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“Striking out” as crime reduction policy: The impact of “three strikes” laws on crime rates in U.S. cities Tomislav V. Kovandzic a; John J. Sloan III a; Lynne M. Vieraitis a a University of Alabama at Birmingham,

Online Publication Date: 01 June 2004

To cite this Article: Kovandzic, Tomislav V., Sloan III, John J. and Vieraitis, Lynne M. (2004) '“Striking out” as crime reduction policy: The impact of “three strikes” laws on crime rates in U.S. cities', Justice Quarterly, 21:2, 207 — 239

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A R T I C L E S

" S T R I K I N G OUT" A S C R I M E R E D U C T I O N P O L I C Y :

T H E I M P A C T O F " T H R E E S T R I K E S " I.AWS O N C R I M E R A T E S I N U . S . C I T I E S

TOMISLAV V. KOVANDZIC* J O H N J. SLOAN, III**

L Y N N E M. VIERAITIS*** U n i v e r s i t y of Alabama at B i r m i n g h a m

During t h e 1990s, i n response to public dissatisfaction over w h a t were perceived as ineffective crime reduction policies, 25 states and Congress passed t h r e e strikes laws, designed to d e t e r criminal offenders by m a n d a t i n g significant sentence e n h a n c e m e n t s for those w i t h prior convictions. F e w large-scale e v a l u a t i o n s of t h e i m p a c t of t h e s e laws on crime rates, however, have been conducted. Our study used a m u l t i p l e t i m e series design and U C R d a t a from 188 cities w i t h populations of 100,000 or more for t h e two decades from 1980 to 2000. We found, first, t h a t t h r e e strikes laws a r e positively associated w i t h homicide r a t e s in cities in t h r e e s trike s s t a t e s and, second, t h a t cities i n t h r e e strikes states witnessed no significant reduction in crime rates.

Between 1993 and 1996, the federal government and 25 states passed w h a t are popularly known as "three strikes and you're out" laws (Austin & Irwin, 2001). Intended to both deter and incap-

* Tomislav Kovandzic is a n a s s i s t a n t professor in t h e D e p a r t m e n t of J u s t i c e Sciences at t h e U n i v e r s i t y of A l a b a m a at B i r m i n g h a m . His c u r r e n t r e s e a r c h i n t e r e s t s include criminal j u s t i c e policy and g u n - r e l a t e d violence. His most r e c e n t articles h a v e appeared in Criminology and Public Policy, Criminology, and Homicide Studies. He received his PhD in Criminology from Florida State U n i v e r s i t y in 1999.

** J o h n J . Sloan H I is i n t e r i m c h a i r p e r s o n o f t h e D e p a r t m e n t of J u s t i c e Sciences a t t h e U n i v e r s i t y of A l a b a m a at B i r m i n g h a m w h e r e h e is also associate professor of c r i m i n a l justice, sociology, a n d women's studies. His r e s e a r c h i n t e r e s t s include c r i m i n a l j u s t i c e policy, fear and perceived risk of victimization, and j u v e n i l e justice. His w o r k h a s a p p e a r e d in such journals as Justice Quarterly, Criminology, Criminology and Public Policy, a n d Social Forces.

*** Lynne M. Vieraitis is an a s s i s t a n t professor in t h e D e p a r t m e n t of Justice Sciences at t h e U n i v e r s i t y of A l a b a m a at B i r m i n g h a m . H e r r e s e a r c h i n t e r e s t s include economic in eq ua lity and violent crime, g e n d e r and victimization, and c r i m i n a l j u s t i c e policy. H e r w o r k h a s a p p e a r e d in Criminology, Violence Against Women, and Social Pathology. She received h e r P h D in Criminology from t h e Florida S t a t e U n i v e r s i t y in 1999.

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208 "STRIKING OUT" AS CRIME REDUCTION POLICY

acitate recidivists, this legislation generally mandates significant sentence enhancements for offenders with prior convictions, including life sentences without parole for at least 25 years on conviction of a t h i r d violent felony or for some categories of offenders simply life without parole (Austin & Irwin, 2001; Clark, Austin, & Henry, 1997; Schichor & Sechrest, 1996). 1

Proponents of the s t a t u t e s based t h e i r support on published results of career-criminal r e s e a r c h (Shannon, McKim, Curry, & Haffner, 1988; West & Farrington, 1977; Wolfgang, Figlio, & Sellin, 1972) and a r g u e d t h a t the s t a t u t e s would deter and incapacitate high-rate recidivist offenders and t h u s result in lower crime rates. First, u n d e r the sentencing schemes, "high- level" offenders ( m e a s u r e d both by the type and the n u m b e r of prior convictions) would be specifically targeted for incarceration (Stolzenberg & D'Alessio, 1997; Walker, 2001; Zimring, 2001). Second, the s t a t u t e s would significantly reduce judicial sentencing discretion, thereby increasing t h e certainty of p u n i s h m e n t while e n h a n c i n g the t e r m of i m p r i s o n m e n t and t h u s increasing t h e severity of the sanction. Finally, states would rely more heavily on prisons for r e p e a t offenders t h a n t h e y h a d in the past ( D i h l i o , 1994, 1995, 1997; Jones, 1995; Scheidigger & Rushford, 1999; Wilson & Herrnstein, 1985; Wilson, 1975; Wyman & Schmidt, 1995). Proponents a r g u e d t h a t by enhancing recidivists' sentences, e n s u r i n g they actually serve enhanced terms, a n d reducing the chance for early parole release, t h e s t a t u t e s would reduce judicial discretion, limit t h e opportunity for parole boards to release "dangerous" offenders back into t h e community, and reduce crime levels because offenders would be deterred, incapacitated, or both.

Although these laws have now been in effect for nearly a decade and California's has been evaluated several times (e.g., Greenwood, Rydell, Abrahamse, Caulkins, Chiesa, Model, et al., 1994; Stolzenberg & D'Alessio, 1997; Zimring, Hawkins, & Kamin, 2001), only two larger-scale evaluations have been published (Kovandzic, Sloan, & Vieraitis, 2002; Marvell & Moody, 2001), and t h e y focused mainly on homicide. Thus, while much has been le a rn e d about how three strikes laws m a y work in California or about their impact on one serious crime, no large-scale comprehensive analysis has been published.

This study extends t h e work of Kovandzic et al. (2002) and Marvell and Moody (2001) by evaluating w h e t h e r t h r e e strikes

1 There is significant variability in t h e offenses t h a t "trigger" t h e strike as well as in t h e specific s e n t e n c e s a d m i n i s t e r e d u n d e r t h e laws. See A u s t i n a n d Irwin (2001) for an excellent analysis of t h i s variation.

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KOVANDZIC, SLOAN, AND VIERAITIS 209

laws do in fact reduce most forms of serious persona] (murder, rape, robbery, and aggravated assault) and property (burglary and motor vehicle theft) crime. Specifically, we examined the potential d e t e r r e n t and incapacitative effects of the laws on serious crime rates using panel data collected for 188 U.S. cities with populations of 100,000 or more for t h e period 1980 to 2000. Our evaluation extends previous research in several ways. First, we include numerous control variables in t h e statistical models to mitigate the problem of omitted variable bias. Second, to examine the potential incapacitative effects of the laws, which would be unlikely to appear until years after the laws h a d been passed, we use a longer post-intervention period in our models. Finally, we a t t e m p t to address, though admittedly with limited success, the issue of simultaneity (i.e., rising crime rates m a y affect the passage a n d application of three strikes laws) in our crime rate models. If simultaneity is not adequately addressed, potential crime-reducing effects of t h e laws might be negated by t h e positive effects of crime on the passage and application of the laws.

In the sections t h a t follow, we provide an overview of three strikes laws and review published analyses of the impact of t h e laws on crime. Then we present our methods and data analytic plan. Finally, we present results of our analysis and conclude by discussing our results and their implications for sentencing policy in the United States.

Three S t r i k e s L a w s

In 1993, Washington became the first t h r e e strikes state when it passed an initiative m a n d a t i n g life t e r m s of imprisonment without possibility for parole for individuals convicted a third time for specified violent offenses. California quickly became the second, passing its well-publicized law in 1994. By 1996, 23 other states and t h e federal government had enacted similar statutes.

Analyses of the content of these laws by Turner, Sundt, Applegate, and Cullen (1995) and Austin and Irwin (2001) reveal several recurring themes. First, almost all the states include serious violent offenses (e.g., murder, rape, robbery, and serious assault) as strikeable. Other states include drug-related crimes (Indiana, Louisiana, California); burglary (California); firearm violations (California); escape (Florida); treason (Washington); and embezzlement and bribery (South Carolina). Second, there is variation in the n u m b e r of strikes needed for an offender to be out. In eight states, two strikes bring a significant sentence enhancement. Third, states differ in the t e r m of incarceration imposed on offenders who strike out. Eleven impose m a n d a t o r y life

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210 "STRIKING OUT" AS CRIME REDUCTION POLICY

t e r m s of i m p r i s o n m e n t w i t h o u t parole, a n d t h r e e allow for parole b u t only after a specified l e n g t h y t e r m of incarceration (25 y e a r s in California, 30 years in New Mexico, a n d 40 y e a r s in Colorado). Additionally, five (Alaska, Arizona, Connecticut, Kansas, a n d Nevada) call for sentence e n h a n c e m e n t s , b u t leave t h e specifics to t h e discretion of t h e court. Finally, six (Alaska, Florida, N o r t h Dakota, Pennsylvania, U t a h , and Vermont) provide for a r a n g e of sentences for r e p e a t offenders t h a t m a y include life in prison if t h e final strikeable offense involves serious violence.

Dickey a n d Hollenhorst's i n - d e p t h a s s e s s m e n t (1998) r e v e a l s - - despite claims by policy m a k e r s a n d prosecutors t h a t t h e laws were a n essential crime fighting t o o l - - t h a t m o s t states have n o t applied t h r e e strikes legislation extensively. For example, by mid-year 1998, 17 states h a d b e t w e e n 0 a n d 38 offenders sentenced u n d e r t h r e e strike provisions (Alaska, Arizona, Colorado, Connecticut, I n d i a n a , Maryland, M o n t a n a , New Jersey, New Mexico, N o r t h Carolina, P e n n s y l v a n i a , South Carolina, Tennessee, U t a h , Vermont, Virginia, Wisconsin). Only t h r e e (Florida, Nevada, Washington) h a d slightly more t h a n 100 offenders serving t h r e e strike sentences. The only two states t h a t have applied t h e legislation w i t h any consistency are California a n d Georgia. As of mid-year 1998, Georgia h a d sentenced almost 2,000 offenders u n d e r one a n d two strike provisions, a n d California more t h a n 40,000 u n d e r two a n d t h r e e strike provisions.

Effects o f Three Strikes L a w s on Crime 2

Despite t h e popularity of the laws a n d t h e decade t h e y h a v e been in effect, few published s t u d i e s h a v e explicitly e v a l u a t e d t h e i r i m p a c t on crime. Those t h a t have can be separated into those whose focus was California a n d those whose focus was national. Additionally, some of t h e studies focused only on t h e laws' i m p a c t on certain crimes (e.g., homicide), while others e x a m i n e d t h e laws' i m p a c t on a larger set of offenses (e.g., serious property crime). ~

2 T h e r e h a s b e e n a g r e a t deal of c o m m e n t a r y o n t h e i m p a c t of t h r e e s t r i k e s laws o n p r i s o n p o p u l a t i o n s ( A u s t i n 1994), t h e i r r a c i a l d i s p a r i t y (Crawford, Chiricos, & Kleck, 1998), t h e c o n s t i t u t i o n a l i t y of t h e l a w s (Kadish, 1999), a n d t h e i r f a i r n e s s (Dickey & H o l l e n h o r s t , 1998; Vitiello, 1997). B e c a u s e t h e c u r r e n t s t u d y e x a m i n e d t h e p o t e n t i a l i m p a c t of t h e laws on c r i m e r a t e s , t h e l i t e r a t u r e r e v i e w is l i m i t e d to p u b l i s h e d s t u d i e s a d d r e s s i n g t h a t q u e s t i o n .

3 S t u d i e s i n c l u d e d for r e v i e w clearly do n o t r e p r e s e n t a c o m p r e h e n s i v e r e v i e w of p u b l i s h e d r e s e a r c h on C a l i f o r n i a ' s t h r e e s t r i k e s law. T h e y w e r e selected e i t h e r b e c a u s e t h e y u s e d s o p h i s t i c a t e d q u a n t i t a t i v e e v a l u a t i v e d e s i g n s or, i n t h e case of Z i m r i n g , H a w k i n s , a n d K a m i n (2001), b e c a u s e of t h e d e p t h of t h e a n a l y s e s .

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K O V A N D Z I C , S L O A N , A N D V I E R A I T I S 211

Evaluating California's Three Strikes Law

The first study to examine the potential incapacitative impact of California's three strikes laws was a projection analysis conducted by Greenwood et al. in 1994. Specifically, the authors used a m a t h e m a t i c a l model t h a t tracked the flow of criminals t h r o u g h t h e justice system, calculated the costs of r u n n i n g t h e system, and predicted the n u m b e r of crimes criminals commit when on the street. The results of the simulation analysis suggested t h a t a fully implemented law would reduce serious crimes (mostly assaults and burglaries) in the state by 28% per y e a r at an average a n n u a l cost of $5.5 billion. 4 The authors assumed no d e t e r r e n t effect of t h e laws on crime, claiming this assumption was consistent with prior deterrence research.

Using ARIMA time-series analysis with monthly data, Stolzenberg and D'Alessio (1997) examined the impact of California's three strikes law on FBI index offenses in the 10 largest cities in the state from 1985 to 1995. Trends in t h e petty- theft r a t e were used as a control group to mitigate possible t h r e a t s to internal validity. Three different intervention points t h a t signify the effects of the law were considered and the authors opted to use the abrupt p e r m a n e n t change model (i.e., the date t h e law w e n t into effect, March 1994) because it provided the best fit to t h e data. They reported that, with the possible exception of Anaheim, the law h a d little impact on either index crimes or petty theft. They presented three possible explanations: (1) existing sentencing schemes already confined substantial numbers of high-risk offenders in prison, resulting in a diminishing marginal r e t u r n from increased levels of incarceration; (2) by the time m a n y offenders are confined for their third strike, their criminal careers are already on the downturn; and (3) there is little evidence t h a t juveniles, despite their accounting for a disproportionate a m o u n t of crime in California, were affected by t h e law. ~

Males and Macallair (1999) tested the hypothesis t h a t California counties t h a t enforced the law more frequently would

4 G r e e n w o o d e t al. (1994) m a d e a s e r i e s of a s s u m p t i o n s , some of w h i c h could be c h a r a c t e r i z e d as q u e s t i o n a b l e , w h i c h h a d s i g n i f i c a n t i m p l i c a t i o n s for t h e r e s u l t s . F o r example, t h e y a s s u m e d t h e f r a c t i o n of citizens b e c o m i n g a c t i v e c r i m i n a l s o v e r t h e 2 5 - y e a r p e r i o d would r e m a i n r o u g h l y c o n s t a n t , t h e y did n o t allow offenders to s w i t c h b a c k a n d f o r t h b e t w e e n h i g h a n d low offense r a t e s , a n d t h a t t h e law would b e i m p l e m e n t e d a n d e n f o r c e d as w r i t t e n .

5 A s i m i l a r a r g u m e n t was m a d e b y S c h m e r t m a n n , A m a n k w a a , a n d Long (1998) i n t h e i r a n a l y s e s of t h e i m p a c t of t h r e e s t r i k e s l a w s on p r i s o n p o p u l a t i o n figures. S c h m e r t m a n n e t al. concluded t h a t f a i l i n g to c o n s i d e r age effects o n c r i m i n a l a c t i v i t i e s r e s u l t s i n a n i n c o m p l e t e a n a l y s i s of t h e costs a n d b e n e f i t s of t h e policy i n w h i c h t h e costs of t h e policy a r e u n d e r e s t i m a t e d w h i l e i t s b e n e f i t s a r e o v e r e s t i m a t e d .

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212 " S T R I K I N G O U T " A S C R I M E R E D U C T I O N P O L I C Y

see g r e a t e r reductions in crime a n d t h a t age group populations (in this case t h e over-30) m o s t t a r g e t e d by t h e law would show g r e a t e r decreases in crime p a t t e r n s . To examine this question, Males a n d Macallair (1999) collected county FBI index offense arrest statistics for t h e state's 12 l a r g e s t counties, disaggregated by age, 3 y e a r s after t h e law took effect (1995-1997) a n d c o m p a r e d those d a t a w i t h 3 years' w o r t h of prior d a t a (1991-1993) in t h e s a m e counties. 6 They found t h a t county crime d a t a for post-law years failed to s u p p o r t t h e p r e s u m e d crime reduction promised by t h e law, either t h r o u g h selective incapacitation or deterrence. Counties t h a t invoked t h e law at h i g h e r r a t e s did n o t experience t h e g r e a t e s t decrease in crime. I n fact, S a n t a Clara, one of six counties m o s t frequently i m p l e m e n t i n g t h e law, w i t n e s s e d an increase in violent crime. Males a n d Macallair (1999) also failed to find age-related incapacitative effects, regardless of how often t h e law was invoked. T h e i r s t u d y t h u s suggested t h a t California counties t h a t vigorously a n d strictly enforced t h e state's t h r e e strikes law did not experience a decline in any crime category compared to counties t h a t applied it less frequently.

Z i m r i n g et al. (2001) u s e d various d a t a to examine t h e potential d e t e r r e n t a n d incapacitative effects of t h e law. They found t h a t "the odds of i m p r i s o n m e n t for second and t h i r d strike d e f e n d a n t s w e n t up only modestly" a n d t h a t t h e r e was "no credible case to be m a d e for d r a m a t i c qualitative i m p r o v e m e n t s in t h e rate of i m p r i s o n m e n t from t h e a d v e n t of t h r e e strikes in 1994 a n d 1995" (p. 94). T h e y also a r g u e d t h a t lower crime rates found statewide in 1994-1995 were evenly spread a m o n g both t a r g e t (second a n d t h i r d strike offenders) a n d n o n t a r g e t e d populations (first strike offenders). Overall, t h e y concluded t h a t s h o r t - t e r m felony crime reduction in t h e state as a r e s u l t of t h e t h r e e strikes law was b e t w e e n 0% and 2%. ~

S h e p h e r d (2002) u s e d time-series cross-section d a t a for 58 California counties for t h e 1983-1996 period to m e a s u r e t h e full d e t e r r e n t effect on crime rates. She s u g g e s t e d t h a t prior studies (Zimring et al., 1999; Greenwood et al., 1994) u n d e r e s t i m a t e d t h e effect because t h e y focused only on r e p e a t offenders. If strike sentences d e t e r only r e p e a t offenders facing t h e i r last strike, she hypothesized, t h e n t h e laws should d e t e r both strikeable a n d nonstrikeable felonies. O n t h e other h a n d , if t h e law deters all

6 T h e counties i n c l u d e d A l a m e d a , C o n t r a Costa, F r e s n o , Los A n g e l e s , O r a n g e , Riverside, S a n B e r n a r d i n o , S a n Francisco, S a c r a m e n t o , S a n t a C l a r a , S a n Diego, a n d V e n t u r a .

7 T h e Z i m r i n g e t al. (2001) s t u d y did n o t focus exclusively o n t h e crime- r e d u c i n g effects of C a l i f o r n i a ' s t h r e e s t r i k e s s t a t u t e . R a t h e r , i t w a s a m u c h b r o a d e r - b a s e d a n a l y s i s of t h e politics, j u r i s p r u d e n c e , a n d i m p a c t of t h e s t a t u t e .

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KOVANDZIC, SLOAN, AND VIERAITIS 213

potential criminals, t h e n one might expect strike sentences to reduce only strikeable felonies as prospective criminals, fearing initial strikes, avoid committing crimes t h a t qualify as strikes. To examine this possibility, Shepherd regressed county-level crime rates on the n u m b e r of offenders receiving a two or three strike sentence divided by the total n u m b e r of those receiving any sentence and used numerous demographic, economic, and deterrence control variables to mitigate omitted variable bias. The findings supported the theory of full deterrence because only strikeable felonies were reduced by the probability of two and t h r e e strike sentences. Specifically, Shepherd estimates t h a t strike sentences led to 8 fewer homicides, 12,350 fewer robberies, 5,222 fewer aggravated assaults, 7 fewer rapes, and 144,213 fewer burglaries during t h e first 2 years. With the exception of Shepherd, then, studies on the impact of three strikes laws in California did not support their efficacy.

N a t i o n a l Studies

Two published studies, Marvell and Moody (2001) a n d Kovandzic et al. (2002), examined the impact of three strikes laws on state crime rates and city homicide rates, respectively. Marvell a n d Moody (2001) used state panel data for 1970 to 1998 to examine changes in crime rates in three strikes states compared to non-three strikes states. They reported t h a t in states with the laws, homicides increased by 10% to 12% in t h e short term, a n d 23% to 29% in the long term. They suggested t h a t offenders facing the possibility of life in prison for a third strike m a y be more likely to kill witnesses at t h e crime scene in an effort to avoid detection. Marvell and Moody also found t h a t three strikes laws did not reduce rates of rape, robbery, assault, burglary, larceny, or auto theft.

Kovandzic et al. (2002) found similar results for homicide using panel data from 188 cities for the 1980-1999 period. Results indicated that, compared with cities in states without the laws, cities in states with three strikes laws experienced a 13% to 14% increase in homicide rates in the short t e r m and a 16% to 24% increase in t h e long term.

In summary, published studies of the impact of three strikes laws on crime have generally concluded t h a t the laws either have minimal impact on crime or m a y "backfire" and cause an increase in homicide. The latter situation may, as Kovandzic et al. (2002) concluded, illustrate the "law of u n i n t e n d e d consequences" in action. Not only does the policy choice not reduce the extent or seriousness of the problem targeted, but actually intensifies it.

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214 "STRIKING OUT" AS CRIME R E D U C T I O N POLICY

To w h a t e x t e n t h a s t h e r e b e e n a l o n g - t e r m backfire effect of t h r e e s t r i k e s l a w s on serious crime? H a v e cities in s t a t e s w i t h t h e s e l a w s e x p e r i e n c e d significant declines or i n c r e a s e s in s e r i o u s crime over time? In t h e a n a l y s e s below, w e a d d r e s s t h e s e a n d r e l a t e d issues. We f i r s t t u r n to a d i s c u s s i o n o f t h e m e t h o d s a n d d a t a a n a l y t i c p l a n u s e d in t h e c u r r e n t study.

D A T A A N D M E T H O D S

This s t u d y e s t i m a t e d t h e overall a n d state-specific effects of t h r e e s t r i k e s l a w s on U C R index crimes u s i n g a m u l t i p l e time- series design (MTS), w i t h city-level t i m e - s e r i e s cross-section d a t a for t h e y e a r s 1980 t h r o u g h 2000 for all 188 U.S. cities w i t h a p o p u l a t i o n of 100,000 or m o r e in 1990 a n d for w h i c h r e l e v a n t U C R d a t a w e r e available. O f t h e 188 cities w i t h p o p u l a t i o n s of 100,000 or m o r e in 1990, 110 w e r e in s t a t e s t h a t p a s s e d t h r e e s t r i k e s l a w s b e t w e e n 1993 a n d 1996.

M T S is c o n s i d e r e d one of t h e s t r o n g e s t q u a s i - e x p e r i m e n t a l r e s e a r c h d e s i g n s for a s s e s s i n g t h e i m p a c t of criminal j u s t i c e policy w h e n m o r e t h o r o u g h e x p e r i m e n t a l control is n o t possible or practical, as is t h e case h e r e (Campbell & S t a n l e y , 1963, pp. 5 5 - 57). s Its m a i n a d v a n t a g e is t h a t it allows t h e r e s e a r c h e r to t r e a t t h e p a s s a g e of t h r e e s t r i k e s l a w s as a " n a t u r a l e x p e r i m e n t , " w i t h t h e 110 cities r e s i d i n g in t h r e e s t r i k e s s t a t e s as " t r e a t m e n t cities" a n d t h e 78 n o - c h a n g e cities as "controls." Specifically, w e c o m p a r e d o b s e r v e d c h a n g e s in crime r a t e s in t h e t r e a t m e n t cities (before a n d a f t e r t h r e e s t r i k e l a w s ) to o b s e r v e d c h a n g e s in crime r a t e s in t h e control cities. I f t h r e e s t r i k e s l a w s r e d u c e d crime t h r o u g h d e t e r r e n c e a n d i n c a p a c i t a t i o n t h e n t h e t r e a t m e n t cities s h o u l d e x p e r i e n c e a n i m m e d i a t e drop in crime g r e a t e r t h a n t h e control cities a t t h e t i m e t h e l a w s w e r e adopted, w i t h a n a d d i t i o n a l r e d u c t i o n s p r e a d o u t over t i m e a s o f f e n d e r s b e g a n s e r v i n g t h e a d d i t i o n a l portion of t h e i r prison t e r m s d u e to t h e t h r e e s t r i k e s s e n t e n c e e n h a n c e m e n t .

A d d i t i o n a l a d v a n t a g e s of t h e M T S design include, first, t h e ability to e n t e r proxy v a r i a b l e s for o m i t t e d v a r i a b l e s t h a t c a u s e c r i m e r a t e s to v a r y across y e a r s a n d cities (the p r o x y v a r i a b l e s , w h i c h n u m b e r n e a r l y 400 here, a r e d i s c u s s e d f u r t h e r below); second, a l a r g e r s a m p l e size (n= 3,320 or more), p e r m i t t i n g u s to

a The MTS design has been utilized in many recent evaluations of criminal justice interventions including juvenile curfew laws (McDowall et al., 2000), firearm sentence enhancement laws (Marvell & Moody, 1995), concealed-carry handgun laws (e.g., Ayres & Donahue, 2003; Kovandzic & Marvell, 2003; L o t t & Mustard, 1997), Brady law (Ludwig & Cook, 2000), and earlier studies examining the effects of three strikes laws (Kovandzic et al., 2002; Marvell & Moody, 2001; Shepherd, 2002).

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include n u m e r o u s controls in t h e crime r a t e models for factors t h a t might be correlated with other explanatory variables and therefore lead to spurious associations among these variables (Wooldridge, 2000, p. 434); and, third, g r e a t e r statistical power (due to the large sample size) a n d with it the ability to detect more modest effects of t h r e e strikes laws on crime rates (see Wooldridge, 2000, p. 409).

The city was chosen as the u n i t of analysis because it is the smallest and most internally homogeneous unit for which UCR crime d a t a for a large national sample of geographical areas were available. Analyses using states or regions are more susceptible to aggregation bias because t h e y are too heterogeneous and necessarily ignore important within-state variation in crime rates and variables affecting those rates. For example, a state could have one jurisdiction with relatively low crime rates where t h r e e strikes sentence enhancements are applied quite frequently, and other areas with much higher crime rates and little or no application of t h r e e strikes sentence enhancements, consistent with the idea t h a t t h r e e strikes sentence e n h a n c e m e n t s reduce crime. 9 However, when t h e areas are aggregated to the State level, the high-crime areas could dominate t h e crime m e a s u r e so much t h a t t h e state would show a higher-than-average crime rate despite a causal effect of t h r e e strikes laws on crime rates operating at lower levels of aggregation.

One drawback of using city data, however, is t h a t disturbance t e r m s for cities within the same cluster (i.e., state) might be serially correlated during a particular y e a r because of some undefined similarity. In such a situation, s t a n d a r d errors are likely to be underestimated, t h u s inflating t-ratios for the three strikes law variables (Greenwald, 1983; Moulton, 1990). To avoid this problem, we used a Huber-White correction for s t a n d a r d errors (available in SAS 8.0), t h a t accounts for the tendency of within- cluster error terms to be correlated.

Econometric Methods for Time-Series Cross-Section Data

Following convention for time-series cross-section data, our basic model is t h e fixed-effects model, which entails a dichotomous d u m m y variable for each city and year, except the first y e a r and city, to avoid perfect collinearity (Hsiao, 1986, pp. 41-58; Pindyck

9 Zimring et al. (2001) made this very point. In California, for example, there apparently is wide variation in how the state's three strikes law is applied to offenders with second and third strikes. Obviously, despite what the law says, how the sentencing policy is implemented has tremendous implications for any possible crime reducing effects generated by the law.

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216 "STRIKING OUT" AS CRIME REDUCTION POLICY

& Rubinfeld, 1991, pp. 224-226). The y e a r and city dummies are an integral p a r t of the approach because t h e y partially control for omitted or difficult-to-measure variables not entered in the crime rate equations. Specifically, the city dummies control for unobserved factors t h a t remained approximately stable over the study period and t h a t caused crime rates to differ across cities. Examples include demographic characteristics, economic deprivation, criminal gun ownership, and deeply embedded cultural and social norms. The city dummies also control for m e a s u r e m e n t errors in UCR crimes due to reporting differences across cities.

The year dummies control for national events t h a t could raise or lower crime rates in a given y e a r across t h e entire country. For example, the 1994 Crime Control a n d L a w Enforcement A c t - - which contained several major crime-reduction programs including truth-in-sentencing, the federal version of a three strikes law, funds for 100,000 new police officers, expansion of the death penalty, a ban on possession of guns by juveniles, and enhanced penalties for drug offenses and using firearms in c r i m e s - c o u l d have affected crime rates throughout the country. Another example is the emergence and proliferation of crack cocaine in the mid- 1980s, which m a n y scholars have suggested was indirectly respon- sible for dramatic increases in violent crime, especially homicide and robbery, in most American cities during the late 1980s and early 1990s (Blumstein, 1995). Because the analysis includes fixed- effects for both years and cities, the coefficient estimates for t h e t h r e e strikes law variables and specific control variables (discussed below) are based solely on within-city changes over time.

Finally, we followed Ayres and Donahue's (2003) and Marvell and Moody's (1996, 2001) recommendation of including linear- specific time-trend variables for each city. Each of t h e time-trend variables is coded zero for all observations except in a particular city, where it is a simple counter. The trend variables control for trends in a city t h a t depart from national trends captured by the y e a r dummies. They are important because without t h e m the coefficient on the three strikes law variables would simply m e a s u r e w h e t h e r crime rates are higher or lower for the years after t h e law (relative to national trends captured by the y e a r dummies), even if the increase occurred before or well after the law went into effect. The city-specific t r e n d variables, however, do not control for trends t h a t are erratic (e.g., drug m a r k e t and gang activity) or t h a t depart from nationwide trends.

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K O V A N D Z I C , S L O A N , A N D V I E R A I T I S 217

Three Strikes Laws

The laws and their effective dates were obtained from Marvell and Moody (2001), and verified by checking relevant secondary sources (Dickey & Hollenhorst, 1998; Clark, Austin & Henry, 1997; T u r n e r et al., 1995). Because three strikes laws are designed to both deter and incapacitate highly active criminals, and because both of these effects are unlikely to manifest themselves at similar time points, we could not m e a s u r e and evaluate the effects of the laws using a single variable. Instead, we created two separate variables to account for both causal processes.

To capture any d e t e r r e n t effects, we used a post-passage d u m m y variable scored "1" starting the full first y e a r after a law w e n t into effect and "0" otherwise. In the y e a r a law w e n t into effect, t h e variable is the portion of the year remaining after the effective date. The post-passage d u m m y variable allowed us to test for a once-and-for-all d e t e r r e n t effect as prospective strike offenders l e a r n e d about t h e stiffer penalties provided by the laws, most likely through "announcement effects" surrounding passage of t h e laws. 1° If t h r e e strikes law supporters are correct t h a t passage of these laws reduces crime by deterrence, one would expect to see a sudden and persistent drop in crime captured by t h e post-passage d u m m y in the city panel regression. Because the dependent variables in the panel regressions are the n a t u r a l logs of the crime rates, the coefficient on the post-passage d u m m y can be i n t e r p r e t e d as the percent change in crime associated with adoption of t h e l a w - - t h a t is, the law will raise or lower crime, by (for example) 5%. Because it is possible the laws h a d a greater d e t e r r e n t effect in later years as prospective strike offenders learned about the laws through application to other offenders, we also estimated crime models with the post-passage d u m m y variable lagged one year. Although the results are not shown, lagging the post-passage d u m m y variable one y e a r has virtually no impact on the results. That variable might, however, reflect mild incapacitation effects of t h r e e strikes laws, because some offenders would not have received prison sentences prior to the passage of the laws. For example, California's two and three strike laws m a n d a t e t h a t offenders convicted of any second (for the two strike law) or third felony be sentenced u n d e r the law's provisions. Because t h e majority of offenders sentenced u n d e r the laws have been convicted of nonviolent crimes such as burglary, drug

lo O f course, one way t h a t prospective t h r e e s t r i k e s d e f e n d a n t s could avoid t h e additional p e n a l t i e s from s u c h a law would be to move t h e i r criminal activity to a m o r e h o s p i t a b l e j u r i s d i c t i o n ( p r e s u m a b l y one w i t h o u t a t h r e e s t r i k e s law).

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218 "STRIKING OUT" AS CRIME REDUCTION POLICY

possession, and weapons possession (Zimring et al., 2001), it is conceivable t h a t some of t h e less serious offenders would have escaped receiving prison t e r m s in t h e absence of t h e laws (Marvell & Moody, 2002). The laws m a y also have an i m m e d i a t e incapacitative impact by leading potential strike d e f e n d a n t s to plead to g r e a t e r crimes t h a n t h e y would have prior to passage of t h e law (Marvell & Moody, 2001).

While it is therefore conceivable for incapacitative effects to begin immediately, one would not expect t h e m to reach full long- t e r m impact until a substantial portion of strike d e f e n d a n t s begin serving t h e extended portions of t h e i r prison t e r m s due specifically to the t h r e e strikes sentence enhancement. Because most convicted felony offenders with serious prior criminal records would probably have received lengthy prison t e r m s prior to t h e t h r e e strikes laws, these effects would not occur until m a n y years after t h e laws are passed (Clark et al., 1997; King & Mauer, 2001; Kovandzic, 2001; Marvell & Moody, 2001). T h a t most strike defendants would have received prison t e r m s even in the absence of the laws m a y explain w h y Marvell a n d Moody (2001) and others have found no i m m e d i a t e impact on state prison populations. Providing additional support for the claim t h a t most strike defendants would have received prison t e r m s before t h e laws, Kovandzic (2001) found t h a t roughly 80% of those sentenced u n d e r Florida's 1988 h a b i t u a l offender law would have received m a n d a t o r y prison t e r m s even if t h e y h a d been sentenced u n d e r the state's sentencing guidelines. Another 17% fell in a discretionary range and could have received prison terms. Perhaps more noteworthy is Kovandzic's (2001) finding t h a t of the habitual offenders who would have been subject to m a n d a t o r y prison t e r m s in the absence of the habitual offender law, 75.2% would have received prison t e r m s of 3 y e a r s or more, 61% t e r m s of 5 y e a r s or more, and 18% t e r m s of 10 years or more.

Because it is impossible to know exactly when strike defendants would have otherwise been released from prison had they not been sentenced under three strikes provisions, we followed Marvell and Moodys (2001) approach of using a post-passage linear trend variable indicating the number of years since enactment of three strikes legislation. For example, consider a city in California, which passed its law in 1994. In this case, in 1995 the time trend variable is equal to one, in 1996 it is equal to two, in 1997 it is equal to three and so on, until the year 2000 where the time trend variable is equal to six. The post-passage linear trend variable assumes that each year an increasing n u m b e r of strike defendants are serving t h a t portion of their prison term due specifically to the three strikes

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KOVANDZIC, SLOAN, AND VIERAITIS 219

provision, such t h a t a time t r e n d emerges after adoption reflecting a dampening effect on crime that grows progressively stronger over time (at least until the increase in the number of defendants serving extended prison terms under the three strikes laws came to an end). I f the estimated coefficient on the post-passage trend variable were virtually zero, one would conclude that three strikes laws have no incapacitative impact on crime rates.

Crime Rates

The dependent variables are the rates of homicide, robbery, assault, rape, burglary, larceny, and motor vehicle theft, per population of 100,000. The crime data were t a k e n from the FBI's Uniform Crime Reports (1981-2001), which reports crime counts for a city only if the individual law enforcement agency responsible for t h a t jurisdiction submits 12 complete monthly reports. D e s p i t e having a population greater t h a n 100,000 in 1990, we dropped seven cities due to missing data problems: Moreno Valley, CA, Rancho Cucamonga, CA, Santa Clarita, CA, Overland Park, KS, Kansas City, KS, Cedar Rapids, IA, and Lowell, MA.

Specific Control Variables

In addition to the y e a r dummies, city dummies, and city-trend variables, we included eight specific control variables t h a t prior macro-level research has suggested are important correlates of crime (see Kovandzic et al., 1998; Land, McCall, & Cohen, 1990; Sampson, 1986; Vieraitis, 2000). Most account for causal processes emphasized by strain/deprivation, social disorganization, and opportunity/routine activity theories. Failure to control for these factors could suppress (i.e., mask any negative impact of three strikes laws on crime) or lead to spurious results if t h e y are corre- lated with the passage of three strike laws and with crime rates.

The specific control variables in the crime rate models included percent of the population t h a t was African American, percent t h a t was Hispanic, percent aged 18-24 and 25-44, percent of households headed by females, percent of persons living below t h e poverty line, percent of the population living alone, per capita income, and incarceration rate. These data for 1980 and 1990 were obtained from U.S. B u r e a u of the Census (U.S. Bureau of the Census, 1983, 1994). Year 2000 data were obtained from the U.S. Census B u r e a u website using American Fact Finder (http://factfinder.census.gov). Because these m e a s u r e s were available only for decennial census years, we used linear interpolation estimates between decennial census years. Given the

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220 "STRIKING OUT" AS CRIME REDUCTION POLICY

small changes in these variables, a linear t r e n d was assumed and considered justified. Income data for 1980-2000 were obtained from the U.S. D e p a r t m e n t of Commerce's Bureau of Economic Analysis website (http://www.bea.doc.gov). Income data were county-level estimates t h a t we used as imperfect substitutes for city-level income. Personal income data were converted from a c u r r e n t dollar estimate to a constant-dollar 1967 basis by dividing per capita income by the consumer price index (CPI). Prison population was the n u m b e r of inmates sentenced to state institutions for more t h a n a y e a r divided by state population, available annually at the state level; these values were used as proxies for city-level imprisonment. State prison population data were obtained from the Bureau of Justice Statistics website (http://www.ojp.usdoj.gov/bjs). Because the prison population data were year-end estimates we took the average of the c u r r e n t y e a r and prior years to estimate mid-year prison population.

Data Transformations and Regression Assumptions

All continuous variables were expressed as n a t u r a l logs to reduce the impact of outliers and divided by population figures to avoid having large cities dominate t h e results. This procedure allowed coefficients for the continuous variables to be interpreted as elasticities--the percent change in the crime rate expected from a 1% change in the independent variable (see Greene, 1993). With respect to the dichotomous and post-passage linear t r e n d variables, exponentiating the variables and subtracting the result from 100 produced t h e useful interpretation of the percent change in the crime rate associated with the passage of a three strikes law and the percent change in the crime rate for each additional year the law is in effect, respectively (see Wooldridge, 2000). Hetero- scedasticity was detected using the Breusch-Pagan test, mainly because variation in crime rates was greater over time in the smaller cities t h a n in the larger ones. To avoid inefficient and biased estimated variances for the p a r a m e t e r estimates, we weighted the crime models by functions of city population as determined by the test (Breusch & Pagan, 1979). Results of panel- unit-root-tests (Levin & Lin, 1992; Wu, 1996) indicated t h a t the crime rate series were stationary, i.e., t h e unit root hypothesis was rejected in all instances. That the crime rate variables had a constant mean suggested t h a t the analysis be conducted in levels and not differenced rates. In any event, we reestimated the crime rate models using differenced rates and t h e p a r a m e t e r estimates for t h e three strikes law variables were similar to those in Table 1. Autocorrelation was mitigated by including lagged dependent

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K O V A N D Z I C , S L O A N , A N D V I E R A I T I S 221

variables (Hendry, 1995); lagged dependent variables also have the added benefit of controlling for omitted lagged effects (Moody, 2001). The results for the three strike variables were essentially t h e same without them. Examination of collinearity diagnostics developed by Belsley, Kuh, and Welsh (1980) revealed no serious collinearity problems for the three strike variables. While t h e r e were collinearity problems among the proxy variables, this did not impact the results for the three strikes variables, and we measured only the significance of proxy variables in groups using the F test.

R E S U L T S

Crime Trends Before and After Implementing Three Strikes Laws

Before proceeding to results of the more sophisticated econometric analysis, we began our empirical investigation of the effect of three strikes laws on crime by graphing t h e p a t t e r n of index crime rates (per 100,000 population) over time in three groups of cities: those in states t h a t adopted a t h r e e strikes law in 1994, those in states t h a t adopted t h e laws in 1995, a n d those in states t h a t never adopted them. 11 As discussed, if passage of a t h r e e strikes law reduces crime primarily through deterrence, presumably through a n n o u n c e m e n t effects, one would expect cities in states with the laws to experience a more sudden and persistent drop in crime t h a n t h a t in cities in states without the laws. On t h e other hand, if t h r e e strike laws reduce crime mainly through incapacitation, one might expect cities in states with t h e law to experience a more gradual and continuing decrease in crime t h a n t h a t in cities in states without the laws as offenders in three strikes cities begin serving the extended portion of their prison terms due to sentence enhancement.

Analysis reveals a number of interesting findings (see Figure 1). First, crime rates in all three city groupings moved roughly in t a n d e m over the past 20 years: crime rates declined in the early 1980s, began rising in the mid-1980s, and then declined markedly through the 1990s. This pattern indicates broad forces t h a t tended to push crime rates up and down nationwide. Second, despite all three city groupings having experienced a sizeable drop in crime throughout the 1990s, crime rates in three strikes cities declined slightly faster. Because the drop in crime grows gradually over time

11 B e c a u s e W a s h i n g t o n a d o p t e d its t h r e e s t r i k e s law i n l a t e 1993 ( D e c e m b e r 1993), we decided to i n c l u d e S e a t t l e , S p o k a n e , a n d T a c o m a i n t h e 1994 g r o u p i n g of cities. S i m i l a r l y , we decided to i n c l u d e A n c h o r a g e , A l a s k a i n t h e 1995 g r o u p i n g of cities since t h e law w a s a d o p t e d i n e a r l y 1996 ( M a r c h , 1996).

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KOVANDZIC, SLOAN, AND VIERAITIS 223

r a t h e r than abruptly, it appears t h a t incapacitation is the main force behind three strikes laws. As a result, if one were forced to make causal attributions based on Figure 1, one might conclude t h a t three strikes laws tend to reduce crime rates through incapacitation.

Of course, one cannot place much confidence in such a conclusion because the evidence in Figure 1 assumes t h a t the only unique factor working to influence crime in three strikes cities is the t h r e e strikes law. As discussed, prior macro-level crime theory and research have identified numerous correlates of crime. I f any of these factors were correlated with both the laws and with lower crime, t h e n the apparent causal relationship between the laws and crime observed in Figure 1 would be spurious. For example, states t h a t enacted three strikes laws m a y have also relied more heavily on incarceration as part of a larger effort to "get tough on crime," such t h a t their prison populations grew faster t h a n in other states. If this was the case, t h e n the apparent incapacitative effects noted in Figure 1 might really be due to an overall increase in prison populations, for which the graph does not control. Because crime rates in all t h r e e city groupings began declining well before the passage of most t h r e e strikes laws in 1994 and 1995 this seems like a logical possibility. We therefore now t u r n to regression analysis to examine the d e t e r r e n t and incapacitative impact of t h r e e strike laws on crime while controlling for n u m e r o u s potential confounding factors.

Estimating the Impact of Three Strikes Laws

Estimates of the aggregate impact of three strikes laws on city crime rates using the described regression procedures are presented in Table 1. The major features include using aggregate post-passage d u m m y and post-passage t r e n d variables, loga- rithmically transformed rates for all continuous variables, city dummies, year dummies, and city-trend dummies. The use of the aggregate law variables implicitly assumes the laws have a uniform impact on crime, which t u r n s out not to be the case given the large n u m b e r of negative and positive coefficients found for the disaggregated law variables (see state-specific analysis below). The results in Table 1 do not support what was shown in Figure 1, t h a t three strikes laws were associated with slightly lower crime rates, most likely due to incapacitation. Although six of the seven post- passage trend variables are, as expected, negative and therefore consistent with the hypothesis that three strike laws reduce crime through incapacitation, the coefficients are small and not close to statistically significant, even at the generous .10 level. Given the large n u m b e r of degrees of freedom (D.F. = 3,320 or more in each

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K O V A N D Z I C , S L O A N , A N D V I E R A I T I S 225

model), even m o d e s t incapacitative effects should h a v e produced significant negative coefficients for t h e post-passage t r e n d variable.

The m o s t likely r e a s o n for t h e d i s p a r a t e results b e t w e e n F i g u r e 1 a n d Table I is prison population, which is associated w i t h statistically significant lower r a t e s in five of the seven crime categories. To e x a m i n e this possibility f u r t h e r , we re-ran t h e crime regressions from Table 1 w i t h o u t t h e prison population variable. The r e s u l t s confirmed our initial suspicions t h a t prison population g r o w t h was largely responsible for t h e small incapacitation effects observed in Figure 1. A l t h o u g h n o t shown, t h e coefficients for t h e post-passage t r e n d variables were negative a n d statistically significant for robbery a n d larceny (the bulk of t h e index crime rate) a n d m a r g i n a l l y significant for homicide, burglary, a n d auto theft. These findings s u p p o r t t h e supposition t h a t states a d o p t i n g t h r e e strikes laws were t h e s a m e ones relying more heavily on incarceration as a crime-control s t r a t e g y d u r i n g t h e " i m p r i s o n m e n t binge" of t h e 1980s a n d 1990s. The finding t h a t prison population g r o w t h reduces crime is consistent w i t h a sizable body of research showing t h a t incarcerating criminals reduces crime, especially homicide (Devine, Sheley, & Smith, 1988; Kovandzic et al., 2002; Levitt, 1996; Marvell & Moody, 1994, 1997, 1998, 2001).

T h e r e is also no evidence t h a t t h r e e strikes laws reduce crime t h r o u g h deterrence. The coefficients for t h e post-passage d u m m y are about evenly divided by sign a n d are far from significant, except for homicide, whose coefficient is positive a n d significant. T h e s e p a r t i c u l a r results suggest t h a t homicide r a t e s in cities increase, on average, by 10.4% after a t h r e e strikes law is adopted. 12 This finding is c o n s i s t e n t w i t h results r e p o r t e d by Kovandzic et al. (2002) a n d Marvell a n d Moody (2001). The m o s t likely explanation is t h a t a few criminals, facing l e n g t h y prison t e r m s on conviction for a t h i r d strike, m a y a t t e m p t to avoid such penalties by killing victims, witnesses, or police officers to reduce t h e i r c h a n c e s of a p p r e h e n s i o n a n d conviction.

Robustness Checks

Additional analyses (not r e p o r t e d in Table 1) indicated t h a t t h e nonsignificant effects of t h r e e strikes laws on crime r a t e s a p p e a r to be fairly r o b u s t u n d e r v a r y i n g model specifications. T h a t is, t h e r e s u l t s for both variables were fairly consistent u n d e r a l t e r n a t i v e analyses with o t h e r possible model specifications a n d regression procedures. T h e s e included e n t e r i n g t h e t h r e e strikes law variables in t h e crime regressions separately r a t h e r t h a n simultaneously,

12 TO calculate t h i s p e r c e n t a g e we u s e d t h e a p p r o x i m a t i o n 100 * [exp (5) - 1].

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226 "STRIKING OUT" AS CRIME REDUCTION POLICY

using differenced rates, dropping the city-trend variables, not logging the continuous variables, not weighting the crime regressions, dropping t h e lagged dependent variables, and using conventional standard errors. The major exception occurs for homicide, where the coefficient on the post-passage dummy variable in the homicide regression is no longer significant when using differenced rates and is highly significant when using conventional s t a n d a r d errors.

Other Notable Findings

Although not the focus of this study, results for some of the control variables should be noted (Table 1). First, increases in the percentage of a citys population t h a t is African American or Hispanic appear positively associated with property crime rates but has little impact on rates of violence. Second, prison population growth is negatively associated with crime rates, though the coefficients are somewhat smaller than those found in other state and national studies (Marvell & Moody, 1994, 1997; Levitt, 1996). As expected, increases in the number of persons in a city between the ages 18 to 24 are positively related to rates of homicide, robbery, and larceny. Our results contradict recent works by Levitt (1999) and Marvell and Moody (2001) which concluded t h a t age structure changes have little impact on crime rate trends. Per capita income appears positively associated with rates of homicide, rape, and auto theft. This finding is inconsistent with theoretical expectations, but mirrors findings reported by other studies (Marvell & Moody, 1995; Lott & Mustard, 1997). Finally, the number of families headed by females is positively associated with homicide rates. To our knowledge, this is the first time this variable has been related to cross-temporal variation in homicide rates.

Is A d o p t i n g a Three Strikes L a w Endogenous?

One possible explanation for the lack of impact of three strikes laws on crime rates is simultaneity, which can happen if unusual increases in crime lead policy makers to enact three strikes laws. In other words, adopting and applying three strikes laws m a y be endogenous to the crime rate. I f simultaneity does occur, the coefficients on the three strikes law variables would be biased, most likely positively, and mask any crime-reduction impact of the laws.

The most common procedure used to address potential endogeneity problems in evaluations of legal interventions is two- stage least squares (2SLS) regression. As Marvell and Moody (1996) a n d others (Kennedy, 1998) have noted, the problem with

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KOVANDZIC, SLOAN, AND VIERAITIS 227

2SLS is t h a t it requires a t least one identifying r e s t r i c t i o n - - a t least one variable t h a t is strongly correlated with t h e endogenous explanatory variable (i.e., adoption of three strikes laws), is uncorrelated with the error t e r m in the crime r a t e equation and does not conceptually belong in the crime equation, or is a proxy for a variable t h a t should be in the crime rate equation. These r e q u i r e m e n t s are extremely difficult to satisfy, mainly because the i n s t r u m e n t s cannot be considered convincingly exogenous or are only weakly correlated with the endogenous explanatory variable.

Perhaps the easiest way to test w h e t h e r t h r e e strikes laws have been adopted in response to u n u s u a l increases in crime is to simply exclude from the model specifications the years immediately before t h e laws were adopted. If an upward t r e n d in crime is responsible for the law, then dropping these years from the model specifications should produce significant negative coefficients for t h e law variables. To examine this possibility, we excluded observations of t h e 3 years prior to the adoption of the laws but included the y e a r of the adoption (it is unlikely t h a t current-year crime could impact crime legislation contem- poraneously). The results of this estimation procedure for all seven UCR crimes are presented in Table 2, but to conserve space only t h e coefficients for the three strike law variables are presented.

The coefficients on the three strikes law variables reported in Table 2 are roughly identical to those reported in Table 1, which indicates t h a t the lack of significant results for the t h r e e strikes law variables in Table 1 is not the result of abnormal crime spikes in the years immediately before a t h r e e strikes law was adopted. We also tried dropping 2 years prior to the passage of a law and obtained similar estimates. Simultaneity also seems to be ruled out by Figure 1, because there is no evidence t h a t crime rates were growing faster (or declining more slowly) in three strike cities. In fact, Figure 1 suggests t h a t crime rates were actually declining slightly faster in three strikes cities t h a n in others immediately before the adoption of most three strikes laws in 1994 and 1995. Thus, t h e r e is no statistical evidence t h a t policy m a k e r s passed t h r e e strikes laws because crime rates in their states were rising more quickly, or declining more slowly, t h a n in other states. This finding is not surprising given t h a t the public and policy makers respond mostly to news accounts of highly publicized crimes (e.g., Polly Klaas), which in t u r n are uncorrelated with actual or official crime rates (Kappeler, Blumberg, & Potter, 1996; McCorkle & Miethe, 2002; Surette, 1998).

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228 " S T R I K I N G O U T " A S C R I M E R E D U C T I O N P O L I C Y

T a b l e 2. T h r e e S t r i k e s L a w V a r i a b l e s W i t h O b s e r v a t i o n s F r o m 3 Y e a r s P r i o r t o t h e A d o p t i o n o f T h r e e S t r i k e s L a w E x c l u d e d

T h r e e S t r i k e s L a w V a r i a b l e s

P o s t - P a s s a g e D u m m y P o s t - L a w L i n e a r T r e n d

D e p e n d e n t V a r i a b l e Coef. t Coef. t

Homicide .2_! 3.01 -.00 -.11

Rape .06 1.69 .01 .85

R o b b e r y .0_99 2.24 -.01 -.78

A s s a u l t .05 1.49 -.00 -.40

B u r g l a r y .06 1.68 .00 .12

L a r c e n y .05 1.89 -.07 -1.37

Auto T h e f t .01 .21 -.00 -.41

Notes: T h i s t a b l e p r e s e n t s t h e r e s u l t s of c r i m e r e g r e s s i o n s w i t h o b s e r v a t i o n s for t h e t h r e e y e a r s p r i o r to t h e a d o p t i o n of a t h r e e s t r i k e s law excluded. Only t h e r e s u l t s for t h e t h r e e s t r i k e s law v a r i a b l e s a r e p r e s e n t e d . T h e c o n t r o l v a r i a b l e s are s i m i l a r to t h o s e u s e d i n Table 1. S t a n d a r d e r r o r s are c o r r e c t e d for c l u s t e r i n g . Coefficients t h a t are s i g n i f i c a n t a t t h e .10 level a r e italicized. Coefficients t h a t are s i g n i f i c a n t a t t h e .05 level a r e b o t h italicized a n d u n d e r l i n e d .

Estimating State-Specific Effects of Three Strikes Laws on Crime Rates

T h e r e is little evidence in t h e r e s u l t s p r e s e n t e d in T a b l e 1 to s u p p o r t t h e claim t h a t t h r e e s t r i k e s l a w s r e d u c e crime r a t e s t h r o u g h e i t h e r d e t e r r e n c e or incapacitation. H o w e v e r , t h e r e g r e s s i o n s s h o w n in T a b l e I e s t i m a t e d a n aggregated effect for t h e l a w s a c r o s s all cities in t h r e e s t r i k e states. If, for e x a m p l e , t h e i m p a c t of t h e l a w s on crime r a t e s v a r i e s significantly across s t a t e s , t h e n t h e model p r e s e n t e d is misspecified. Moreover, as noted, t h e d a n g e r s of e s t i m a t i n g a single a g g r e g a t e d effect a r e p a r t i c u l a r l y a c u t e in t h i s case b e c a u s e of v a s t differences in, first, t h e c o n t e n t s of t h r e e s t r i k e s legislation across t h e s t a t e s (e.g., w h a t c o n s t i t u t e s a "strike" as well as p r o s e c u t o r i a l a n d j u d i c i a l discretion in a p p l y i n g t h e laws, see C l a r k e t al., 1997); second, p u b l i c i t y s u r r o u n d i n g p a s s a g e o f t h e laws; and, third, t h e application o f t h e l a w s in practice.

O n e w a y to avoid a g g r e g a t i o n b i a s is to c h a n g e t h e m o d e l specification to e s t i m a t e a state-specific effect for e a c h s t a t e a d o p t i n g a t h r e e s t r i k e s law. In o t h e r words, one w o u l d include in t h e p a n e l d a t a r e g r e s s i o n s for each crime c a t e g o r y a s e p a r a t e post- p a s s a g e d u m m y a n d p o s t - p a s s a g e linear t r e n d v a r i a b l e for e a c h g r o u p o f cities in a t h r e e s t r i k e s s t a t e . T h e s e e s t i m a t e s for all s e v e n index crime c a t e g o r i e s a r e p r e s e n t e d in Table 3, w h i c h s h o w s t h a t t h e coefficients on t h e p o s t - p a s s a g e d u m m y and p o s t - p a s s a g e t r e n d v a r i a b l e s e p a r a t e l y e s t i m a t e t h e d e t e r r e n t a n d i n c a p a c i t a t i v e

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KOVANDZIC, SLOAN, AND VIERAITIS 229

effects of t h r e e strikes laws for each of the 25 states t h a t passed t h e laws between 1993 and 1996.

Results presented in Table 3 reject t h e more constrained specifications of the aggregate regressions, which implicitly assumed t h a t the impact of three strikes laws was constant across jurisdictions. Indeed, for each crime type, we were able to reject the hypothesis t h a t the 21 post-passage dummies and 21 post-passage t r e n d variables were essentially equal. This suggests t h a t the panel data regressions presented in Table 1, which assumed uniform impacts for all three strikes cities, are too restrictive. With the exception of homicide and auto theft, t h e coefficients on the post-passage d u m m y variables from the disaggregated analysis suggest t h a t the n u m b e r of states experiencing a statistically significant decrease in crime after adopting three strikes law is roughly identical to the n u m b e r experiencing a statistically significant increase (see Table 3). For example, for robbery, six states saw a decrease and four an increase. For homicide, the disparity was nine to three. For auto theft, the numbers were nine and five. Of the 147 estimated impacts of the law on crime rates (21 states by seven crime categories), 42 represented statistically significant decreases in crime on passage of the laws and 44 represented statistically significant increases. Overall, Table 3 shows 73 decreases and 74 increases in crime.

Results from the disaggregated analysis for the post-passage t r e n d variables also suggest substantial h e t e r o g e n e i t y in the laws' impact on city crime r a t e s over time. For every crime type, the n u m b e r of states experiencing statistically significant decreases in crime r a t e s over time was roughly equivalent to the n u m b e r of states experiencing significant increases. Specifically, out of 147 e s t i m a t e d impacts on crime over time, 54 exhibited statistically significant decreases and 43 exhibited statistically significant increases. Overall, t h e results for the state-specific post-passage t r e n d variables indicate 76 decreases and 71 increases (Table 3).

The n e t 5-year d e t e r r e n t and incapacitative impact of three strikes laws on crime rates for each state are reported in Table 4. To calculate t h e n e t 5-year impact, it is necessary to add t h e coefficients on t h e post-passage d u m m y a n d post-passage t r e n d

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232 "STRIKING OUT" AS CRIME REDUCTION POLICY

v a r i a b l e s f o r i n d i v i d u a l y e a r s a n d t h e n s u m t h e y e a r l y i m p a c t s . TM

E s t i m a t e s o f t h e 5 - y e a r i m p a c t s o f t h r e e s t r i k e s l a w s o n c r i m e

r e v e a l t h a t o n l y o n e s t a t e ( A r k a n s a s ) s h o w s a n e t 5 - y e a r d e c r e a s e

i n a l l s e v e n c r i m e c a t e g o r i e s w i t h o u t s h o w i n g a s t a t i s t i c a l l y

s i g n i f i c a n t i n c r e a s e i n a n o t h e r c r i m e c a t e g o r y . T h r e e s t a t e s

( C a l i f o r n i a , L o u i s i a n a , a n d N e w J e r s e y ) s h o w a s t a t i s t i c a l l y

s i g n i f i c a n t d e c r e a s e i n f o u r o r m o r e c r i m e c a t e g o r i e s , b u t a

s t a t i s t i c a l l y s i g n i f i c a n t i n c r e a s e i n a t l e a s t o n e c r i m e c a t e g o r y

a s w e l l .

W h i l e i t w o u l d b e t e m p t i n g t o c o n c l u d e t h a t t h r e e s t r i k e s l a w s

a r e r e s p o n s i b l e f o r t h e m a j o r i t y o f t h e c r i m e d r o p i n t h e s e s t a t e s ,

e s p e c i a l l y i n C a l i f o r n i a , w h e r e t h r e e s t r i k e p r o v i s i o n s a r e a p p l i e d

q u i t e f r e q u e n t l y , o n e m u s t a c c o u n t f o r t h e f a c t t h a t t h e r e s u l t s f o r

s o m e l a w s a r e p r o b a b l y n o t h i n g m o r e t h a n r a n d o m a r t i f a c t s o r a r e

p r o x i e s f o r o t h e r c o n t e m p o r a n e o u s c h a n g e s t a k i n g p l a c e a r o u n d

t h e a d o p t i o n o f a t h r e e s t r i k e s l a w , n o t e x p l i c i t l y c o n t r o l l e d f o r i n

t h e m o d e l s p e c i f i c a t i o n s . M o r e o v e r , i f o n e is w i l l i n g t o c o n c l u d e

f r o m T a b l e 4 t h a t t h e l a w s r e d u c e c r i m e i n t h e s e s t a t e s t h e n o n e

h a s t o a t l e a s t e n t e r t a i n t h e p r o s p e c t t h a t t h e l a w s a l s o l e a d t o

l a r g e c r i m e i n c r e a s e s a s w e l l . T a k e , f o r e x a m p l e , N e v a d a a n d

P e n n s y l v a n i a , w h i c h e x p e r i e n c e d l a r g e s t a t i s t i c a l l y s i g n i f i c a n t

i n c r e a s e s i n c r i m e f o l l o w i n g t h e a d o p t i o n o f a t h r e e s t r i k e s l a w .

U n l e s s o n e i s w i l l i n g t o c o n c l u d e t h e l a w s h a v e h a d t h e u n i n t e n d e d

c o n s e q u e n c e o f i n c r e a s i n g c r i m e i n t h e s e s t a t e s , t h e n o n e c a n n o t

s i m p l y s e l e c t t h e s t a t e s t h a t s e e m t o do w e l l u n d e r t h e l a w a n d

c o n c l u d e t h a t t h e l a w s w o r k t o r e d u c e c r i m e . T h a t is, o n e c a n n o t

c h e r r y - p i c k t h o s e s t a t e s t h a t a p p e a r t o b e n e f i t f r o m t h e p a s s a g e o f a t h r e e s t r i k e s l a w a n d i g n o r e s t a t e s w h e r e t h e l a w s a p p e a r t o

h a v e a d e l e t e r i o u s i m p a c t o n c r i m e .

13 The predicted impact of a law for individual years is: Year 1: 1*beta(post-passage dummy for cities in state X) + 1*beta(post- passage trend for cities in state X) Year 2: 2*beta(post-passage dummy for cities in state X) + 2*beta(post- passage trend for cities in state X) Year 3: 3*beta(post-passage dummy for cities in state X) + 3*beta(post- passage trend for cities in state X) Year 4: 4*beta(post-passage dummy for cities in state X) + 4*beta(post- passage trend for cities in state X) Year 5: 5*beta(post-passage dummy for cities in state X) + 5*beta(post- passage trend for cities in state X)

Where: beta (post-passage dummy) and beta (post-passage trend) represent the estimated coefficients on the post-passage dummy and post-passage trend variables. Summing the individual year impacts, we were able to calculate a net five-year impact as: beta (post-passage dummy for cities in state X) + 3*beta (post-passage trend for cities in state X). We also tested whether this linear combination of regression coefficients was significantly different from zero and report results of this testing in Table 3.

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K O V A N D Z I C , S L O A N , A N D V I E R A I T I S 2 3 3

T u r n i n g now to t h e i n d i v i d u a l crime categories t h e m s e l v e s ,

t h e r e does n o t a p p e a r to be a s t r o n g correlation b e t w e e n t h e p a s s a g e of a t h r e e s t r i k e s law a n d a decrease in a n y i n d i v i d u a l crime category. I n m o s t cases t h e n u m b e r of s t a t e s t h a t exhibited a

T a b l e 4. S t a t e - S p e c i f i c A n n u a l i z e d 5 - Y e a r I m p a c t o f T h r e e S t r i k e s L a w s O n U C R I n d e x C r i m e R a t e s .

A u t o Aggr. B u r g l a r y L a r c e n y T h e f t Homicide Rape R o b b e r y A s s a u l t

A l a s k a -13.0% 5.5% -30.1% -8.9% -6.5% -4.8% -13.7%

A r k a n s a s -35.8% -9.3% -29.3% -48.8% -15.5% -16.7% -17.7%

C a l i f o r n i a -1.5% 14.7% -12.3% -5.2% -9.1% -6.2% -21.6%

Colorado 1.7% 19.8% 1.5% -11.2% 3.9% 1.4% 4.6%

C o n n e c t i c u t -12.0% -13.3% -.6% -.2% -17% 2.2% -10.9%

F l o r i d a 20.8% 3.3% -4.9% 4.5% -4.0% -6.8% -6.9%

G e o r g i a 16.6% -.2% 5.9% 15.5% 3.9% -3.7% 6.9%

I n d i a n a 24.8% -8.5% 4.7% -13.4% 3.5% -2.0% .3%

K a n s a s 22.4% 3.1% -23.4% 12.1% -18.7% -.8% -11.8%

L o u i s i a n a -4.7% 26.1% -14.8% -13.1% -9.5% -3.4% -9.7%

M a r y l a n d 23.0% -3.9% -.4% 20.9% -3.6% -1.3% -19.6%

N e v a d a 57.3% 17.1% 19.7% 4.1% 22.2% 3.2% 26.6%

N e w J e r s e y 34.8% -17 6% -19. 0% -.3% -22.2% -13.2% -8.4%

N e w Mexico 8.5% 22.8% 17.1% -20.9% .1% 8.9% 21.5%

N o r t h C a r o l i n a -6.0% -11.1% -12.1% 12.2% -3.6% .3% 26.2%

P e n n s y l v a n i a 26.1% 20.6% 9.7% 27.2% 3.2% 4.3% 7.8%

T e n n e s s e e 12.1% 5.8% 3.8% -4.1% 1.3% 5.1% 2.7%

U t a h 12.6% -4.7% 33.0% 41.6% 11.1% 3.3% 23.0%

V i r g i n i a -3.7% -14.2% -1.2% 6.8% 6.0% -4.1% -3.1%

W a s h i n g t o n 6.7% -5.1% 5.2% -8.2% 14.4% .5% 17.6%

W i s c o n s i n 9.8% -15.9% 7.2% 45.4% 14.2% 8.9% -10.5%

S u m m a r y of 5-Year Effects

N e g a t i v e & 1 8 7 6 6 6 9

S i g n i f i c a n t

N e g a t i v e & n o t 6 3 4 5 4 5 2

s i g n i f i c a n t

P o s i t i v e & 8 6 7 9 4 4 6

s i g n i f i c a n t

Positive & n o t 6 4 3 1 7 6 4

s i g n i f i c a n t

N o t e s : T h e d e p e n d e n t v a r i a b l e is t h e n a t u r a l log of t h e c r i m e r a t e l i s t e d a t t h e t o p of e a c h column. T h e d a t a s e t is c o m p r i s e d of a n n u a l city-level o b s e r v a t i o n s . While n o t shown, city, year, a n d city t r e n d effects a r e i n c l u d e d i n all specifications. All r e g r e s s i o n s a r e w e i g h t e d b y a f u n c t i o n of city p o p u l a t i o n as d e t e r m i n e d b y t h e b r e u s c h p a g a n t e s t . S t a n d a r d e r r o r s a r e c o r r e c t e d for c l u s t e r i n g b y s t a t e . Coefficients t h a t a r e s i g n i f i c a n t a t t h e .10 level a r e u n d e r l i n e d . Coefficients t h a t a r e s i g n i f i c a n t a t t h e .05 level a r e italicized, coefficients t h a t a r e s i g n i f i c a n t a t t h e .01 level a r e i t a l i c i z e d a n d u n d e r l i n e d .

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234 "STRIKING OUT" AS CRIME REDUCTION POLICY

statistically significant decrease in any individual crime category was roughly identical to the n u m b e r of states t h a t exhibited a statistically significant increase. The greatest disparity between significant increases and decreases occurs for homicide, with eight states showing a statistical increase in homicide and only one reporting a statistical decrease. Overall, 72 of the 147 tests indicate t h a t t h r e e strikes laws reduced crime, with 29 of these estimates being statistically significant (at the .05 level). At t h e same time, 31 of t h e 147 estimated n e t 5-year effects indicated a statistically significant increase in crime, resulting in a ratio of about one crime decrease for every one increase.

D I S C U S S I O N A N D C O N C L U S I O N

Consistent with other studies, ours finds no credible statistical evidence t h a t passage of three strikes laws reduces crime by deterring potential criminals or incapacitating repeat offenders. The results of the aggregate law variable analysis provided no evidence of an immediate or gradual decrease in crime rates, and homicide rates were actually positively associated with the passage of three strike laws. The findings for the state-specific analysis were mixed, with some states showing increases in some crimes, and others showing decreases. Overall, 29 of the 147 tests were negative and significant, indicating t h a t t h r e e strikes laws reduced crime, while 31 demonstrated a statistically significant increase in crime.

We offer several possible explanations for why passage of three strikes laws does not appear to be negatively correlated with crime rates. First, ethnographic research on criminals (Hochstetler & Copes, 2003; Jacobs, 1999; Shover, 1996; Wright & Decker, 1994, 1997) suggests t h a t rarely are they concerned about getting caught (i.e., they are confident in their ability to commit crime or they can successfully manage any fear), or they simply aren't aware of the laws or the way in which the laws operate (Marvell & Moody, 1995; Kovandzic, 2001). In addition, m a n y offenders are u n d e r the influence of alcohol and/or drugs (U.S. D e p a r t m e n t of Justice, 2003) and this m a y serve to lessen their concerns with getting caught (Shover & Honaker, 1999). Second, as Stolzenberg and D'Alessio (1997) suggest, the laws frequently target offenders beyond t h e peak age of offending, and thus, t h e impact on crime is minimal because t h e y are already committing fewer crimes. In addition, the effectiveness of three strikes laws for reducing crime rates depends on the ability of the system to identify potential high-rate offenders before they commit a large n u m b e r of crimes. This would entail incarcerating youthful offenders because the

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peak ages for offending are between the ages of 15 and 24. However, it is incredibly difficult to predict which offenders are most likely to become career criminals. Moreover, the vast majority of youthful offenders stop their criminal behavior on their own, without imprisonment (Clear, 1996). Third, the ability of in- capacitation to reduce crime is also limited by the possibility t h a t offenders are simply replaced by other offenders. To the extent t h a t t h e social conditions in which crime occurs r e m a i n t h e same, there will likely be a ready supply of motivated potential offenders to replace those removed through incarceration. Moreover, a large percentage of crime, particularly drug crimes and robbery, is committed by offenders acting in groups (Reiss, 1988). Incarcerating one of a group of co-offenders m a y not end t h e group's criminal behavior because it persists with one less member or simply replaces t h a t member with another (Clear, 1996).

Fourth, the failure of three strikes laws to reduce crime m a y be explained by the fact t h a t most offenders were receiving enhanced penalties prior to passage of the laws. Three strikes laws would thus not have a significant effect on crime rates simply because t h e y did not raise t h e severity of p u n i s h m e n t appreciably (Stolzenberg & D'Alessio, 1997). Fifth, some would argue t h a t the laws do not reduce crime because they are not enforced, are not severe enough, or both. The results of t h e state-level analysis (see Table 4) show mixed results in crime rate trends between states t h a t apply the law frequently or have severe laws versus states t h a t apply the law less frequently or have less severe laws. For example, California's law, which is severe a n d frequently enforced, exhibits an incapacitation effect on six out of seven crimes. However, in Georgia, also identified as a state with a severe and frequently enforced t h r e e strikes law, t h e r e was an increase in crime in five out of seven categories. As we will discuss, this possibility is best tested with methodologies other t h a n those used in this study.

Given our findings and the sophistication of the methodology, as well as results of studies by Marvell and Moody (2001) and Kovandzic et al. (2002), policy makers should reconsider the costs and benefits associated with three strikes laws. Although the laws have failed to produce w h a t is arguably one of the most important benefits, a reduction in crime, researchers have identified n u m e r o u s costs associated with three strikes and other habitual offender laws. These include the racial disparity in their application (Crawford, Kleck, & Chiricos, 1998; Males & Macallair, 1999); the financial costs of increased trials (as offenders opt to take t h e i r chances with juries; Cushman, 1996), of building a n d

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236 " S T R I K I N G O U T " A S C R I M E R E D U C T I O N P O L I C Y

staffing prisons (Austin, 1996; Greenwood et al., 1994) a n d of providing medical care to aging prisoners (King & Mauer, 2001); and, p e r h a p s m o s t costly, t h e potential increase in homicide r a t e s as offenders a t t e m p t to avoid s t r i k i n g o u t by e l i m i n a t i n g potential witnesses (Kovandzic et al., 2002; Marvell & Moody, 2001).

Despite t h e growing body of empirical work e x a m i n i n g t h e effects on crime a n d other social p h e n o m e n a of t h r e e strikes laws, researchers should continue to explore this topic, especially in light of t h e continual advances in r e s e a r c h methodology. I n addition, r e s e a r c h e r s should use qualitative m e t h o d s to explore t h e law in action in various jurisdictions because t h e r e is comparatively little i n f o r m a t i o n from jurisdictions outside of California. Considering our finding t h a t t h e laws r e d u c e d crime in some states, a more comprehensive analysis (e.g., publicity of t h e law, offenders' perspectives, prosecutorial a n d judicial discretion) of w h a t is going on in those p a r t i c u l a r states can provide i n f o r m a t i o n t h a t should help to establish w h a t is or is n o t w o r k i n g a n d why. Interviews w i t h offenders w o u l d f u r t h e r our u n d e r s t a n d i n g of t h e possible d e t e r r e n t effects of t h r e e strikes laws by assessing offenders' levels of a w a r e n e s s of, behavioral responses to, a n d t h e i r experiences w i t h t h e laws. Research on prosecutors could g e n e r a t e valuable i n s i g h t into how frequently t h e law is u s e d a n d how it is used, e.g., as a plea b a r g a i n i n g tool. A l t h o u g h t h r e e strikes laws were d e s i g n e d in p a r t to limit judicial discretion, t h e r e is still a r a n g e of possible sentences w i t h i n t h e guidelines. Thus, interviews w i t h j u d g e s r e g a r d i n g how t h e y exercise discretion should also contribute to our u n d e r s t a n d i n g of t h e law in action.

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