited sample sizes due to a focus on only those cases where a criminal 
 155
 
event could clearly be distinguished, and that was generally limited to sexual assault and 
assault.  The limitations of this are clear?that the studies only result in price estimates 
for a few crimes, and also that within the included categories cases could be missed if a 
crime occurred, but the claimant sought relief based on a claim of something in addition 
to the intentional tort (such as negligence in the case of a motel owner that did provide 
secure rooms thus leading to a sexual assault).  This study uses a propensity score model 
to re-weight observations to account for potential differences between cases. However, it 
is certainly possible than there remains unobserved heterogeneity related to damage 
awards.  
In general, the propensity score generalizes the relationship between losses and 
injuries to more cases in RAND to allow more cases in RAND to be used in the analysis. 
Subsequently, this supports the interpolation of RAND data on to more cases in NIBRS. 
The assumption, which cannot be tested, is that the generalizability of the entire study is 
improved if a larger proportion of NIBRS data are used in the analysis. However, if the 
NIBRS cases that match to RAND are different from the NIBRS cases that do not (even 
when the number of NIBRS cases is expanded) than this adjustment does not improve 
generalizability. As noted, this can be tested to some extent by the comparison of 
property losses in burglary and robbery for cases in NIBRS that do, and do not, match to 
RAND. If, however, the cases that match to RAND are similar in property losses within 
crime categories, but different in other attributes (such as indirect damages) than this 
correction will not improve generalizability. As noted above, the types of cases that are 
least likely to match to NIBRS (homicide and rape) appear to be most dissimilar to the 
RAND cases. 
 156
 
Limitations of the RAND Data 
 The RAND data have several other limitations that should be noted. One key 
limitation of the RAND data is that it does not include some key variables, such as race. 
African-Americans are over-represented as arrestees and as victims relative to the 
proportion of African-Americans in the population.  However, African-Americans may 
be under-represented in the RAND data and thus the estimated harms may or may not be 
representative of this population.  
 As noted, the RAND data does not reflect data from all fifty states. While the data 
includes jurisdictions that contain about 40 percent of the US population, the distribution 
of awards may be higher in more urban areas than non-urban areas. The awards may also 
be skewed by the relative lack of observations in the Deep South (although Texas and 
Missouri are represented).  To the extent that awards are different in the jurisdictions 
included in the RAND data than in the rest of the United States, the results will not be 
representative.  In addition, because the data are not drawn from a random sample of US 
cities, other demographic factors, such as age and gender, may not be representative of all 
victims of crime. Since these variables are used to link data across the two datasets, it is 
difficult to observe the effects of the limited geographic coverage. However, since a 
single crime is likely to include events from a variety of different city sizes, some 
investigation of how awards on the interpolated data set vary by population size may 
show the extent to which different areas are associated with differential award patterns.  
 To test for these differences, I ran t-tests comparing the average award by age and 
gender of the victim. Differences are observed in awards as a function of age and gender. 
On average, women receive less ($157,000) than men ($183,590) and the difference is 
 157
 
highly significant (p<0.001). A bivariate regression finds that each additional year of age 
is associated with about $700 dollars in harms (p<0.001). To account for the possibility 
that awards are non-linear in age (that older victims have smaller awards), a squared term 
is added to the model. This yields a much larger age effect, where each additional year of 
age is associated with $2,000 in expected average award.  However, it is difficult to 
interpret these findings since variation in awards by age is expected (due to differences in 
the types of harm from crime by age). Differences in gender are also difficult to interpret 
since it is possible that women may experience less serious injuries on average.  
 Differences in harms as a function of the population of a jurisdiction are more 
indicative of a lack of representativeness in the RAND data. In expectation, for example, 
the victim of a robbery in a large urban area may have larger losses due to the higher cost 
of living in urban areas, and thus more expensive property to steal. However, a t-test 
comparing awards in jurisdictions with populations over 100,000 ($230,000) to 
jurisdictions under 100,000 in population (($127,000) shows significant differences in 
average award (p<0.001).  
 Combining these results in a linear regression (with a log link to account for 
award skew) suggests that population size explains more of the award than would be 
expected as a function of differences in cost of living. When logged award is regressed on 
population size there is an additional $31,000 in average award for every additional 
100,000 in population (p<0.001). When other independent variables are added to the 
model (age of victim (and age squared), victim gender, type of injury) the effect of 
population persists. In fact, population size does not appear to co-vary with the other 
independent variables, as an additional 100,000 in population is associated with a 
 158
 
$30,772 increase in award on average. Finally, it should be noted that most of the gender 
effect on average award appears to be due to co-variation with injury and population size. 
While women average $26,000 less in average award, controlling for injury and other 
factors reduces that difference to slightly less than $10,000 (p<0.001).  
Representativeness of NIBRS 
The choice to use NIBRS data instead of NCVS data means that the criminal data 
are themselves non-representative. I believe that the advantages of the NIBRS data?a 
more precise estimate of property loss, improved sampling of the most serious cases, and 
inclusion of important populations excluded in NCVS?outweighed the cost in terms of 
lost representation. Nevertheless, this may have introduced another source of error. 
Three other limitations of the study are addressed below. First, it should be noted 
that cases that result in a civil award may not yield an unbiased estimate of all cases with 
criminal liability. While the most obvious source of bias?that weaker claims are more 
likely to be settled out of court?suggests that civil jury awards overestimate the true 
harms to victims of crimes, it is more likely that the risk tolerance of the parties to a 
claim rather than the size or strength of the case predict whether a case proceeds to a jury 
trial, and thus the direction of the bias is ambiguous. It may also be true that cases settled 
by a judge rather than a jury may tend to result in somewhat smaller verdicts. However, 
given that the RAND data includes only cases resulting in a jury trial, this bias cannot be 
tested empirically. 
 159
 
Social Costs 
With respect to theoretical issues, there remains a criticism of the jury award 
approach on the grounds that the aggregated costs to society will yield a different value 
than would a social cost calculation.  Clearly, the jury award method does not yield an ex 
ante estimate of willingness to pay, and thus is likely to result in different estimates of 
social cost.  The approach is better than one that relies on cost of illness, for several 
reasons. First, jury awards can be argued to be an objective, third party evaluation of the 
sum of the harms suffered by a particular victim. Cost of illness, by contrast, is merely a 
schedule of costs associated with an average injury that resembles the victim in the case 
under study. In addition, by relying solely on jury awards, and not a blended cost of 
illness and jury award estimate, far fewer assumptions are required, which is helpful from 
a theoretical perspective, since it limits the number of ways in which estimates are 
generated.  
This paper does not argue that the final prices approximate the costs of illness that 
would have been generated from an ex ante study. However, in practice it is difficult to 
see how a study could be performed that captures the ex ante price of discrete crimes. 
The research literature includes several contingent valuation studies that develop 
estimates of the social cost of broad categories of crime. These authors correctly note that 
from a policymaking perspective, social cost is the right unit of analysis. For broad policy 
questions, such as the appropriate level of incarceration or appropriate number of police 
officers, a robust measure of social cost will best inform debate. 
However, at the programmatic level, those estimates may have less value. A 
question about the social cost of gun violence is likely to elicit a more informed estimate 
 160
 
than the cost of drug-related offending. And for particular programs, broad measures of 
social cost are likely unattainable. For instance, to understand whether a program 
designed to rehabilitate prisoners returning to a handful of neighborhoods in a single city 
is cost-effective, it is difficult to specify a contingent valuation question that directly 
informs that analysis. The same issues relate to a specialized court for substance abusing 
defendants or a sanctioning scheme as an alternative to incarceration. For these types of 
programs, precise estimates of the benefits in the form of reductions in victim harm are 
an asset to evaluation.  
Conclusion 
This study develops estimates of the distribution of prices for criminal victimization. 
The mean estimates are higher than much of the published literature, while the medians 
are in line with the lowest estimates due to the skew in the price distribution. Table 4.5 
describes the comparison of my estimated means to extant estimates and Table 4.6 
describes the comparison of my estimated medians to extant estimates.  
 161
 
 
Table 4.5. Comparison of New Price Estimates to Extant Estimates (mean) 
  
Crimes with Direct and Indirect Costs 
Jury Award Literature C.V. Roman 
Crime Type 
 
Cohen 1988
Miller, 
Cohen 1996
Rajkumar 
& French 
1997 
French & 
McColliste
r 2008 
Cohen, et 
al. 2004 
Propensity 
Model 
Murder/Non-negligent 
Manslaughter  
$2,842,242 $4,178,096 $7,772,054 $9,322,054 $10,825,622 $1,564,186
Rape 
 
102,218 129,629 74,271 219,566 264,502 156,295 
Robbery  25,200 19,370 32,040 46,484 258,922 299,573 
Assault 24,067 22,350 32,040 122,716 78,123 145,103 
Burglary  2,745 2,235 1,909 4,362 27,901 5,556 
Motor Vehicle Theft  6,257 5,960 1,666 9,141 5,412 18,973 
Theft 362 551 1,067 1,475 819 2,655 
Source: Each of the estimates is derived from the study cited. All estimates are presented in 2008 dollars 
(Cohen (1988) are estimated in 1985 dollars, Miller et al. (1996) are estimated in 1993 dollars). The rape 
data in Roman are a weighted average of forcible rape, forcible sodomy and sexual assault with an object.  
The assault data from the Roman study includes a weighted average of aggravated assault and simple 
assault, assault data from other studies may include aggravated or attempted assaults. The French and 
McCollister study presents estimates for aggravated assault only.  The larceny/theft value in the Roman 
study is the weighted average mean of NIBRS categories: Theft From Building, Theft From Coin-
Operated Machine or Device, Theft From Motor Vehicle, Theft of Motor Vehicle Parts/Accessories, All 
Other Larceny. 
 
 
 162
 
 
Table 4.6. Comparison of New Price Estimates to Extant Estimates (median) 
  
Crimes with Direct and Indirect Costs 
Jury Award Literature C.V. Roman 
Crime Type 
 
Cohen 1988
Miller, 
Cohen 1996
Rajkumar 
& French 
1997 
French & 
McColliste
r 2008 
Cohen, et 
al. 2004 
Propensity 
Model 
Murder/Non-negligent 
Manslaughter  
$2,842,242 $4,178,096 $7,772,054 $9,322,054 $10,825,622 $1,380,246
Rape 
 
102,218 129,629 74,271 219,566 264,502 18,908 
Robbery  25,200 19,370 32,040 46,484 258,922 88,915 
Assault 24,067 22,350 32,040 122,716 78,123 155,270 
Burglary  2,745 2,235 1,909 4,362 27,901 814 
Motor Vehicle Theft  6,257 5,960 1,666 9,141 5,412 6,174 
Theft 362 551 1,067 1,475 819 192 
Source: Each of the estimates is derived from the study cited. All estimates are presented in 2008 dollars 
(Cohen (1988) are estimated in 1985 dollars, Miller et al. (1996) are estimated in 1993 dollars). The rape 
data in Roman are a weighted average of forcible rape, forcible sodomy and sexual assault with an object.  
The assault data from the Roman study includes a weighted average of aggravated assault and simple 
assault, assault data from other studies may include aggravated or attempted assaults. The French and 
McCollister study presents estimates for aggravated assault only.  The larceny/theft value in the Roman 
study is the weighted average mean of NIBRS categories: Theft From Building, Theft From Coin-
Operated Machine or Device, Theft From Motor Vehicle, Theft of Motor Vehicle Parts/Accessories, All 
Other Larceny. 
 
Some of the differences in the present estimate are due to definitional issues. For 
instance, an assault in other studies may refer only to a simple assault, whereas in the 
present study, the assault price is an average weighted by the prevalence of both simple 
and aggravated assault.  With respect to theft, this is likely the cause of the difference. 
This study includes many thefts from businesses, which includes relatively larger harms 
than other types of theft.  
This study produces a lower homicide estimate than appears in prior research. Most 
prior studies rely on an estimate of the statistical value of human life, rather than a direct 
estimate, which is how the homicide is estimated in this study. As discussed in Chapter 3, 
 163
 
homicide is a particularly difficult crime type to estimate. Prior studies have used the 
statistical value of a human life and either applied that estimate to all homicides, or used 
the estimate as a weight to adjust for risk of death associated with other crimes (generally 
because homicide data were unavailable). However, that strategy assumes no variation in 
the costs associated with homicide which may (or may not) be true from a social welfare 
perspective.  While the approach used in this study does identify substantial variation in 
the costs of homicide, a substantial weakness of the approach with respect to homicide 
remains. That is, unlike other categories of crime, the victim is not being compensated by 
the jury, and thus the estimate is not an ex post proxy for willingness to accept. Thus, for 
homicide, I replace the number generated in this estimate for the standard approach to 
valuing homicide ? using the value of a statistical life from the extant literature. 
The other estimate generated here that is inconsistent with prior approaches is the 
estimate for the price of rape. While the mean value for rape is in line with prior 
estimates, rape has a lower price in this study than robbery, which reverses the usual 
ordering from other studies. In terms of injury, the profiles for rape and robbery look very 
similar, as about 70 percent of rape victims experience no injury or an apparently minor 
injury. Severe lacerations, broken bones, and other internal injuries are reported more 
commonly in robbery cases than in rape cases, and as shown in Chapter 4, these kinds of 
injuries are associated with much larger awards. This difference in injuries leads to the 
higher price for robbery. It should be noted that the difference between robbery and rape 
exists in both the means reported above and the medians (about $100,000 for robberies 
compared to about $20,000 in rape cases).  
 164
 
 As discussed in the limitations section, less than half of all NIBRS observations 
for rape matched to a RAND subgroup. Thus, it appears that the jury approach, using the 
current dataset, may not be appropriate to estimate the price of rape. However, even if the 
data had matched at a higher rate, it is still likely that the estimate that was generated 
would be unsatisfactory. That is, the main limitation to using the jury compensation 
method is that much of the harm of rape is psychological. The empirical relationship 
between direct losses and indirect losses is much different for a rape victim than for 
victims of other crimes. Overall, direct and indirect awards are relatively equal. In the 
small number of cases that could be affirmatively coded as a rape, the mean jury award in 
the RAND data is about $1.3M, which is almost entirely an award for indirect damages. 
Thus, I would propose using extant estimates of jury awards for rape from studies that 
gathered relatively large numbers of rape cases (see Cohen and Miller 1999). However, 
the problems with these past awards are serious, and further investigation of this question 
is appropriate. In sum, Table 4.7 presents the final estimates for awards in all categories.  
 165
 
  
Table 4.7. Price Estimates for Crimes  
  
Crimes with Direct and Indirect Costs 
Crime Type 
 
Mean 90% 75% 
Median  25% 10% 
Murder  
$6,900,000 -- -- 
-- -- -- 
Rape 
 
272,121 -- -- 
-- -- -- 
Robbery  279.085 $605,225 $334,515 $88,915 $68,326 $18,908 
Assault 134,770 334,515 155,270 66,644 13,285 611 
  Agg. Assault  283,794 569,701 294,335 89,815 27,956 1,900 
  Simple Assault  101,623 238,396 87,000 59,083 35,239 600 
Arson  
$16,979 $3,621 $1,096 
$850 $323 $170 
Extortion/ Blackmail  
3,498 7,700 1,700 
170 0 0 
Burglary/ B&E  
4,444 5,279 2,210 782 222 12 
Motor Vehicle Theft  15,175 39,100 17,000 6,800 2,550 41 
Counterfeiting/ 
Forgery  
8,208 1,870 459 34 0 0 
Swindle 4,389 7,990 1,771 170 2 0 
Credit Card  973 1,820 617 37 0 0 
Impersonation 955 1,159 5 2 0 0 
Source: Each of the estimates is derived from the study cited. All estimates are presented in 2008 
dollars (Cohen (1988) is in 1985 dollars, Miller et al. (1996) are in 1993 dollars.  
 166
 
Chapter Five: Implications for Research and Policy 
 
 
 There is a substantial body of literature that has emerged over the last two decades 
that attempts to value the price of criminal victimization. The price estimates developed 
in this paper and in the extant literature have three important applications. First, they 
inform cost-benefit analysis of new policies and programs by creating a standardized 
metric with which to evaluate outcomes.  Second, because the costs of crime vary 
between crimes, these estimates can inform the optimal allocation of criminal justice 
resources in crime control, where criminal justice system stakeholders must choose 
among a range of anti-crime strategies with heterogeneous impact on types of crime. 
Third, they provide new information that can be used to evaluate the effectiveness of 
crime control efforts over time.  
While this paper expands the number of crime categories with an estimate from less 
than a dozen to more than 30, it is fair to ask whether the estimates are credible. While it 
is difficult to argue that price estimates are not important in developing evidence-based 
policies, it is fair to question whether these price estimates, or any price estimates, can 
credibly inform these discussions. Other approaches, such as contingent valuation, clearly 
result in estimates that are closer to their theoretical economic foundations.  
However, it is far from certain that contingent valuation studies can be developed 
that create prices for particular crimes, which is crucial to evaluating all but the broadest 
of social policies. In order to evaluate programs with discrete outcomes, such as 
desistance from domestic violence, or drug crimes, or serious person crimes, prices must 
 167
 
be available to describe the benefits of crime reductions. Since the risks of victimization 
are so small for serious crimes, a reasonable person is unlikely to be able to make an 
informed judgment about their ex ante willingness to pay. Suppose it is shown that using 
DNA to solve burglaries doubles the number of burglary arrests. Suppose that the 
program could be taken to scale and applied everywhere in the United States. As a result, 
the real (average) risk of having a household burglarized is reduced from about 2 percent 
to about 1 percent for any American household. Is it plausible that a reasonable person 
could make an informed statement about their willingness to pay for that reduction? 
If contingent valuation techniques cannot generate these estimates, the next best 
alternative appears to be a jury compensation approach. Although the theoretical 
foundation is shakier?the method only approximates ex ante willingness to accept?the 
technique has been shown to produce estimates that scholars have been willing to use in a 
wide variety of law and economics research. As noted earlier, the most cited study using 
this approach (Cohen, Miller and Wiersma, 1996) has been cited more often than the 
most famous study using those estimates (Levitt, 1996).   
Precedent, however, is probably a necessary, but not sufficient, justification for 
using these estimates. Since there is no obvious way to externally validate these 
estimates, perhaps the best strategy for evaluating their strength is to consider each of the 
assumptions that underlay the estimates. Before doing so, it is worthwhile to separate out 
those estimates that have the most serious empirical problems?homicide and rape?and 
consider how well the other estimates withstand close inspection. 
For the least serious property crimes that makes use of only NIBRS data, only two 
assumptions are required. First, the study assumes that individuals accurately report 
 168
 
losses to police. With respect to the reporting accuracy in NIBRS, I can find no prior 
research that validates the accuracy of NIIBRS property loss data.  However, there are 
some reasons to believe it is more accurate than survey data. First, the report tends to 
occur close to the time of the victimization, and thus there should be fewer re-call 
problems. Second, in many cases, the account given to the police is likely to be validated, 
which would occur if losses are insured and a claim is filed. Victims may also have 
incentive to respond truthfully, since accuracy of claims may assist them in getting items 
back if they are recovered by the police, while misstatements might reduce that chance. 
Second, the study assumes that the ten states in NIBRS can be generalized to the entire 
country. Since NIBRS only includes ten states that exclude most major metropolitan 
areas and likely have lower costs of living, the estimates are probably not perfectly 
representative of all victim losses. However, to the extent that there is bias, it is probably 
in the direction of under-estimating losses, and thus these data produce a conservative 
estimate.  
There are several additional assumptions that are required for the estimates of the 
more serious property crimes where price estimates depend on both NIBRS and RAND 
data. First, it is assumed that juries accurately estimate indirect losses as a function of 
direct losses (the serious person crimes requires an additional assumption that they 
accurately estimate claims, as is discussed below). With respect to the accuracy of the 
civil jury, the research in Chapter 2 overwhelmingly suggests that on average, juries do 
about as well as experts and judges in evaluating claims. Second, the study assumes that 
the awards from RAND can be generalized to all crimes.  This assumption rests on the 
principle that juries evaluate claims based on victim harms, and not other extra-legal case 
 169
 
attributes. The extant literature in Chapter 3 supports this claim. In addition, the 
comparison of property losses of those NIBRS cases that did and did not match to RAND 
suggests that if there is bias, it is 20 percent or less. Finally, this approach assumes that 
there should be an indirect loss associated with crimes that do not result in physical harm. 
Again, there is no way to test this assumption, but the assumption that people suffer harm 
from  the loss of property in addition to the value of that property appears to be a small 
one.  
Two assumptions are required for the estimation of serious person crimes. The first 
assumption is that juries are accurate estimators of losses in civil cases and that awards 
reflect the harms suffered by victims. Again, prior research in this area suggests that 
juries do a relatively good job of evaluating claims, and the civil jury system has 
remained a relatively stable pillar of the justice system for decades. Second, the study 
assumes that the awards to compensate for harms from an injury will not vary if the harm 
results from a crime as opposed to a non-criminal incident. This is a relatively strong 
assumption that does not hold, as reflected by the real differences in average awards 
between the two types of cases. However, the propensity score model appears to a good 
job balancing cases on observable attributes related to assignment of a case as a crime or 
not crime case. Finally, the study assumes that the omission of important data about the 
crime (such as victim race) and the lack of geographic overlap between the two datasets 
will not bias results. A test of the effect of population size on awards suggests that awards 
increase relatively quickly as city size increases. However, it cannot be determined 
whether that is a natural phenomenon reflecting differences in cost of living, severity of 
 170
 
criminal incidents and risk tolerance, or whether the study is overestimating harms in 
large cities (or underestimating harms in rural areas).  
Rape and Homicide 
 Ultimately, the study did not generate estimates for rape and homicide. AS 
discussed in chapter 4, the theoretical grounds for estimating homicide prices seem too 
limited to produce a credible estimate. Since the homicide victim cannot be made whole 
in any way, the study cannot be said to approximate the ex ante willingness to accept 
price of the victims. While it is unclear whether the jury verdict approach can plausibly 
be used to estimate homicide prices, the estimates generated here do show substantial 
variation in the price of homicide. This suggests additional research in the field, using 
contingent valuation approaches, to estimate confidence bounds on homicide prices. This 
would answer the question of whether social costs also vary by the type of victim, or 
whether society-level outcomes are unaffected by whom the victim is, just whether there 
was a homicide victim.  
 With respect to rape, this study also suggests that using jury awards to indirectly 
estimate rape prices may also not be an effective strategy. The main limitation is that the 
variables used to interpolate the jury data onto the crime data?victim injuries?do not 
adequately capture the extent of the harm suffered by victims of rape. The alternative 
would be to use jury data alone in cases of rape to estimate prices. The data used in this 
study did not contain enough observations to allow for this, but other research has 
successfully gathered sufficient observations (see Cohen and Miller, 1999 but note that 
there are unresolved statistical problems in this study).  
 171
 
 Thus, in conclusion, the estimates generated here appear to improve on existing 
price data.  Though the limitations of this approach are real, these estimates rely on far 
fewer assumptions than past research. The assumptions that are subject to criticism are 
fewer in number than in past research, and the ones that remain have been heavily vetted 
in the scholarly literature. None of the assumptions alone appear to be so strong as to call 
into question the entire endeavor. Moreover, the weight of the assumptions does not 
appear to fall so heavily toward over- or under-estimation that the entire approach should 
be abandoned. Thus, the weight of the evidence supports the use of price estimates 
derived from civil jury awards.  
Implications for Future Research 
 While this study makes several improvements on past studies using civil jury 
data, there is room for substantial improvement. In particular, these estimates could be 
improved if future studies of civil jury behavior explicitly coded cases in terms of 
whether there were criminal events that lead to the victim being harmed, and what type of 
event occurred. As noted, it is very likely that there are a substantial number of criminal 
incidents in the RAND data that cannot be affirmatively coded as a crime that did result 
from a criminal incident. In addition, coding additional information about both the victim 
(race) and the defendant (was the defendant the alleged perpetrator; what was the 
victim?s age, race, association with the victim, etc.,) would improve future studies. 
Finally, additional information about the timing and location of the criminal event (rather 
than of the timing and location of the civil proceeding) would improve the study.  More 
information about the type of crime in particular would substantially improve this line of 
research. 
 172
 
 
Implications of the Research 
The implications for research are relatively clear, but the implications for policy and 
practice are not as obvious. The clearest application of these data is for use in cost-benefit 
analyses of criminal justice policies and programs. Typically, the main effect of a 
criminal justice policy will be to change the rate of offending within the target 
population. Although there may be spillover effects, the main effect is to change the 
number and/or type of the distribution of criminal victimizations. Thus, the ?benefits? of 
the policy can be measured as that change, and those effects can be translated into a 
consistent metric (dollars) using the price data from this study.  
The strength of the approach taken here is that it develops estimates of the price of 
crime that can be conditional on a set of observable attributes. Rather than simply 
applying a single point estimate to a broad crime type, the whole distribution can be used 
to relate prices of crime to effects of a policy or program. Where a policy or program 
targets only a sub-group of all victims, an analogous sample of the NIBRS population, 
with prices, can be selected from these data. Thus, much more precise costs and benefits 
of policies and programs can be estimated. 
The implications for policy and practice are less clear. Rigorous cost-benefit 
analysis is a necessary but not sufficient condition for improved decision-making. That is, 
careful cost-benefit analysis will provide policymakers with better information than exists 
without CBA. But unless the information is coupled both with a willingness to make 
decisions based on that evidence, and with a finding that is actionable, there is scant 
reason to believe that better policies will result.  
 173
 
The largest barrier to effective policymaking resulting from careful cost-benefit 
studies is that the information is not actionable. That is, CBA enumerates the winners and 
losers from a policy or program, and thus whether the policy satisfies some normative 
standard, such as Pareto optimality or the Kaldor-Hicks condition. However, if the 
winners cannot somehow compensate the losers, the policy is unlikely to be 
implemented. Given that most governments operate with very constrained resources, it is 
reasonable to presume that most budgeting is a zero-sum game. In order for a new policy 
or program to be funded, those funds must be taken from some other area. This works 
quite well if the policy benefits the agency that funds the project. If the agency funding 
the project does not benefit enough to cover the losses, as is more commonly the case, the 
policy faces large barriers to implementation. 
 Consider the case of a proposed diversion program for drug-involved offenders. 
The program is designed to identify drug dependent arrestees and treat them in lieu of 
incarceration. The diversion program provides judicial oversight and supervision to those 
offenders while they complete a course of drug treatment, and successful participants 
have their charges dismissed. The program is significantly more expensive than business 
as usual case processing and the courts pay for the program. The main beneficiary of the 
program is the correctional system, as successful participants will not have to use prison 
resources since they will not be incarcerated. In addition, they may commit fewer crimes 
thus saving private citizens money (since fewer will be victimized) and saving the 
criminal justice system money as well, since there will be fewer new crimes to 
investigate and prosecute and fewer offenders to incarcerate.  
 174
 
 It seems natural for the corrections system (the winner from a cost-benefit 
perspective) to compensate the court system (the loser from the cost-benefit perspective).  
The court incurs new costs to set up and run the diversion program, and the corrections 
system saves funds as a result. However, in reality, most of the cost savings from the 
program goes outside the criminal justice system. Since the demand for prison beds is far 
greater than the supply, prison beds tend to be filled. If one were to imagine a queue of 
offenders who were legally eligible for a prison bed based on the crimes they had 
committed (or violations of community supervision), that queue would likely be several 
times as big as the number of available. Even a large-scale diversion program would be 
unlikely to remove enough eligible offenders to actually reduce the number of prison 
beds used.  
A standard approach to budgeting is to fund only those programs that have cost 
offsets. The approach, known as pay as you go in the United States federal government is 
widely used de facto or de jure to guide governmental decision making around the world. 
In the case of the diversion program described above, the winner (prisons) cannot 
reasonably compensate the courts for the cost of the diversion program, since the 
diversion program does not actually free resources for use elsewhere. Such a situation is 
more the rule than the exception with respect to new policies and programs in the 
criminal justice system. 
It is important to note that an essential ingredient is missing from this policy 
cookbook. The real winner from this hypothetical diversion program?the public?is not 
included in this calculus. Generally, budget decisions are made within systems, and 
external concerns are excluded from decision-making. Thus, the most efficient solution to 
 175
 
this problem, asking the public to pay more to support a program for which they are the 
primary beneficiary, is not considered. 
In order for CBA results to be both necessary and sufficient for decision-making, the 
results must include some accounting for how resources can be more efficiently 
employed. If the public is not included in the budget calculus for the diversion program, 
it seems unlikely that such a program will ever include more than a small number of 
participants. In fact, this is exactly what has happened in the United States with respect to 
drug courts.  Drug courts are diversion programs for drug-involved arrestees that function 
much like the hypothetical diversion program described above. Although the first courts 
appeared in the United States, they have become increasingly prevalent around the world, 
particularly in the United Kingdom. 
Most research suggests that drug courts in the U.S. are quite cost-beneficial. A 
substantial body of research estimates that there are between $2.25 and $2.75 in benefits 
for each dollar of new costs (Aos, et al., 2002; Bhati, Roman and Chalfin, 2008). The 
costs and benefits of U.S. drug courts are distributed in the same way as described above, 
where the court systems pays a substantial additional amount over business as usual case 
processing (on average $4,000 to $5,000 more per case). Much of the benefit of drug 
courts is in the form of reductions in victimization of private citizens, perhaps as much as 
70% of all benefits (Bhati et al., 2008).  
In the United States, start up funds for new drug courts mainly come from the 
federal government, and this funding lasts only two or three years.  To sustain drug court 
operations, local funding is used, and this rarely includes new taxes. Thus, although the 
public wins they are not asked to offset court costs. And, because prison see only a minor 
 176
 
benefit, in the zero-sum game of criminal justice system budgeting there is no source to 
off-set the courts cost. And as a result, the programs would not be expected to grow. By 
our estimates, fewer than 5% of all individuals who arrested each year in the United 
States and who are at risk of drug abuse or dependence enter a drug court (Bhati, et al., 
2008). There is little reason to believe this will change.  
This phenomenon is not unique to drug courts. The High Scope/Perry Pre-school 
experiment was a random controlled study of a preschool program in Ypsilanti, Michigan 
beginning in the fall of 1962. Subjects were followed from age 3 to age 41 and 
subsequent evaluations found improvements in ?children?s readiness for school and? 
subsequent educational success, economic success in early adulthood, and reduced 
number of criminal arrests? (Schweinhart, 2003:2). The program is often credited with 
facilitating the development of Head Start, an initiative by the U.S. federal government to 
promote early education for three and four year-olds. Despite the enormous interest in 
Head Start, early education remains relatively uncommon. Schweinhart, the author of 
many of the Perry preschool studies wrote in 2003 (more than 40 years after Perry began) 
that, ?[t]he continuing challenge is to take such programs to scale so that all preschool 
programs for young children living in poverty? are exposed to the positive effects of the 
program (Schweinhart, 2002:2). 
One reason that the Perry Preschool model was not adapted more widely was the 
same diffusion of benefits seen in the drug court model. That is, Schweinhart estimates 
that Perry Program yielded more than seven dollars in benefits for every dollar in cost. 
While the costs were paid by the schools system, most of the benefit went to private 
citizens. More than 65 percent of the benefits are from a reduction in the number of crime 
 177
 
committed against private citizens. The rest of the savings went to a variety of 
governmental agencies.  Fourteen percent accrued to justice agencies, ten percent to the 
government at large in the form of new taxes, and three percent in welfare tax savings. 
Only seven percent of the benefit of Perry Preschool was returned to the educational 
system (mainly due to reductions in the need for special education services). 
The important insight from the Perry Preschool evaluation is that the choice of the 
lens through which results are examined matters enormously. The usual approach to 
budgeting is to first identify offsets within the same budget. In the case of Perry 
Preschool, the costs of the program exceed the benefits within the educational system by 
more than two to one (and probably even more so since the benefits of reduced special 
education may occur over years).  Thus, through that lens, Perry Preschool is not worth 
funding. Across all governmental agencies, the benefits exceed the costs by more than 
two to one, but the costs of moving funds from one agency to another may exceed the 
benefits. Only viewed through a lens of net social welfare is Perry Preschool a clear 
winner worth funding.    
 178
 
Appendix A.1  
 
Recovering Missing Ratio?s of Economic to Non-economic values 
As shown in Table 2.1, total awards were available for 13,170 records in the RAND data. 
Complete records with both economic and non-economic damages initially were only 
available for 3,827 records. For the remaining 9,343 records, these missing values can be 
either imputed for all observations, or calculated from observed values for some and 
imputed for others.  Cohen and Miller (1999) use a regression analysis where they regress 
total award on economic award to recover missing values for non-economic award. 
However, this assumes that the data are missing completely at random (MCAR) and are 
thus validly observed from other observations. Binary tests for differences suggest that 
the cases where no data are missing are different from the cases where data are missing 
across a wide range of indicators. An alternative would be to specify a model that 
predicts the ratio of non-economic to economic damages. Since the ultimate use of these 
data will be to create a ratio of non-economic to economic damages to weight economic 
costs in NIBRS, imputing such a ratio does not appear to contribute much new 
information to the analysis.  
Thus, values for missing columns can be directly calculated for some records. In 269 
records there are values for economic awards, but no corresponding values for non-
economic awards. Where the economic award was equal to the total awards, the value for 
non-economic awards was calculated as zero. The 61 cases where the values did not 
match, the remainder of the difference between total award and economic award was 
allocated to the non-economic variable. Similarly, in 1,030 records there are values for 
 179
 
non-economic awards, but no corresponding values for economic awards. For the 855 
cases where non-economic award was equal to the total awards, the value for non-
economic awards was calculated as zero.  The 173 cases where the values did not match, 
the remainder of the difference between total award and non-economic award was 
allocated to the economic variable. 
Table A.1.  
Dependent Variable Missing Values.  
Description Total Award Economic Award Non-Economic Award Unspecified  Percent Matching  Dropped 
Complete Data 3,827 3,827 3,827 0  100%  0 
Only Economic (no unspecified 
values) 
269 269 269 0  77%  0 
Only Non-Economic (no unspecified 
values) 
1,030 1,030 1,030 0  83%  0 
Economic and Unspecified 148 148 111 148  75%  37 
Non-Economic and Unspecified 134 95 134 134  71%  39 
Economic, Non-Economic, 
Unspecified 
170 170 170 170  --  170 
None 3 0 0 0  0%  3 
Total Award = $0 84 0 0 0  100%  0 
Total 5,665 5,539 5,541 452  --  252 
         
Only Unspecified 7,253 -- -- 7,253  --  -- 
Note: All records include a non-missing value for total award (first row in Table A.1). Values may be missing for Economic or Non-Economic award values, or the data may 
include a value where the type of award is ?Unspecified?. Values in bold can be calculated from other non-missing values according to the percentages in the 
?Percentage Matching? column.  Values for observations where Economic and Non-Economic awards are missing but non-missing values are present for unspecified 
categories are imputed in the next stage of the analysis. 
 
 For some records, data were not only missing for a damage category, but the 
record included values for an unspecified amount. In 148 records there are values for 
economic awards, there are values for unspecified awards but no corresponding values 
for non-economic awards.  In 111 cases, the economic award was equal to the total 
award, and the value for non-economic awards was calculated as zero. The 37 cases 
where the values did not match were dropped. Similarly, in 134 records there are values 
 180
 
for non-economic awards and values for unspecified awards, but no corresponding values 
for economic awards. For the 95 cases where the non-economic award was equal to the 
total awards, the value for non-economic awards was calculated as zero.  The 39 cases 
where the values did not match were dropped. Finally, in 87 cases, the total award was 
$0, and this value was added to both the economic and non-economic variables. 
 Table A.2 reports the results of this analysis. Across all categories, the 
distribution of cases with economic and non-economic awards (as well as punitive 
awards) is about 30 percent lower than the average across all cases. This suggests that the 
cases where both types of damages are recoverable have smaller awards than cases where 
specific awards are not recoverable.  To the extent that this persists through the remaining 
data cleaning steps (including the removal of outliers) and that it persists for cases with 
no or minimal injury (the cases that will be used in the calculation of non-economic 
damages in NIBRS, this will result in a conservative estimate of the losses in these cases.  
 181
 
Ta ble A.2.  
Distribution of Total Award, by economic and non-economic damages.  
Category  
Sub-
Category 
Total Award 
(adjusted) Punitive Award
Economic 
Award 
Non-Economic 
Award 
Total 
(Econ+Non
+Pun) 
All Obs.  $1,376,341 
$133,036 
$365,384 $492,283 $990,073 
Crime   
 
   
 Crime 1,372,276 257,570 131,218 488,404 877,192 
 No-Crime 1,376,643 
123,765 
382,815 492,572 999,152 
Issue   
 
  
 
Crime 1,372,276 
257,570 
131,218 488,404 877,192 
 Malpractice 2,256,547 
71,574 
839,966 751,748 1,663,288
 
Liability 1,150,014 
94,952 
294,542 459,736 849,230 
 Other 1,356,582 
473,041 
180,285 569,920 1,223,246
 
   
Note: All records include a non-missing value for total award (n=12,918). The ?Other? category is mainly comprised of 
negligence cases. Values may be missing for Economic or Non-Economic award values, or the data may 
include a value where the type of award is ?Unspecified?. Thus, the component columns do not sum to the totals. 
However, missing data are recorded as ?0? in the RAND data as are valid ?0? observations. Total award is  
?adjusted? to reflect 2003 dollars.  
 
 
 182
 
Appendix A.2  
 
Selection into Civil Trial 
The processing of civil cases results in only a small proportion of cases actually 
reaching trial (only 2-8 percent of all cases are ultimately adjudicated by a jury).  This 
process is likely non-random (Ostrom, Rottman and Goerdt, 1996; Danzon and Lillard, 
1983; Vidmar, 1993).  Generally, the extant literature asks whether the non-random 
selection of cases into the civil court system leads to cases with larger (or smaller) awards 
in the cases that are ultimately arbitrated by jury. For this paper, the question is slightly 
different. Suppose jury awards are, on average, greater than the expected award for a 
settlement. The critical question is whether those awards are greater because the average 
harm to victims is greater in jury cases, or is it due to differences resulting from the legal 
process that is unrelated to plaintiff harm? Past research generally reports that jury 
awards are higher than awards at settlement. However, if cases that are settled are biased 
downward from the true harm, than jury awards are a better source for the estimation of 
victim harms than settlement data.  There is no empirical way to determine the extent of 
selection in this study given that there are no cases in the RAND data that are not 
adjudicated by jury. A review of the extant literature offers support for and against this 
hypothesis.  
Economic Theory  
Economic research on decision-making in litigation is framed by the pioneering work of 
Landes (1971), Posner (1973) and Gould (1973) who develop theoretical rational choice 
frameworks to identify case attributes that predict pre-trial settlement.  As noted, between 
 183
 
2 and 12 percent of all civil suits ultimately result in a jury-verdict (Ostrom, Rottman and 
Goerdt, 1996; Danzon and Lillard, 1983; Vidmar, 1993) and the plaintiff loses in about 
half of those cases.  Thus, only about 1 in 25 civil cases results in a jury award.  
Landes (1971) developed a theoretic model that identifies case attributes that 
predict the choice between settlement and trial in criminal cases.  Both parties are utility 
maximizing subject to resource constraints.  In the Landes model, the decision to settle or 
go to trial is a function of the probability of conviction at trial, the severity of the crime, 
the availability and productivity of the prosecutor?s and defendant?s resources, 
differential cost of a trial relative to settlement, and risk preferences (61). The process is 
one of strategic bargaining, where a settlement is reached out of court when both actors 
perceive the costs of the trial (including risk) exceed the benefits. The negotiated 
settlement is therefore bounded by the minimum defense offer and the maximum offer by 
the prosecutor (66).   
Posner (1973) subsequently developed a similar model to predict out-of-court 
settlement in civil cases.  Both parties are utility maximizing and risk neutral. The 
plaintiff?s (p) minimum offer is the expected value of the litigation to the plaintiff (P
p
J ? 
C
p
) plus the settlement costs (S
p
).  The expected value of the litigation is the present 
value of the judgment in the event of a win (J), multiplied by the probability of a win 
(P
p
), minus the expected cost of litigation (C
p
). The defendant?s (d) maximum offer is the 
expected cost of litigation ((1 ? P
d
)J + C
d
) to the defendant minus settlement costs (S
d
). 
The expected cost of litigation is the present value of the judgment (J) multiplied by the 
probability of the defendant winning (1 ? P
d
) plus the cost of litigation (C
d
).   
 184
 
Thus, the necessary, though not always sufficient sufficeint, condition for 
settlement is that the plaintiff?s minimum offer is less than the defendant?s maximum 
offer: 
P
p
J ? C
p
 + S
p
 < (1 ? P
d
)J + C
d
 ? S
d
  (2.1) 
The case proceeds to trial when the plaintiff?s minimum offer is greater than the 
defendant?s maximum offer.  
P
p
J ? C
p
 + S
p
 > (1 ? P
d
)J + C
d
 ? S
d
 (2.2) 
The probability a case goes to trial is therefore a function of both parties? expectations 
about the trade-off between the costs of litigating a case (C
p
, C
d
) and settling the case (S
p
, 
S
d
) and the expected judgment (J).  Settlements will be smaller than verdict awards on 
average because settlement costs are expected to be much lower than litigation costs 
(417).  
Gould (1973) adopts the same approach as Posner (1973) but relaxes the 
assumption that both parties are risk neutral.  By incorporating the expected utility 
hypothesis developed by von Neumann and Morgenstern, Gould shows that risk aversion 
and risk preference by either or both parties can alter the probability a case is settled 
before going to trial.  Moreover, the specific amount of the settlement depends on the 
bargaining power of both parties.  If the plaintiff is likely to win (as P
p
 ~1 and (1 ? P
d
) ~ 
0) the settlement will be close to the amount in the claim. Conversely, if P
p
 ~0, the 
settlement will be small (287-8).   
The net effect of this bargaining on the relative size of jury awards to awards from 
a settlement is somewhat ambiguous. If 1< P
p
 <0.5 than the average jury award would be 
 185
 
expected to exceed the settlement, since an acceptable settlement offer will be reduced by 
the expected likelihood of a plaintiff win. Conversely, if 0.5< P
p
 <0, then the average 
settlement will exceed the jury award since the plaintiff is expected to lose in these cases 
and receive no award.  However, average jury awards are unambiguously likely to be 
greater than settlement awards since S
p
,
d
 < C
p
,
d
. Thus, on average, the model predicts that 
jury awards will be larger, but only as a function of the differences in costs between 
litigation and settlement.  
Prior Research 
Danzon and Lillard (1983) apply the models developed by Landes (1971), Gould (1973) 
and Posner (1973) to study the dispositions of medical malpractice claims and address the 
issue of selection bias.  The model is estimated from data drawn from two surveys of 
insurance company claim files closed in 1974 and in 1976.  Less than 10 percent of cases 
were tried to verdict (which falls into the usual range of 2-12 percent).  The mean award 
at verdict was $102,000 and $26,000 at settlement.  However, jury awards are not 
normally distributed ? half of the total award from all claims was explained by less than 3 
percent of all claims (347). The authors observe that if the plaintiff?s minimum ask (P
p
J ? 
C
p
 + S
p
) becomes negative, the claim will be dropped. 
Danzon and Lillard use this model to estimate the unobservable variables, 
including potential award at verdict, potential settlement, minimum plaintiff offer and 
maximum defendant offer (346).  On average, cases settle for 74 percent of their potential 
verdict.  The difference between jury awards and settlement increases with plaintiff 
litigation cost and decreases with defendant litigation costs (375) as predicted by theory 
which incorporates a term discounting the expected value of a verdict for the probability 
 186
 
of winning and for litigation costs that are averted.  Danzon and Lillard note that out-of-
court settlements are strongly influenced by potential verdicts (375).   
Viscusi (1988) analyzes a sample of 10,784 closed product liability claims closed 
between mid-1976 and mid-1977.  Nineteen percent of claims were dropped, 77 percent 
were settled out of court and 4 percent were settled at court.  The plaintiff won in court in 
less than 2 percent of all cases.  Cases settled outside of court settled for less than the 
expected court award due to averted litigation costs, plaintiff risk aversion and the 
nonzero probability of losing (206).  Viscusi asserts that out-of-court settlements 
understate the true value of pain and suffering as the litigation process lowers the 
plaintiff?s reservation price and the defendant?s maximum offer amount below the 
expected court award (214-5).  Thus, while verdict awards are expected to be higher in 
cases adjudicated by a jury, it does not hold that the harms to victims in these cases are 
greater than in cases that are settled (215).  
Sloan and Hsieh (1990) also adopt the standard utility maximization approach to 
analyze medical malpractice claims closed in Florida from October 1985 through March 
1988.  The distribution of case dispositions is similar to Viscusi?of the 6,612 
observations, 16.5 percent were closed before a suit was filed, 72 percent were settled 
before a verdict and 11.5 percent of claims were decided at verdict or on appeal.  In these 
data, the average award to plaintiffs is larger for cases disposed of later in the litigation 
process. Mean payments (in 1987 dollars) were $30,000 for cases settled before a suit 
was filed, $67,000 for cases settled after a suit was filed but before a verdict was reached, 
and $95,000 for cases decided at verdict (1007).  The authors propose that the higher 
awards are mainly explained by plaintiff risk taking, delay in receiving payment and 
 187
 
higher litigation costs (1026).  Sloan and Hsieh do not entirely discount the possibility 
that cases with higher potential awards were selected for trial and they assert that the 
cases adjudicated in court would have settled for more on average than cases that actually 
settled (1027).  
Conclusion 
Prior research generally concludes that out-of-court settlements are lower than awards at 
verdict because settlements are discounted for the risk of an adverse outcome for the 
plaintiff and averted litigation costs on the side of the defendant.  Later research 
comparing awards from out-of-court settlements and from cases resulting in trial verdicts 
finds that settlement awards are almost always lower than awards at verdict.  However, 
much of the difference between settlements and awards at verdict can be explained by 
economic theory. Thus, differences in award size may not be an indication that cases 
settled by jury have more serious harms than cases settled out of court. Put another way, 
if the null hypothesis is that the harms to victims in cases settled by jury and settled out of 
court are equal, than there is little evidence in prior research to reject that null.  
 188
 
Appendix A.3 
 
Assessing the Effectiveness of the Propensity Score Weights 
 Table A.3.1 describes the differences in descriptive statistics between the original 
sample (labeled All) and the smaller sample produced by the propensity scores (labeled 
PS). The most striking difference between the two datasets is that most of the cases 
resulting in a punitive award are not included in the smaller sample. In the original 
dataset, 563 observations included a punitive award (4.4%) and the average award was 
more than $133,000. In the sample created by the propensity scores, only 4 observations 
with a punitive award remain. This results from the inclusion of a dummy for punitive 
award in the algorithm that creates a cross-combination of all attributes. Thus, in order to 
be included in the final dataset, there must be at least one observation with a punitive 
award (and the other attributes in that row) in both the crime and not crime categories. 
Since punitive awards were relatively uncommon in general, it is not surprising few 
remain in the final dataset.  However, since the theoretical literature identifies not having 
the option of a punitive award as a predictor of bias in jury awards, losing these 
observations may well reduce bias in the final sample, and may assist in balancing 
between the crime and not crime groups. 
 More importantly, balancing between the crime and not crime groups produces 
the curious result of making the mean award slightly more dissimilar. While the total 
award is virtually the same, the lack of any punitive awards in the smaller sample (the PS 
sample) means that the mean award is slightly larger once those cases are removed. 
Those differences are not evenly distributed between crime and not crime cohorts. While 
 189
 
the samples labeled as crime have a slightly smaller mean adjusted award ($955,000 
compared to $974,000 in the full sample), the propensity score adjustments result in a 
large change in the not crime cohort, where there is in an increase in mean award from 
$1.33 million to $1.49 million.  Thus, the net result of the propensity score modeling has 
been to create a more balanced distribution of the dependent variable on the predictors, 
but slightly less balance in the adjusted means.  
Table A.3.1.  
Comparison of Total Award Distribution Before and after Propensity Score Weighting.  
Category  Total Award  
Punitive 
Total, Excluding 
Punitive 
Percent any Shared 
Negligence 
 Mean Percentage of Shared 
Negligence 
All  (N=12,918) $1,432,689 $133,036 $1,301,968 25.4% 28.0% 
PS  (N=5,516) 1,430,350 497 1,429,853 26.1  
Crime Indcator - Al       
      Crime (N=895) $1,125,827 $257,570 $974,324 16.1 23.7 
      No-Crime (12,023) 1,459,306 123,765 1,330,387 24.3 28.2 
Crim Indcatr - PS       
      Crime (N=609) $956,037 $292 $955,745 18.5 22.1 
      No-Crime (4,909) 1,490,251 593 1,489,728 15.8 28.4 
Issue - All       
     Crime (N=890) 1,125,827 257,570 974,324 16.1 10.8 
     Malpractice (N=2,219) 2,066,114 71,574 1,994,539 11.8 7.8 
     Liability (N=8,500) 1,284,391 94,952 1,189,435 30.3 28.5 
     Other (N=1,304) 1,322,731 473,041 849,690 11.4 23.9 
Issue - PS       
     Crime (N=609) $956,037 $292 $955,745 18.5 22.1 
     Malpractice (N=960) 2,630,792 1,867 2,628,343 10.4 25.9 
     Liability (N=3,385) 1,207,040 0 1,207,040 19.0 28.5 
     Other (N=564) 1,006,243  0 1,006,243 5.9 24.7 
      
Note: All records include a non-missing value for total award (n=12,918 and N=5,516). All values are adjusted for inflation and presented in 2003 dollars. The ?Total Award? column 
includes all awards (before any reduction for shared negligence). The ?Total, Excluding Punitive? column is the total award without punitive award (before any reduction in 
shared negligence). ?Percent any Shared Negligence? is the percentage of all cases (in that category) that have any ?comparative? or shared negligence. ?Mean Percentage 
of Shared Negligence? is the average percentage reduction due to ?comparative? or shared negligence.  
 
 
 190
 
Independent Variables 
 Table A.3.2 describes the means of the independent variables in the propensity score 
analysis.  The independent variables fall into three categories: the exclusion restrictions 
which are the potential sources of selection as determined by the theoretical literature, 
variables that are common to both the RAND and the NIBRS data that will be used to 
impute values for victims of crime in NIBRS, and other variables that may predict jury 
award. All of these variables were used in propensity score model. 
Among the selection variables, three variables were constructed to match the 
theoretical literature. First, as described above, the literature describing predictors of jury 
awards generally concludes that it is the presence of a defendant that is a business that is 
associated with larger jury awards, rather than the resources (the ?deep pockets?) of the 
defendant. In the RAND data, defendants included businesses, the government and 
hospitals. Each of those was coded as ?business defendants?. 
 Next, the literature suggests that when juries are not given the option of making a 
punitive award, awards for noneconomic and particularly economic losses may be higher. 
Thus, awards in these cases would overestimate the true harms to victims.  However, 
these data are not observable in the RAND data. To approximate this source of bias, a 
dummy variable was coded that is 1 when there was a punitive award, and 0 in other 
cases. The intuition behind this approach is straightforward, that the covariation between 
the presence of a punitive award and other predictors should approximate the covariation 
between the absence of an award and other predictors.  
 
  
 191
 
Table A.3.2.  
Distribution of Independent Variables (Super-Weighted).  
Category Sub-Category 
 
Selection Factors (N=5,516) Mean 
Region Midwest 20.6% 
 South 4.0% 
East 43.4% 
 West 32.0% 
Gender (Male=1) 42.9 
 Reprehensiveness of the Defendant 28.0% 
 Business as a Defendant 49.1% 
 Availability of a Punitive Award to the Jury 0.1% 
Crime 11.0% 
Common Variables   
 Age 36.3
Injury Type No Injury 7.8% 
 Dead 8.6% 
Broken Bones 19.7% 
 Internal Injury 2.3% 
 Severe Lacerations 1.6% 
 Other Major Injury 57.7% 
 Apparent Minor Injuries 24.4% 
 Loss of Teeth 2.7% 
 Unconsciousness 1.2% 
Other Predictors  
 Plaintiff Count 1.28 
 Number of Issues 1.21 
Issue Crime 11.0% 
 Malpractice 17.4% 
 Negligence 61.4% 
 Other 10.2% 
Note: All records include a non-missing value for total award (n=5,516). All values are adjusted for inflation and presented in 2003 dollars. The ?Total Award? column 
includes all awards (before any reduction for shared negligence).  Injury categories are not mutually exclusive and sum to greater than one. 
 
Finally, the civil jury literature suggests that all else being equal, when a defendant is 
particularly reprehensible the plaintiff would receive a larger award. Again, this 
extralegal factor would tend to cause awards to be overestimated. A variable that directly 
estimates defendant ?reprehensiveness? was also not available in the RAND data. Here 
 192
 
again, a similar logic was applied, that the inverse condition?a lack of 
reprehensiveness?could capture the co-variation associated with selection bias.  
 193
 
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