A Review Of The Econometric Evidence On The Effects Of Capital Punishment

A Review of the Econometric Evidence
on the Effects of Capital Punishment zyxwvutsrqponmlkjih
SAMUEL CAMERON*
University of Bradford
ABSTRACT: This paper chiefly surveys the econometric work on the effect of
capital punishment. It also provides a case study of how econometric methods are
used by economists in an area where it is not always easy to keep prior belief separate
from scientific inquiry.
INTRODUCTION
This article is chiefly concerned with surveying the econometric work on the
effect of capital punishment.’ This should be of interest to those interested in
the economics of crime and the application of microeconomics to policy issues.
It will also provide a case study of how econometric methods are used by
economists in an area where it is not always easy to keep prior belief separate
from scientific inquiry. This should prove particularly interesting to those
involved in the emerging field of the “rhetoric” of economics (see, e.g.,
McCloskey, 1985). The article considers the necessary background to
interpretation of the empirical work. The empirical work is then surveyed in
terms of “first generation” studies, that is, those which emerged around the time
that capital punishment was being reintroduced in the United States, and
“second generation” studies which have sought to update or reexamine the older
* Direct all correspondence to: Dr. Samuel Cameron, Department of Social and Economic Studies,
University of Bradford, Richmond Building, Richmond Road, Bradford, West Yorkshire BD7 IDL, England.
The Journal of Socio-Economics, Volume 23, Number l/2, pages 197-214
Copyright @ 1994 by JAI Press Inc.
All rights of reproduction in any form reserved.
ISSN: 1053-5357

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HE JOURNAL OF SOCIO- ECONOMICS Vol. 23/ No. l-211 994
studies. First-generation studies were generally published in 1975-1978; second-
generation studies have emerged since 1983. Studies are now appearing which
cover the postmoratorium period (Chressanthis, 1989; Cloninger, 1991b).
BEFORE T
HE ECONOMIST
S
Until Ehrlich’s 1975 implementation of Becker’s approach to crime in general,
economists had been absent from the debate on capital punishment. Indeed,
there was not really a debate. The area had been dominated by sociological
and psychological approaches whose theory and empirical evidence pointed to
the absence of a deterrent effect.
The crudest approach is the “hereditary” one that criminals are simply born
rather than made. Some people would be seen as murderers2 because of the
particular gene combination bequeathed by their parents. As the born murderer
is viewed as “irrational,” this person will fail to exhibit any response to
punishments. Psychological theories have tended to go beyond this into a more
dynamic concept of personality (see, e.g., Eysenck, 1970). It is possible to find
an argument for the efficacy of capital punishment within the psychological
paradigm in that the exercise of punishment may condition a moral conscience.
However, punishment will not be a universal preventative. The response of
individuals depends on whether they are extroverts or introverts. The former
respond poorly to conditioning whilst the latter respond well. All types of
punishment run the risk of being too severe for the easily conditioned. As
Eysenck says (1970, p. 169), “the attempts of society to treat both types alike
probably means sitting between two stools and getting the worst of all worlds.”
The sociological approach to murder revolves around the notion of a culture
of violence (Glaser, 1977). Violence is only unacceptable where society has
decided that it is not conducive to the functioning of society. It thus becomes
an illegitimate mode of behaviour which is made formally illegal. Different
cultures will not move away from the legitimacy of violence at the same rate.
It can be argued that communities within a tradition of violence will be less
responsive to punishment because their members have yet to fully internalize
the norm of a nonviolent society. It is in this vein that sociologists explain the
fact that most interests them about capital punishment, namely, the high level
of murder and assault in the Southern states despite the presence of higher
execution rates. The archetypal empirical study which formed the focus for the
econometric work of Ehrlich was by Sellin (1959). In a crude attempt to control
for other factors, he compared contiguous states of the United States, finding
those with capital punishment to have similar murder rates to those without it.
Lempert (1983) attempts to rehabilitate Sellin in face of the economist’s critique
that Sellin was wrong to compare states without reference to the rate of
application of capital punishment. He computes partial correlations of the
differences in homicide rates between i andj with their execution rate difference

Econometric Evidence on the Effects of Capita/ Punishment 199
over a number of years. This isjustified on the grounds that a control for interstate
differences via regression analysis is subject to severe problems of obtaining
adequate data to measure the relevant variables other than punishments. The zyxwvutsrqpon
i andj are neighbouring states chosen in the hope that the difference in execution
and homicide is not due to other variables. The results do not find much support
for deterrence. This is really a time-series study. It does not show that the less
executing states will have fewer murders than the more executing but simply
that a faster growth in executions is associated with a faster growth in homicides. zyxwvutsrqpon
ENT
ER T
HE ECONOMIST
S
Becker (1968) opened up the field of study of crime to economists. He did this
with entirely conventional microeconomics, as is common in the Chicagoan
invasion of hitherto unexplored areas. He derives the supply of crime from a
conventional subjective expected approach to decision making under
uncertainty. Crime is the outcome of rational utility-maximizing behaviour.
Hence, there are no “criminals” as such. A criminal is simply somehow whose
portfolio choice contains some activities which are designated as illegal. As
Chicagoan economists assume similarity in tastes, everyone would be equally
likely to commit crime if they were faced with the same constraints. The volume
of crime, therefore, responds to the movements of underlying relative price
variables. The relative price variables fall into two categories: those that are
directly manipulated by governments in response to crime and those that are
outside the control of the criminal justice agencies. The former are generally
regarded as deterrents to crime and include the severity of punishment and the
likelihood of being caught and punished, which is conditional on the amount
of resources devoted to catching and trying criminals. The latter group of
variables generally derives form the labor market. Labor-market variables such
as income and unemployment are taken to measure the opportunity cost of
undertaking criminal activity. For example, if expected income in legitimate
work is higher, then we expect substitution away from risky illegitimate work
to be reinforced by the greater loss of income inexperienced while in prison.
The labor market will also tend to generate the expected pecuniary return from
criminal acts. The more buoyant is the labor market, the greater will be the
value of objects in the possession of potential victims of crime.
The supply of crime function is part of a general equilibrium system. Society
is viewed as responding to the negative externality of crime through spending
on abatement technologies like the police force and the court system. (see Usher,
1986, 1987). In Becker’s normative analysis, this response is driven by the
objective of minimizing social costs. The consequence for econometric analysis
is that there is simultaneity between the crime rate and the probability of
conviction and punishment. Society has a derived demand function for
conviction and punishment which is positively related to the level of crime.

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HE JOURNAL OF SOCIO-ECONOMICS Vol. 23/ No. l-211 994
The economic approach marks a departure from the simple correlations that
marked earlier empirical studies of crime. The supply function concept stresses
the need for a structural equation which includes exogenous measures of the
expected costs and benefits of crime. The general equilibrium approach
demonstrates the need for methods other than ordinary least squares if
consistent, unbiased estimates are to be obtained. This research agenda sparked
a horde of empirical studies purporting to show that devoting more resources
to the criminal justice system would deter crime (see Cameron, 1988).
The econometric study of capital punishment has simply involved slotting
murder into the above framework. None of the papers cited below makes any
attempt to alter the theoretical framework in any fundamental way to allow
for murder different in some way from pickpocketing, tax fraud, or buying the
services of a prostitute. The expected costs of murdering are the same as those
from any other crime, apart from one modification needed to allow for capital
punishment. That is, a murder may result in the death of the murderer. This
is allowed for by attaching a subjective probability to the event of receiving
a death sentence and attaching this to the utility of dying at the time the sentence
is implemented. The determinants of the expected benefits of murder may be
the same as those for property crime where the murder is instrumental to the
property crime. In such cases, murder may be a weapon of last resort, used
only when extreme resistance is offered to surrendering money. Where no direct
monetary pay-off is involved, murder must be assumed to generate psychic
income. People are regarded as having a taste for violent acts against other
people. They are obviously willing to indulge these tastes if the price is right.
When we allow for capital punishment being used against murder, we have
the following utility function for the prospective criminal (Ehrlich, 1975,
Layson, 1983):
EU= (I--PCON) U(G) + PCON(l-PE) U(C,) + PCON.PE zyxwvutsrqponmlkjihgfedcba
U(C2) (1)
where EU = expected utility,
PCON = probability of a murder conviction,
PE = conditional probability of execution given a murder conviction,
U(G) = utility of the individual if not convicted of a murder,
U(CI) = utility of the individual if convicted of d not executed,
U(Cl) = utility of the individual if executed.
This utility function is linear in the probability of death and other punishments
(see Blatt, 1979-1980, for a critique of this). It reduces to the simple case of
someone who is not contemplating murder when PE = 0. Therefore, there is
no formal difference between the murderer and any other criminal if there is
no capital punishment or the potential murderer believes that there is no
probability of it being implemented.

Ec o no me tric Evid e nc e zyxwvutsrqponmlkjihgfedcbaZYXWVUTSRQPONMLKJIHGFEDCBA
o n the Effe c ts o f Ca p ita l Punishme nt 201
The issue of capital punishment does bring some new problems to light in
the welfare economics of punishment.3 These are not discussed here as they
have no implications for the specification of murder supply equations.
In empirical work, it is implicitly assumed that subjective probability is
monotonically related to objective probability when the coefficients of
regression models are interpreted. The initial research estimating murder supply
functions treated the execution rate as endogenous through a demand for capital
punishment equation (this was not always specified as instrumental variables
was usually employed). Exogenous variables such as age, race, labor force
participation, and poverty have been used to measure the opportunity costs
of murder and taste variation in the demand for punishment. Ehrlich (1975)
shows that the above equation predicts the following order of magnitude (in
absolute terms) of murder supply elasticities; arrest rate, conviction rate,
execution rate. The elasticities have been estimated using time-series and cross-
section data: to date, pooled cross-section/time-series data has not been used.
The initial time-series work attracted great publicity in the United States
despite the fact that it only indicates short-run effects. Ehrlich’s work was
considered by the Supreme Court of the United States when considering the
resumption of capital punishment. This sparked much of the research and
critique which followed. In Canada, Ehrlich’s work figured in the parliamentary
debates on the death penalty in 1976 (see Avio, 1979, p. 649, fn. 3). In general,
estimates have been from U.S. data although there are a few Canadian (Avio,
1979, 1988; Layson, 1983; McKee & Sesnowitz, 1977a) and one U.K. (Wolpin,
1978a, 1978b) study. There is a rather basic reason for the lack of cross-country
replication: the majority of democratic nations, apart from the United States,
long ago abandoned the use of capital punishment. This poses a problem for
the purely “scientific” study of capital punishment. Even the most robust results
for the U.S. data would still be subject to the caveat that they are specific to
one society. zyxwvutsrqponmlkjihgfedcbaZYXWVUTSRQPONMLKJIHGFEDCBA
EMPIRICAL WORK: FIRST
- GENERAT
ION ST
UDIES
Ehrlic h’s Work
Ehrlich (1985) used data from 1933-1967 to estimate a murder supply function
by instrumental variables with AR( 1) correction. The murder variable was FBI-
recorded homicides per capita. All equations featured all variables in
logarithms. Punishment variables were arrests divided by murders, convictions
divided by arrests, and executions divided by convictions. The severity of prison
sentence was not included. The point estimates of the elasticities were 0.06
execution, 1.3 arrests and 0.4 for conviction, thus confirming the predicted
ordering. Working back from the execution elasticity, Ehrlich produced his
famous conclusion that one execution would, on average, deter eight murders.

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HE JOURNAL OF SOCIO-ECONOMICS Vo l. 23/ No . l-2/ 1 994
Further support for Ehrlich’s work was given by a very simple piece of time-
series work by Yunker (1976), which found an effect of executions almost 20
times as great!
To further back up his original position, Ehrlich carried out a cross-section
analysis for the continental United States using data for 1940 and 1950. The
specified equation was similar to that of the earlier paper apart from the addition
of a dummy variable to account for the difference between the executing and
non-executing states. Again, a significant deterrent effect of executions was
found although it was slightly smaller, at the sample means, than in the earlier
work. Bearing in mind that cross-section data should represent long-run effects,
this appears to be a substantial finding. It also seems reasonable that long-run
deterrence should be less than the short-run effect. A similar paper by Cloninger
( 1977)4 using 1960 cross-section data lends further support to Ehrlich’s position.
This paper differs in the following ways: a linear functional form is used; the
execution rate is the average for the previous five years; and a North-South
dummy is used rather than that employed by Ehrlich. Considering that the result
for execution survives these specification changes and a new set of data, it might
be considered to be fairly robust.
The Challenge to Ehrlich’sFindings
It would have been surprising if the Ehrlich results had gone unchallenged
given the tradition, outside economics, of believing that capital punishment was
ineffective. There seems also to be a tendency among those with a humanitarian
opposition to capital punishment to be unwilling to accept any evidence of its
efficacy. A number of criticisms have been leveled at the first generation of
capital punishment studies. Attempts to make these stick have generally been
in the form of replications of some sort. I now review the criticisms under various
headings for both cross-section and time-series evidence.
Inadequate Sample
Barnett (1978) points out that there may be insufficient temporal variation
to identify a supply of murder function. Over the sample period used in Ehrlich
(1975), arrest rates rarely deviated much from 90% while execution rates hovered
close to zero, with conviction rates also being highly stable. For the cross-section
data, zyxwvutsrqponmlkjihgfedcbaZYXWVUTSRQPONMLKJIHGFEDCBA
to tal executions for the continental states were in the order of the low
100s around 1940 and below 50 around 1960 (see Glaser, 1977, p. 245). There
is also a very irregular distribution of this total: for example Cloninger (1977)
has an execution rate with a maximum of 0.1, which is for one state; there is
one state with a value of 0.03, a small group in the 0.01-0.02 range, 20 with
zero, and the rest with very small probabilities. Generalizing about changes in
execution rates from elasticities derived from such data is rather problematic.

Ec o no me tric Evidence o n the Effects of Capital Punishme nt 203
Omitted Variables
It is an elementary point of econometrics that excluding a relevant variable
may bias the estimates of included variables. It is not clear a priori what direction
the bias will go in. For the time-series data, potentially relevant variables have
been added by various authors, so it is possible for us to look and see what
difference this makes. This is not the case for cross-section data apart from a
recent paper by Cloninger (1991a) that used data from large American cities.
He includes the probability of death at the hands of the police in the supply
of murder and violent crime equation. He obtains significant negative
coefficients on this variable but finds no effect of capital punishment. Canadian
data has the advantage of there being a mandatory death sentence so that there
is no need to measure the probability of receiving a death sentence, which is
omitted from the U.S. studies. Length of sentence is also available in this data
analysis, in which those by Avio (1979,1988) and McKee and Sesnowitz (1977b)
fail to find a significant deterrent effect of capital punishment. Forst, Filatov,
and Klein (1978) and McKee and Sesnowitz (1977b) advance a very anti-
Chicagoan argument that the supply function shifted over time due to a general
shift in the propensity to commit.crime, that is, a shift in tastes. The former
add other crime rates to the exogenous variables in Ehrlich’s supply function
while the latter add them to the Yunker (1976) equations. Both find that the
added variables banish the significance of the execution rate. Forst et al. also
note the possible importance of gun ownership but do not attempt to measure
it. Kleck (1979) uses a model for 1949-1973 in which gun ownership, conviction
rates, and arrest rates are endogenous; execution is exogenous. The inclusion
of the gun variable removes the significance of the execution rate.
Wro ng ly Included Variables
There have been few claims that a variable should not have been in the murder
supply function. An exception to this is the dummy for executing and non-
executing states. Ehrlich justifies this dummy as capturing unspecified
unmeasured differences between states. He further argues that individuals in
non-executing states believe that the probability of execution is greater than
zero. We may conclude with Taylor (1978, p. 74) that “it is, of course, very
difficult if not impossible to determine whether either of these explanations is
true. Hence the theoretical grounds for placing both variables (dummy and
execution rates) in the regression are not strong.” A number of papers using
cross-section data (Passell, 1975; Forst, 1977; Boyes & McPheters, 1977;
Bechdolt, 1977) do not employ this dummy and fail to find any support for
Ehrlich. Black and Orsagh (1978) do not use the dummy; their 1950 TSLS
equation supports Ehrlich but 1950 OLS estimates and 1960 OLS and TSLS
estimates do not.

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HE JOURNAL OF SOCIO- ECONOMICS Vol. 23/ No. l-2/ 1 994
Functional form
Passe11 and Taylor (1977), Bowers and Pierce (1975), Forst, Filatov, and Klein
(1978), and Hoenack and Weiler (1980) find, for time series, that alternative
(usually linear) functional forms fail to produce significant deterrent effects of
execution when Ehrlich’s model is replicated. A similar result is found for cross-
section data by Passe11 (1975). However, as noted above, the linear formulation
of Cloninger (1977) is highly supportive of Ehrlich’s cross-section results.
Sample Period
It has been argued that Ehrlich’s results depend crucially on the exclusion
of post-1962 data. The post-1962 data is excluded by Forst, Filatov, and Klein
(1978), Bechdolt (1977), Bowers and Pierce (1975), and Passe11 and Taylor
(1977), with the consequence that the significant deterrent effect of executions
vanishes. The same thing happens for U.K. data when the years 1956-1968 are
excluded (Wolpin, 1978a). Comparing Layson (1983) and Avio (1979) shows
a similar pattern for Canada.
Serial Correlation
Forst, Filatov, and Klein (1978) note that the serial correlation parameter
in Ehrlich (1975) is quite low. As is well known, applying quasi-first differences
with a low rho and small samples may lead to poorer estimates than OLS.
Measurement Error
Bowers, Pierce, and McDevitt (1984) argue that the use of FBI data
understates the murder rate and Vital Statistics data should have been used
instead. Ehrlich has also been criticized for replacing zero in the execution series
by the number one in order to run log regressions. More seriously, the murder
series is involved in the construction of the punishment variables so that
elasticities of punishment may be biased towards minus one (Forst, Filatov,
& Klein, 1978). Forst et al.% criticism derives from a Monte Carlo study rather
than the analysis of actual data. This is criticized by Ehrlich and Mark (1977)
who claim that such an approach cannot say anything about the problems in
their data. They also claim that the use of instrumental variables, in the Ehrlich
studies, will have purged the data of measurement error. As this is also a
somewhat speculative claim, we have here the makings of a stalemate. Avio
(1988) attempts to break the deadlock by exploiting the unique properties of
the Canadian data used in his 1978 paper. The problem he addresses is the fact
that other studies have the same denominator in the execution rate as the
numerator in the conviction rate. Only measurement error in the common
variable is dealt with; there is no way of dealing with measurement error in
the homicide series. For Canadian data only, it is possible to construct a
conviction rate variable that does not suffer the difficulty of a common term

Econometric Evidence on the Effects of Capital Punishment 205
to the execution-rate variable. Two sets of regressions are run: one for the error-
prone punishment variables used in other studies and one with the alternative
construction. The results are convincingly against a deterrent effect of capital
punishment except when the error-prone series are used.
In the cross-section analysis, Barnett (1981) has attempted to deal with
measurement error in terms of heterosedasticity. Some studies apply arbitrary
heteroscedastic “corrections”, for example. Ehrlich (1977) simply assumes that
the error variance is inversely proportional to the square root of population.
Barnett derives an alternative estimator from the assumption of a Poisson
process in the error terms. This WLS estimator is applied to the models of
Ehrlich, Forst, and Passell, with the conclusion that Ehrlich’s model is superior
in terms of smaller prediction error. Unfortunately, this conclusion is based on
estimating the models on samples used by the original authors, which are not
strictly comparable.
Simultaneitylldentification Problems
Brier and Fienberg (1980) question the automatic assumption of simultaneous
murder and execution rates. Using instead a time-series model with murder
recursive on execution, they fail to find a deterrent impact. Hoenack and Weiler
(1980) attack Ehrlich for using an ad hoc selection of instrumental variables
as opposed to a completely specified system. In their complete system, murder
can cause a decrease in the execution rate by putting extra strain on the resources
of the police and criminal justice system. This model is implemented on Ehrlich’s
original time series. Tests of the overidentifying restrictions and examination
of the murder supply equation leads them to conclude: “Ehrlich’s estimated
equation could have been causally generated by the response of the criminal
justice system to murder” (1980, p. 338). In defence of Ehrlich, an analysis of
California data for 1950-1978 by Phillips and Ray (1982) finds, using causality
tests, that causation runs from punishment to murder rather than the other way
round.
The Hoenack-Weiler argument has not been applied to cross-section data.
Boyes and McPheters (1977) test the endogeneity of crime using cross-section
data for violent crime. Specification tests indicate that the execution rate is
exogenous.
Brutalization
Ehrlich fails to consider the possibility of brutalization effects, whereby
execution induces murder by lowering societal respect for human life. There
are a number of pieces of time-series evidence of brutalization. Phillips (1980)
examines weekly homicide rates for London over 1858-1921 and finds that
executions deter murder at the time but this is subsequently reversed. He
concludes that annual data would not reveal any correlation between the two

206 T
series. Phillips and Ray (1982) found that their execution years dummy was
positive, a result which they attempt to disclaim as implausible. Bowers, Pierce,
and McDevitt (1984, ch. 8) study monthly New York data from January 1907
to July 1964, regressing homicide rates on execution rates lagged one to twelve
periods and time trend polynomials. The sum of the lag coefficients suggests
dominance of the brutalization effect with the previous two months having
particularly strongly significant large positive coefficients.
Direct evidence from cross-section work is only to be found in Bechdolt
(1977), where the rape rate is significantly positively related to totaZ executions.
A case could be made that brutalization is the crux of the debate about dummy
variables as they are included because states with execution (or more of it) have
higher homicide rates because of long-run brutalization effects.
The brutalization idea is not one that economists have given any credence.
They could argue that the evidence in favor of it is the result of mispecification.
If we have a simultaneous system where executions respond to the rate of murder
as an logical extension of the Becker framework implies, then a positive
correlation of execution rates with murder rates could show simply the “demand
side” of the system dominating. A correctly set-up simultaneous equations
model ought to be able to settle this issue by providing estimates of the structural
parameter of the execution variable in the murder supply function. Someone
who supports the brutalization hypothesis would argue that brutalization is
compounded in this parameter. Nonetheless, if the estimated parameter is still
significantly negative, we must conclude that the deterrent effect dominates the
opposing brutalization effect. The above studies do not use simultaneous
equations methods to isolate the parameter of interest.5
EMPIRICAL WORK: SECOND- GENERAT
ION ST
UDIES
L
a yson’sWork
Given the above attacks, we might suspect that Ehrlich’s original proposition
had sunk into the obscurity of refutation. Indeed, textbook writers have
concluded that “an honest statement would be that the matter is in doubt”
(McKenzie & Tullock, 1978, p. 136). Recently, important work from a
University of Chicago Ph.D. thesis by Layson has sought to rehabilitate the
pro-deterrence stance. The nucleus of this work has been updates of the U.S.
and Canadian data to the mid 1970s (Layson, 1983, 1985). Layson (1983) adds
data for 1961-1977 to the dataset of Avio (1979). He tests for structural stability
and varies functional form without seriously damaging his conclusion that there
is a significant deterrent effect of executions. It must be stressed that there were
no executions in any of the new data; hence, assumptions have to be made about
the formation of expectations to generate the missing values (cf. Lempert, 1983;
Layson, 1985). Layson’s findings depend crucially on the inclusion of a dummy

Econometric Evidence zyxwvutsrqponmlkjihgfedcbaZYXWVUTSRQPONMLKJIHGFEDCBA
o n the Effects of Capital Punishment 207
variable, equal to 0 up to 1960 and 1 thereafter, in his probability-of-execution
equation. This appears in the list of instruments but is not in the murder supply
equation. Given this, it is difficult to take seriously the claim that the execution
parameter estimates really show the effect of variations in the application of
execution. It could be argued that they reflect more the difference between
having and not having capital punishment on the statute book. The use of this
dummy is criticized by Avio (1984), who demonstrates its bearing on the use
of a structural stability test to show that the later data can be paired with the
earlier. He shows that the data fail a test for the stability of the coefficient of
execution risk given constancy in the other coefficients. This implies that the
earlier results of Avio (1979) stand. Layson (1985) effectively wards off some
of the earlier criticisms of Ehrlich in his update. As with the Canadian study,
most of the additional data have zero executions in most years. He shows that
the double log form is the preferred functional specification. The Vital Statistics
data, allegedly superior to that of the FBI, is used without any damage to the
deterrent effect. The Hoenack and Weiler model is replicated, correcting for
an error in their estimation technique, confirming their results. The impact of
this is negated by Layson’s finding that execution rates are exogenous. Extensive
tests of structural stability are performed indicating that a shift occurred in 1962-
1965 or 1969-1973. Experimentation with a list of 12 exogenous variables
demonstrates that the deterrent effect of executions is robust to specification
changes. Although the above might show that criticism of Ehrlich was
misguided, it has to be borne in mind that the Layson papers fail to take gun
ownership into account, either as exogenous or endogenous variable, and thus
fail to dent the impact of Kleck (1979). As pointed out by Fox and Radelet
(1989) the linear trend term used is hardly adequate to cope with this problem.
The recent econometric literature on cointegration is brought to bear on the
1985 Layson paper by Cover and Thistle (1988). Using his data, they find
punishment probability to be a random walk while homicide is nonstationary.
Accordingly, the homicide series is first differenced. The modified equation fails
to find a significant deterrent effect of executions except when Layson’s
Bayesian revision expectations function is replaced with a 3-year unweighted
moving average of his original series. Here, we have a familiar problem in
economics. Some expectations functions support a hypothesis while others do
not, with there being no prior evidence as to which expectations generation
mechanism is more “correct.” It should not be forgotten that the Cover and
Thistle paper ignores the problem of splicing the later data onto the earlier;
hence, even its pro-deterrence results must be viewed cautiously. The use of
annual time-series data will shed light on short-run effects. A recent paper by
Grogger (1990) looks at a much shorter run. He uses 1960s Californian data
on daily homicides to look at the two- and four-week periods after an execution.
He fails to find any correlation between execution and daily homicide rates.
This study also includes measures of the media publicity given to executions.

208 T
This is uncorrelated with homicide rates, again indicating a lack of deterrence
but also an absence of support for the brutalization hypothesis.
Chressanthis (1989) estimates a loosely Ehrlich-type model using data which
starts in 1965 for no apparent reason and comes up to 1985, thus including
pre-, during, and postmoratorium data. This finds some support for the
deterrent effect, but unfortunately, the only punishment variables included are
the clearance rate for homicide and a dummy for whether or not executions
were taking place.
Cross-sectionReplicationsof Ehrlich
In contrast with the time-series papers, the second generation of cross-section
studies has relied exclusively on using the same dataset in the form of Ehrlich’s
(1977) cross-section for 1950 (Learner, 1983; McManus, 1985; Veall, 1986). All
of these papers share the following elements: only WLS estimates of Ehrlich’s
murder supply function in linear form are reported; the heteroscedastic correction
employed is the arbitrary population-based weight used by Ehrlich; and the
execution rate is assumed to be exogenous. The sole concern of these papers
is to examine the sensitivity of the punishment parameters to changes in the
exogenous variables in the equation. In the Bayesian approach, it is recognized
that different people have differing prior convictions as to which variables must
be in the equation and everyone entertains doubts about which other variables
should be in the equation. Learner and McManus delineate a range of beliefs
over the certain variables ranging from the extremes of inclusion to that of
exclusion of punishments. Our interest is in what happens when the execution
variable is in the doubtful list. Using Learner’s Extreme Bounds Analysis, the
extreme bounds on the execution variable span, zero being consistent with either
positive, negative, or zero impact. McAleer, Pagan, and Volker (1985) point out
that this does not demonstrate anything of consequence as switching a variable
from being a focus (certain) variable to doubtful status must involve a sign change
in its extreme bounds. Veall’s paper is designed to redress this difficulty.
Conventional ad hoc regression strategies such as dropping variables with t-ratios
below an arbitrarily low level are subject to the criticism that data-mining impairs
the validity of inferences based on the final results. Veal1 uses “bootstrapping”
to arrive at correct inferences for such processes. He finds that the confidence
intervals obtained exclude zero for the execution and other deterrence variables.
There appears to be support for Ehrlich’s position again. The above conclusion
would be premature as problems in the literature have been overlooked and the
papers under consideration ignore the literature other than Ehrlich’s original
work. There is, again, no attempt to include a gun ownership variable. In
addition, there are serious problems with the executing/ non-executing dummy.
When it is treated as a doubtful variable, it is found that “there is not a significant
deterrent effect of capital punishment.”

Econometric Evidence on the Effects of Capital Punishment 209 zyxwvutsrqpon
CONCL
USION
The aim of this review is to provide a balanced view of the literature. Economists
and criminologists unfamiliar with the more recent literature have probably
concluded that Ehrlich’s “specific results have by now been thoroughly
discredited” (Lempert, 1983, p. 89). This conclusion comes from the view that
Ehrlich’s results are sensitive to modifications in model specification and sample
period. This does not automatically discredit a model; in particular, it does not
provide support to alternative models. These things only arise if a systematic
testing of alternatives against each other is undertaken. We now have the
spectacle that readers of some of the more recent literature might be lead to
believe that few shadows of doubt hang over the work of Ehrlich; indeed, Layson
sees fit to inform us that “even murderers obey the law of demand” (Layson,
1985, p. 88).
What emerges most strongly from this review is that obtaining a significant
deterrent effect of executions seems to depend on adding a set of data with
no executions to the time series and including an executing/non-executing
dummy in the cross-section analyses. As argued above, there is no clear
justification for the latter practice. The significance of the former requires a
little more discussion. It appears, from considering evidence of when capital
punishment was operating, that it “does not work” yet considering additional
evidence; from when it was not in operation, that it does work. There is no
real paradox here. The results obtained could be attributed to the fact that
homicide has been rising while capital punishment was in abeyance. Some
people would argue that this is an indication that capital punishment works.
It does not, however, justify combining execution-free data with the earlier data.
The econometric evidence of a structural break suggests that the two series
should not be pooled. Accepting this implies that there was no short-run effect
of capital punishment while it was in operation. The implication of this is that
there may be what criminologists call “absolute” but no “marginal” deterrent
effect of executions. In other words, the presence of capital punishment on the
statute book acts as some kind of deterrent but variations in its use do not.
It should be noted that this conflicts with SEU theory upon which the analysis
of murder is based. SEU theory would imply that there should be continuous
substitability between penalties; that is, every increase in execution risk should
lead to an adjustment in the supply response of potential murderers.
SUGGEST
IONS FOR FUT
URE RESEARCH
There are clearly severe data limitations on the amount we can ever know about
the effects of capital punishment. However, new studies of official data should
become possible as the resumption of capital punishment is gathering pace
across the United States. It is hoped that the above discussion will prove useful

210 T
to those who undertake the examination of this data. Aside from the problems
of published data, there is the additional constraint that, unlike other areas of
economics, it is doubtful that experimental studies could ever be used to shed
any light on behaviour. The following suggestions are offered for future
research:
1. More investigations should be undertaken of the impact of the gun
variable; it could be subjected to the Learner methodology to assess the impact
of making it a doubtful variable on the confidence interval of the execution
rate.
2. Bayesian and bootstrapping methods could be applied to some datasets
other than Ehrlich’s 1950 cross-section data.
3. The impact of death sentencing should receive some attention. Existing
work deals solely with executions, thus skipping over the intervening stage of
being sentenced to death. Post-1968 U.S. data might be characterized as having
the probability of execution very close to zero, yet there are large interstate
variations in the issue of a death sentence. This could provide interesting
evidence as the prospect of eking out a miserable existence on death row could
conceivably, even in utility-maximizing models, have a bigger deterrent effect
than execution itself.
4. The dependent variable should be adjusted in recognition of the fact that
it is not the supply of murders. It is well known that many murders are the
outcome of interpersonal disputes where it is difficult to think of them as
intentionally supplied (Glaser, 1977). These should be subtracted. Some
murders are instrumental to other crimes of economic gain; it is desirable that
these be isolated as application of exogenous variables measuring net returns
might be more plausible in such circumstances.’ This suggestion has been made
before (Black & Orsagh, 1978) but has only been implemented by Parker and
Smith (1979), who unfortunately examine homicide without considering capital
punishment. We should also note that attempted murder ought to count in the
supply function. To this end, violent assaults carried out in the pursuit of gain
could be added to murders for gain.’
5. At the most microlevel possible, economists could study the records of
known murderers in the hope of establishing some kind of distribution for
murder over the career of murderers. Existing research does not distinguish
between the rate of murder and the decision to participate in murder.
Investigation of this distinction in microdata might lead to improved
specification of the aggregate supply function.
6. The time-series data could be subjected to structural time-series analysis
rather than regression. Within this framework, the abolition of capital
punishment could be treated as an intervention variable. An unpublished study
using data for England and Wales from 1880-1986 finds support for a deterrent
effect using this method (Deadman & Pyle, 1989).

Acknowledgments: The author would like to thank Professor Dale Cloninger and Ken Avio
for invaluable comments on earlier drafts of this paper. Remaining errors are his sole
responsibility. zyxwvutsrqponmlkjihgfedcbaZYXWVUTSRQPONMLKJIHGFEDCBA
NOT
ES
1. Earlier surveys (Barnett, 1978; McGahey, 1980) are less comprehensive than the present article
and are also out of date.
2. As in much of the literature, I refer to murder in connection with capital punishment
throughout the paper. Capital punishment has been administered for rape and other violent
crimes; a small number of the papers cited investigate this.
3. The welfare economics debate opened with McKee and Sesnowitz (1976) and Reynolds
(1977); it is examined in greater depth in Cameron (1989).
4. Cloninger (1977) contains an error detected by the present author and corrected for in
Cloninger (1987). The corrected results have greater estimated deterrent effects with larger
t-ratios. McGahey (1980) argues that the omission of length of prison sentence generates
bias which leads to Cloninger’s paper providing an estimate of 560 murders deterred by one
execution; this is over 20 times greater than Cloninger’s own estimate. McGahey does not
explain where this number comes from. The coefficient on the execution variable corresponds
to a (H/P) / d (E/H) where H is homicides, P is population, and E is execution. Letting
X stand for other regressors and a, the intercept; b, the coefficient on X, and c, the above
partial differential, we must solve the following quadratic:
(l/P)H’-aH-cXH-bE=O
to get an expression for H/E which reduces to:
b[l I {(H/P)---bWH)ll
5. This criticism is not entirely telling. The simultaneity bias will be avoided in Phillips (1980)
given the extremely short run in which he operates. It could also be argued that the use
of lagged executions exempts Bower, Pierce, and McDevitt (1984) from this criticism.
6. Avio (1988), in his replication of Avio (1978), uses a wide variety of expectations formulations.
None of these prove significant in his “error free” constructions of the punishment variables.
7. Peck (1976) suggests that the utility-maximizing model is only relevant to a small subset
of murders.
8. Cook (1979) analyzes intercity variations in gun robbery rates, which would give a good
opportunity to measure the impact of capital punishment. Unfortunately, he only uses data
for the period when capital punishment was dormant in the United States.
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