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Stewart J. D'Alessio, Lisa Stolzenberg and W. Clinton Terry, III Cellular Telephone Program on Alcohol-Related Fatal Crashes

"Eyes on the Street": The Impact of Tennessee's Emergency

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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.

J U S T I C E Q U A R T E R L Y , V o l u m e 21 No. 2, J u n e 2004 © 2004 A c a d e m y o f C r i m i n a l J u s t i c e S c i e n c e s

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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 learned 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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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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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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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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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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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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IMMIGRATION POLICY, BORDER SECURITY, AND MIGRANT DEATHS: AN IMPACT EVALUATION OF LIFE-SAVING EFFORTS UNDER THE BORDER SAFETY INITIATIVE*

ROB T. GUERETTE Florida International University

Research Summary: Subsequent to U.S. Border Patrol (USBP) efforts to control illegal immigration throughout the 1990s, concern arose over an apparent increase in deaths of illegal migrants as they began to undertake more treacherous routes to enter the United States from Mexico. In response, the Border Safety Initiative (BSI) was created to increase safety along the southwest border. Using multiple data sources, including the USBP BSI Incident Tracking System, this study evaluated the impact of life- saving efforts performed under the BSI program. Results indicate that there has been no overall reduction in the rate of migrant deaths since BSI has been in operation. However, an evaluation of BORSTAR search and rescue teams and the 2003 Lateral Repatriation Program (LRP), which returned apprehended migrants from Tucson sector to less hazardous places along the border, were found to be effective in preventing migrant deaths.

Policy Implications: Critics of U.S. immigration policy claim that the only way reductions in migrant deaths along the U.S.–Mexico border can be achieved is through liberalization of immigration policy and relaxing of border security. Yet, for more than a decade, U.S. policy makers have increased restrictions on immigration and have tightened security at the borders. Considering this, alternative means must be deployed in order to save migrant lives in the near term rather than waiting for a reversal of immigration policy. This study suggests that proactive life-saving measures implemented through a harm-reduction strategy can have some impact on saving migrant lives.

* Part of this research was supported through a project administered by the Border Research and Technology Center, a program of the National Institute of Justice. Points of view or opinions expressed in this article are solely those of the author. The author would like to thank Ronald V. Clarke for his assistance and guidance on the project.

VOLUME 6 NUMBER 2 2007 PP 201–222 R

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KEYWORDS: Migrant Death, Illegal Immigration Policy, Border Deaths, Border Patrol, Border Security

Throughout the last few decades, the United States has faced increasing problems of foreign nationals entering the country illegally in hopes of benefiting from abundant economic opportunity. In response, the U.S. Border Patrol implemented several operations in select border areas designed to prevent and detect illegal entries.1 The purpose of these oper- ations was to close off routes most frequently traveled by migrants and smugglers so that they would (1) be deterred from entry, (2) shift their attempts to ports of entry where inspection is systematic, or (3) alter their routes to more remote terrain where Border Patrol agents would have the tactical advantage (Government Accountability Office (GAO), 2001). In terms of altering migration routes, these operations seem to have been successful (Eschbach et al., 2001; GAO, 2001; Reyes et al., 2002).

In the wake of tightened border security, some border watchers called attention to an apparent increase in deaths as migrants sought out more treacherous routes to enter the United States undetected. Although it was expected that changes in traffic patterns would occur, an increase in migrant deaths was not (GAO, 2001:24). Since the year 2000, more than 300 migrant deaths are recorded along the border each year and it is believed many more perish but remain unfound. Citing these deaths, many criticized U.S. legislation and heightened border security calling for the reversal of immigration policy in the name of saving migrant lives. In response to these concerns, the then Immigration and Naturalization Ser- vice (INS) created the Border Safety Initiative (BSI) on June 16, 1998, which directed the United States Border Patrol (USBP) to increase safety along the border zone.

Rather than relaxing border security, BSI operations have focused on increasing border safety through adoption of a proactive harm-reduction strategy that resembles recent trends in community/problem-based polic- ing (Goldstein, 1979, 1990; Kelling and Coles, 1996; Wilson and Kelling, 1982). Specifically, the BSI program sought to reduce deaths primarily through the use of educational campaigns informing would-be migrants of the dangers of crossing in remote areas, provisions of life-saving equip- ment and training for line agents, and through search and rescue opera- tions performed by Border Search Trauma and Rescue (BORSTAR) teams. The BSI program also carried out a repatriation program in the summer of 2003, which relocated apprehended migrants from the Tucson

1. Operation Gatekeeper in the San Diego sector and Operation Safeguard in the Tucson sector, 1994; Operation Rio Grande Valley in south Texas, August 1997.

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area to less treacherous places along the Mexican border. To date, how- ever, it is unclear whether these efforts have been successful in preventing deaths among illegal immigrants. This study examines the impact of life- saving operations carried out under the BSI program.

RESEARCH BACKGROUND

For the past two decades, U.S. policy makers initiated consecutive poli- cies that led to increased fortification along the southwest border and more restrictive immigration laws. The 1986 Immigration Reform and Control Act (IRCA), the 1990 Immigration Reform Act, and the 1996 Ille- gal Immigration Reform and Immigrant Responsibility Act have all sought to prevent illegal immigration.2 Although several theories offer to explain this policy trend (Andreas, 2000; Martinez, 2002; Nevins, 2002a; Parenti, 1999; Welch, 2002), the uncontestable result has been fewer opportunities for legitimate entry into the United States and increased enforcement against those in violation. The continuation of this restric- tionist trend in the near term seems certain. The U.S. Congress recently authorized even more security at the southwest border, including the building of an additional 700 miles of fencing along the border (Bauza, 2006) and many border states have activated National Guard units to assist the Border Patrol.

One consequence of enhanced border security has been the apparent increase in migrant deaths. Several researchers attributed the cause of migrant casualties to U.S. immigration policy and the border buildup dur- ing the early 1990s (Cornelius, 2001; Eschbach et al., 1999, 2001; Reyes et al., 2002). This result was evidenced both by an increase in environmental exposure-related deaths as migrants began crossing more hazardous routes to enter the United States undetected and by an increase in the number of recorded deaths after the border enforcement campaigns began. Thus, as the difficulty of crossing the border increased, the number of migrants that

2. The 1986 Immigration Reform and Control Act (IRCA) initiated three pri- mary provisions: (1) the creation of sanctions for employers who knowingly hired undocumented aliens, (2) increased enforcement along the U.S. borders, and (3) legali- zation of then current illegal aliens residing in the United States. The 1990 Immigration Reform Act for the first time stipulated that all immigrants were subject to numerical restrictions, restricted criteria for entry, and liberalized conditions for exclusion. In 1996, the U.S. Congress passed the Illegal Immigration Reform and Immigrant Respon- sibility Act and the Antiterrorism and Effective Death Penalty Act. These acts expanded the powers of the Immigration and Naturalization Service (INS) by allowing for the detention and deportation of any illegal and legal immigrant who has been charged with or convicted of a drug offense or who otherwise possesses a criminal record. Additionally, the 1996 act established measures to control U.S. borders and augmented enforcement of laws prohibiting businesses from employing illegal aliens.

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perished also rose. This connection has been used by critics of U.S. immi- gration policy to call for the removal of the border buildup in the name of saving migrant lives (Nevins, 2002b).

Rather than loosening security at the border, the then INS announced the creation of the BSI in response to concerns about migrant deaths. The program was launched in conjunction with the Mexican government and was designed to make the border safer for migrants, officers,3 and border residents, although most efforts have been devoted to migrants. The BSI program became operational in June 1998 and consists of four elements: prevention, search and rescue, identification, and tracking and recording.

Under this initiative, the Border Patrol has implemented several safety measures along the 2,013 miles of U.S.–Mexico border as part of the ongo- ing BSI strategy. These measures are as follows:

• Implementation of public message campaigns and posting signs identifying the dangers of remote terrain crossings.

• Search and rescue operations performed by selected and highly trained agents that comprise the BORSTAR teams.

• Training of line agents in initial life-saving and rescue techniques. • Creation of a data tracking system that records all rescues and

deaths along the U.S. side of the southwest border. The data are intended to inform ongoing life-saving measures.

In addition to ongoing operations implemented under BSI, the Border Patrol conducted a repatriation effort in September 2003 in an attempt to reduce migrant deaths. Facing record numbers of deaths that year in the West Desert of Arizona (located in the Border Patrol’s Tucson sector), the Lateral Repatriation Program (LRP) returned migrants apprehended in this area to other less hazardous places along the border. Originally the plan was to return the migrants to the interior of Mexico, but the Mexican government did not agree so migrants were returned to the southern por- tion of the Texas–Mexican border. It was believed that if migrants were returned directly across the Arizona border, as is standard practice, the migrants would simply reattempt entry, thereby once again risking their lives during the hottest summer months.4 The LRP lasted 23 days and processed over 6,200 migrants at a cost of $1,352,080.

3. Throughout the 1990s, border agents increasingly were subject to sniper attacks, assaults, and shootings during drug enforcement and were assaulted with sticks and stones by Mexican smugglers (see Human Events Staff, 1997; Pendleton, 1995).

4. The effort to repatriate illegal immigrants is not new. A more comprehensive repatriation campaign was carried out in the 1950s, but on this occasion, the purpose of the effort was different. Although the former repatriation program was a response to illegal immigration more generally, the 2003 program was specifically intended to reduce migrant casualty and was managed by the director of the BSI.

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THE CURRENT STUDY

The BSI is a harm-reduction strategy consistent with community- and problem-based policing trends found throughout the United States among local police jurisdictions (Goldstein, 1979, 1990; Kelling and Coles, 1996; Wilson and Kelling, 1982). Since about the 1970s, a paradigm shift in U.S. policing emerged that began a movement away from exclusive reliance on rapid response and routine patrols. New ideas called for greater police–community interaction, a proactive focus on identifying and deal- ing with specific community problems, and the use of data analysis to inform operations. Although the Border Patrol overall has adopted some community-based strategies (such as bike patrol in some border towns), most operations are firmly set in professional era practice. The BSI, how- ever, is more reflective of a problem-based approach because it focuses proactively on life saving and harm reduction and uses data recording to inform when, where, and how border deaths occur. The BSI represents an opportunity to understand how proactive policing might be applied in new contexts, such as in the case of migrant deaths.

Given the current geopolitical environment, removing border security hardly seems a feasible policy option. There have been recent proposals for de facto amnesty and temporary worker programs, but it is uncertain whether these would adequately alleviate the flow of illegal entries, thereby reducing migrant deaths. This uncertainty occurs for several rea- sons. First, policy proposals that include these options also call for increased border security. Just as enhanced border security has correlated with increased migrant deaths, greater border security also leads to greater reliance on human smugglers whose drive for profit can lead to migrant deaths (Guerette and Clarke, 2005). Second, amnesty programs will likely lead to even more immigration (Andreas, 2000). Granting asylum (or paths to citizenship) will reaffirm current smuggling networks and will lure other would-be migrants hoping to benefit from any immediate or future amnesty programs. Third, the yearly allowable entries called for under guest worker programs are not sufficient to offset the yearly flow of immi- gration. Recent proposals stipulate up to 200,000 allowable entries. With over 1 million apprehensions along the southwest border each year, the remainder will be left with only unauthorized opportunities for entry into the United States.

If open borders (or even loosened borders) are not likely in the near term, then can proactive harm-reduction strategies be relied on to make the border safer? The purpose of this article is to examine whether such practices, particularly those of the Border Patrol, serve as a viable appara- tus to save migrant lives. To what extent have actions taken under BSI impacted the rate of migrant deaths along the U.S.–Mexico border? Are

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BORSTAR effective at saving migrant lives? Did the 2003 LRP prevent migrants from dying? The following analyses address these and related questions. First, a discussion of the data and analytical framework used to carry out this study is presented.

DATA DEPENDENT VARIABLE

Data on the frequency of individual migrant deaths5 were gathered from multiple sources. For evaluation of BSI impact, analyses rely on data from state and national vital registration systems compiled by Eschbach et al. (2001) as well as statistics in the BSI Incident Tracking System. Vital regis- tration system data were used because it provides a baseline for compari- son of trends in numbers of migrant deaths for an extended period of time. The BSI Incident Tracking System does not allow for this baseline as data collection and tracking of deaths did not systematically begin until 1999. The total time span of inquiry was from 1984 to 2003.6 It is possible that deaths recorded in the BSI tracking system and the vital registration sys- tems differ because of varying classification systems and collection proce- dures, but one study indicated that these differences are small.7 Even so, caution should be used when interpreting results from a single analysis of data derived from two separate collection processes.

INDEPENDENT VARIABLES

UNDOCUMENTED MIGRANT FLOWS

To account for changes in the volume of illegal immigration over time, yearly U.S. Border Patrol apprehensions for the southwest border were used. The limitations of relying on apprehension data are well docu- mented (Eschbach et al., 2001; Espenshade, 1995) and despite efforts to develop a more precise measure of illegal migrant flow little progress has been made. Apprehension figures are not a direct measure of illegal

5. The BSI Incident Tracking system maintains both individual and event death counts. However, the vital registration data counts only individuals, which meant that the analysis had to be based on counts of individual deaths, not of events. As most cases involve single deaths, whichever is used—individuals or incidents—the general picture will be similar.

6. Vital registration data were compiled from Eschbach et al., 2001 for the years 1984 to 1998. BSI Incident Tracking System figures were used for years 1999 to 2003. Yearly death figures derived from the BSI Incident Tracking System used in this study may diverge from numbers released publicly by the Border Patrol. This divergence is from retrospective editing of the data system in keeping with methodological protocols as more information about each incident is learned.

7. Reyes et al. (2002) compared U.S. vital registration data with USBP data for 1998 and found a small difference of 22.

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migrant flow, but they are a function of both Border Patrol activity and the number of migrants attempting illegal entry. To deal with these diffi- culties, most efforts have tried to use adjustments of apprehension data. For instance, a study by Eschbach et al. (2001) took the log of monthly apprehensions and the log of monthly border patrol man hours, regressed them on one another, and then used the residual as a measure of unde- tected illegal migrant traffic. In their analysis, they found the residual measure to be highly consistent with straight apprehensions (p. 16) and eventually went back to using straight apprehensions in subsequent parts of their analysis (p. 19). Others have also relied on apprehension data as a general measure of migratory activity in the analysis of migrant deaths (Reyes et al., 2002:65).8

MECHANISMS OF BSI INTERVENTION

Recent ideas in crime prevention studies suggest that mechanisms rather than causes should be identified that act within various contexts to explain specific outcomes (Pawson and Tilley, 1997). In this study, two “mecha- nisms” were specifically examined: (1) The impact of BORSTAR teams and (2) The LRP of 2003. Data for BORSTAR involvement in border deaths and rescues were introduced into the BSI Incident tracking system in 2002 but was not systematically recorded until 2003. To determine BORSTAR effectiveness, the 2003 data were used. In separate analyses, the impact of the LRP (as an independent variable) on migrant deaths was examined during the time period in which it took place.

DEMOGRAPHIC AND OTHER SITUATIONAL VARIABLES

Data on the gender of deceased or rescued migrants, their age, and the number of accompanying migrants were also used in some analyses. Data for these variables were collected from the BSI Incident Tracking System.

8. The Border Patrol does maintain records on what are referred to as “get-a- ways” based on observations by border agents in the field. These numbers ostensibly represent an indicator of successful illegal entries and as such could arguably be used to measure migrant traffic volumes. Many of these figures are derived using an ancient Native American tactic referred to as “sign cutting” in which Border Patrol agents smooth border terrain by dragging old tires behind a truck. Smooth sand and dirt allows agents to count series of footprints, thereby determining the approximate number of migrant crossings. After footprints are found, the terrain is resmoothed to identify sub- sequent crossings. However, the reliability and validity of these figures is suspect because much of the terrain along the border does not consist of dirt that can be smoothed and the extent that “sign cutting” is employed varies across sectors. In short, despite efforts to devise a more precise measure of illegal migrant flow apprehension, data provide the most reliable indicator.

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ANALYTICAL APPROACH

Three areas of analysis were undertaken to understand the impact of BSI operations on migrant deaths. First, an aggregate assessment of rates of migrant casualty examined trends before and after BSI implementation. Second, a comparison of whether BORSTAR agents performed better than regular line agents in saving migrant lives was performed. Third, the 2003 LRP was evaluated to determine its effectiveness in reducing migrant deaths.

To assess the aggregate impact of BSI operations, a simple interrupted time series design was used (Cook and Campbell, 1979). The range of analysis was from 1985 to 2003 which was sufficient to determine migrant death trends but did not allow for ARIMA modeling.9 The time series was computed using the rate of migrant deaths per 100,000 border apprehensions.

A series of bivariate and multivariate analyses was employed to deter- mine BORSTAR effectiveness. Bivariate analysis comprised a crosstab comparison of deaths and rescues by BORSTAR or line agent personnel. Analysis of BORSTAR was conducted only for the Tucson sector where they operate more frequently and only for year 2003 when recording prac- tices of their involvement in the BSI Tracking system are most reliable. For multivariate analysis of BORSTAR effectiveness, logistic regression was employed to determine differences in the outcome of death for BOR- STAR and line agents while taking into account gender, age, and number of accompanying victims. Logistic regression was used because it allows for determinations of the extent to which a dichotomous dependent varia- ble is influenced by a set of independent variables (Bohrnstedt and Knoke, 1994; Neter et al., 1996). Thus, BSI Incident Tracking data were coded in a dichotomous arrangement with death coded as 1 and rescue coded as 0. The use of logistic regression also allows for computation of odds ratios to compare the odds of death for each variable. Assessments of differences in the outcome of death in relation to gender, age, and accompanying migrants were used in the regression model to account for their affect on migrant deaths.

To evaluate LRP impact, two analyses were performed. First, compari- son was made between the numbers of exposure-heat deaths recorded in the Tucson sector during September 2003 (when LRP was implemented) with the number of same death types during the same month the prior year. Second, a quasi-experimental design with two nonequivalent com- parison groups was used to (1) compare Tucson’s change in relation to other similarly situated sectors; (2) to determine whether the relocation of

9. ARIMA models generally require around 100 data points for reliable analysis.

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migrants to the Texas sectors simply displaced the death problem to those areas; and (3) whether the receiving sectors experienced a diffusion of benefit. Displacement refers to the relocation of a problem (i.e., migrant deaths) to another area as a result of the intervention (i.e., the LRP). Dif- fusion of benefit represents the opposite of displacement referring to a shared reduction in the occurrence of death even though the specific inter- vention did not occur in those areas.

In doing so, two comparison areas were designated: a control and a buffer (Table 1). The purpose of the control area is to determine whether other similarly situated sectors that were not involved in the LRP exper- ienced declines similar to Tucson. If the control area also shows a decline, then it suggests that the LRP may not be effective and something else could have caused the decline in Tucson sector. The purpose of the buffer area is to determine whether the relocation of migrants to the receiving sectors caused an increase of deaths in those sectors (displacement) or a decrease in deaths (diffusion of benefit). If the death rate increases in these sectors compared with the previous year, then it suggests that dis- placement has occurred. If the death rate decreases, then it suggests that a diffusion of benefit has taken place.

TABLE 1. COMPOSITION, PURPOSE AND REASONING FOR LRP COMPARISONS

Comparisons Composition Purpose Reasoning

Treatment Tucson sector To determine whether A decrease in deaths area migrant death rates suggests effectiveness.

increased or decreased. An increase does not.

Control area El Centro and To determine whether If the control area San Diego other similarly situated also declined, then it sectors sectors that were not suggests LRP is not

involved in LRP effective and experienced declines something else caused similar to Tucson. the decline.

Buffer area McAllen, To determine whether If death rate increases Laredo, Del Rio, the relocation of in these sectors from and El Paso migrants to these sectors the previous year, sectors caused an increase of then it may suggest

deaths in those sectors displacement. If it (displacement) or a decreases, then it decrease in deaths suggests diffusion of (diffusion of benefit). benefit.

The control area was drawn from El Centro and San Diego sectors, which generally have maintained similar rates of death in recent years and

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are located on the western portion of the border like Tucson. To compare deaths across sectors, the numbers of death were standardized into rates of death per 10,000 monthly sector apprehensions. Rates per 10,000 (as opposed to the more common 100,000) were used because the numbers of apprehensions become smaller when disaggregated by the sector level. For the control area, rates were averaged to produce a single composite mea- sure of the death rate in those sectors.

The four Texas-Mexico sectors – El Paso, McAllen, Laredo, and Del Rio – were designated as the buffer area to determine whether displace- ment or diffusion of benefit occurred. These were used as the buffer because the migrants who were apprehended in Tucson sector were evenly relocated and released back into Mexico at each of these sectors.10 Like the comparison area, rates of death per 10,000 monthly sector apprehen- sions for each of the four sectors were computed and the average was used as a single composite measure. The pre-time period was September 2002, and the post-time period was September 2003. A series of coefficients was computed for the LRP based on a technique for evaluating crime preven- tion programs, which allows for determinations of displacement and diffu- sion (Bowers and Johnson, 2003). These coefficients include determination of gross and net effects of the LRP; the latter determines program effects in relation to changes in the comparison areas (See the Appendix for more detail).

FINDINGS

AGGREGATE ASSESSMENT

Figure 1 provides yearly rates of migrant deaths per 100,000 apprehen- sions from 1985 to 2003. Two general peaks can be observed, one in 1988 and the other in 2003. Prior to the implementation of BSI in 1998, the numbers of migrant deaths were actually on the decline after the 1988 peak until just before the BSI program began. Rates of death were reduced in 1999, but then they began to increase, reaching their highest peaks in 2003. Even though the post-BSI increase misses significance at the 0.05 level,11 the trend lines of the pre- and post-periods are distinctly different: with a negative slope in the pre-time period and a positive slope during the post-BSI period. If we accept apprehensions as a proxy mea- sure of border activity, it seems the BSI program has not reduced migrant deaths overall.

10. The number of migrants sent to each sector is as follows: Del Rio 1,576; El Paso 1,575; Laredo 1,454; and McAllen 1,634.

11. The difference in pre- and post-BSI means becomes significant at p < 0.10; (t = –1.912, 17 df).

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FIGURE 1. RATE OF MIGRANT DEATH PER 100,000 APPREHENSIONS, 1985-2003

0 5

10 15 20 25 30 35 40 45 50

1985 1987 1989 1991 1993 1995 1997 1999 2001 2003

R at

e of

D ea

th

Rate per 100K apprehensions Mean, 1985-1997 Mean, 1998-2003

Source: Eschbach et al. (2001) data, 1985-1998; BSI Incident Tracking System, 1999- 2003 (t = –1.911, 17 df, n.s.).

BORSTAR ASSESSMENT

A primary component of the BSI strategy involves BORSTAR, a highly trained volunteer group of Border Patrol agents who perform search and rescue operations along the border region. Many of these agents are emer- gency medical technicians (EMTs) and are trained in a wide assortment of rescue operations, including swift water, mountain, and desert rescue. The training regime is arduous enough so that not all of those who apply make it onto the teams, and partly because of this, their numbers are small. Ostensibly, these highly trained agents can better provide assistance to migrants in distress than can agents without such training and equipment. Accordingly, it can be expected that migrants in distress who are responded to by BORSTAR will be less likely to die and will have greater chances of being rescued. Conversely, those migrants responded to by reg- ular Border Patrol line agents would have a greater risk of death and lower probabilities of rescue. This hypothesis was examined here.

The BORSTAR assessment was conducted only for the Tucson sector where BORSTAR operations are most concentrated12 and only for 2003

12. As of January 2004 the distribution of BORSTAR agents by sector was as fol- lows: Tucson 38, San Diego 20, El Centro 16, Yuma 12, Del Rio 10, McAllen 8, Laredo 6, El Paso 5, and Marfa 1 (Source: United States Border Patrol).

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when data about their involvement was entered systematically.13 Heat exposure cases were analyzed because these are the most common and are most likely to be impacted by rapid response and medical assistance. The response of BORSTAR or line agents examined here was not randomly assigned; however, the chance of either group responding to a distressed migrant was more or less equal. This equality is because, in the Tucson sector, BORSTAR agents are interspersed with regular line agents to patrol the desert section of the border (located on the Tohono O’odham Reservation) during summer months. Thus, each group has a somewhat equal chance of encountering a distressed migrant while on patrol.

Table 2 provides a bivariate comparison of the number and percent of deaths and rescues by BORSTAR and line agents. The ratio of deaths to rescues for BORSTAR agents is considerably better than for line agents. For BORSTAR, roughly 1 out of 10 migrants who were responded to die compared with around 5 out of 10 for the line agents. To put another way, the probability of death occurring for migrants responded to by BOR- STAR is 7%. For those responded to by regular line agents, the probability of death is 47%. This difference was highly significant (Pearson chi-square p < 0.001).

TABLE 2. MIGRANT HEAT-EXPOSURE DEATHS AND RESCUES BY RESPONDING BORDER PATROL

AGENT IN TUCSON SECTOR, FY2003

Deaths Rescues N = 421

Frequency (%) Frequency (%)

BORSTAR 18 (7%) 260 (93%) Line agent 67 (47%) 76 (53%)

Source: U.S. Border Patrol BSI Incident Tracking System. Row percentages are reported. p < 0.001. Pearson chi-square.

Table 3 shows the coefficients for the logistic regression. Like the bivari- ate analysis, the picture is the same; when a BORSTAR agent responds to a distressed migrant, the outcome of death is significantly reduced (p < 0.01). More specifically, holding all variables constant, the odds of a migrant death occurring is reduced 84% when a BORSTAR agent responds compared with a line agent. The only other significant predictor of death is the number of accompanying migrant victims. Holding all else constant for every increase in accompanying migrant victims, the odds of

13. BORSTAR involvement began being tracked in 2002 but not systematically until 2003.

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death occurring significantly decreases (p < 0.001). The model chi-square was significant at p < .001, which suggests a good model fit, and overall the entered variables explained about 48% of the variance in the dependent variable. Separate analyses were performed for BORSTAR effects in the aggregate for all sectors and for all death types. In each analysis, the results were similar. When a BORSTAR agent responds to a distressed migrant, the outcome of death is significantly reduced.

TABLE 3. LOGISTIC REGRESSION OF MIGRANT HEAT-EXPOSURE DEATHS IN TUCSON SECTOR BY

BORSTAR, GENDER, AGE, AND NUMBER OF VICTIMS, FY2003

Standard B

Error Odds Ratio

BORSTAR –1.829** 0.583 0.161 Female 0.215 0.543 1.239 Age 0.042 0.026 1.043 Number of victims –0.772*** 0.199 0.462

Constant 0.691 0.906 1.996 –2 log-likelihood 94.815 Nagelkerke R2 0.476

Model chi-square 44.660; 4 df; p < 0.001. *Significant at 0.05 level, two-tailed test. **Significant at 0.01 level, two-tailed test. ***Significant at 0.001 level, two-tailed test.

BSI LRP

Although the LRP was directed at saving lives from all types of possible deaths, undoubtedly the primary focus was to reduce exposure deaths related to heat. Table 4 provides the number of heat exposure-related migrant deaths per month for 2003 in the Tucson sector. Here, the number of deaths decreased during the LRP (60%). Yet, the decrease was in the wake of large increases in deaths during the prior two months of July and August. This shift in direction provides some support of LRP effective- ness. Note that two other months, May and June, also show decreases in the number of migrant deaths. These reductions could be a product of Operation “Desert Safeguard,” which fortified the West Desert Corridor with additional rescue and line agents together with more aircraft support. Had Desert Safeguard not been in operation, it is likely that increases would have been observed in these two months as well.

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TABLE 4. HEAT-EXPOSURE DEATHS BY MONTH IN TUCSON SECTOR, 2002 AND 2003

2002–2003 % Month TCA 2002 TCA 2003

Change January 0 0 0 February 0 0 0 March 0 0 0 April 1 3 +200% May 6 5 –17% June 47 16 –66% July 12 42 +250% August 13 15 +15% September 10 4 –60% October 0 0 0 November 0 0 0 December 0 0 0

Total 89 85 –3% Source: U.S. Border Patrol.

A primary concern in the application of prevention initiatives is that the problem will be displaced to another area, thereby undermining response effects. Concerns over displacement are particularly relevant when dis- cussing illegal immigration, as evidence exists that migration has been dis- placed to more remote terrain in response to heightened border enforcement campaigns commenced in the early 1990’s (Eschbach et al., 2001; GAO, 2001:2,10; Reyes et al., 2002).

Although the above analysis indicates that deaths were reduced during the time of the LRP in the Tucson sector from the previous year, it does not take into account the possibility of increased death levels in the Texas sectors where the migrants were relocated. At the same time, it does not determine whether the reduction of deaths is attributable to the interven- tion or some other spurious shift that would have taken place had the LRP not been deployed.

Table 5 provides a series of coefficients that help determine the effec- tiveness of the LRP. The first column gives the rate of death per 10,000 monthly sector apprehensions during September 2002, whereas the second column represents the same number for September 2003. The third col- umn presents the difference between the two periods. For Tucson, the dif- ference for the pre- and post-periods indicates a decline of 2.82 deaths per 10,000 apprehensions, which represents the “gross effect” (GE). At the same time, the rate of death increased in the control area from a rate of

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6.97 to 12.49, which is an increase of 5.52. The NE or “net effect” coeffi- cient compares the change of the treatment area (Tucson sector) with the change in the control sectors. The NE in this case is 0.621, which indicates that the LRP was effective in reducing migrant deaths in relation to the comparison sectors.14

TABLE 5. RESPONSE EFFECTS OF LRP FOR ALL DEATH TYPES (RATE OF DEATH PER 10,000

MONTHLY SECTOR APPREHENSIONS)

September September Difference

2002 2003 Tucson (treatment area) 6.24 3.42 –2.82 Control areaa 6.97 12.49 +5.52 Buffer areab 2.47 2.07 –0.40

GE = 2.82 NE = 0.621 WDQ = 0.303 TNE = 10.12 aMean of El Centro and San Diego. bMean of McAllen, Laredo, Del Rio, and El Paso.

To assess displacement and diffusion of benefit effects, Bowers and Johnson (2003) propose the use of a “weighted displacement quotient” or WDQ. The WDQ allows for assessments of displacement or diffusion in relation to effects found in the treatment area. Notice that in the buffer area the rate of death decreased slightly from 2.47 to 2.07, which is a dif- ference of –0.40. The WDQ can either be positive, indicating diffusion, or negative, indicating displacement.15 In this case, the WDQ is 0.303, which signifies that the LRP had a diffusion effect in the buffer zone sectors.

So what then is the overall effect of the LRP? The “total net effect” (TNE) takes into account the treatment effect in relation to both the com- parison areas and the buffer zones, which allows for determination of overall impact of the intervention program. Here the TNE is 10.12, which indicates that, with the benefit of diffusion effects in the buffer sectors, the LRP contributed to an overall reduction in migrant deaths at a rate of 10 deaths per 10,000 monthly apprehensions (or rather 1 death per 1,000 monthly apprehensions). With the LRP repatriating just over 6,000 migrants, it seems that roughly 6 migrant lives were saved. However, even with the apparent effectiveness of the LRP and BORSTAR, the effects

14. A positive number indicates that the program was effective. A negative num- ber indicates that it made things worse, and a zero suggests that the intervention had no effect.

15. If the WDQ is greater than one, then the diffusion effect is greater than the response effect.

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were not large enough to have an impact on the overall rate of migrant deaths in the time series analysis.

CONCLUSION AND POLICY IMPLICATIONS

This study evaluated several components of the BSI. It examined the aggregate impact of the BSI on the rate of migrant death along the U.S. and Mexico border. It also analyzed the effectiveness of BORSTAR involvement in the life-saving campaign and the effect of the 2003 LRP. Both the BORSTAR and the LRP seem to have been successful in saving migrant lives. One implication is that the BORSTAR program should be expanded and given higher priority within all southwest border sectors. Currently, BORSTAR teams operate in various ways and with varying numbers across Border Patrol sectors. In the McAllen sector, for instance, BORSTAR agents have not been deployed in the interior areas of the sector where many exposure-heat deaths are recorded around interstate checkpoints. In FY2003, BORSTAR responded to 509 distressed individu- als along the entire Mexican border, comprising 27% of all individual migrants who were either rescued or died.16 To maximize BORSTAR’s potential to make the border safer, the number of these agents should be expanded in all sectors and they should be used at times and places where migrant deaths most frequently occur.

Like BORSTAR, the LRP also seems to provide an effective means to reduce migrant casualty. The above analysis indicates that roughly six lives were saved at a cost of around $1.4 million under the LRP. In the past, repatriation efforts were viewed as too costly when undertaken as a means to deal with illegal immigration more generally. When directed toward saving migrant lives, however, its application can be more surgical by con- ducting operations in times and places where it is most needed. A repatria- tion effort could also be coupled with other prevention efforts simultaneously, thereby amplifying life-saving effects.

Despite these positive effects, no overall decrease occurred in the num- ber or rate of migrant deaths when examined on the aggregate level. In many ways, this finding is similar to results from evaluations of local crime prevention efforts. Although evaluations of many proactive policing and crime-prevention programs show discernible localized reductions, little evidence exists that they have contributed to overall declines in crime rates experienced across the country (Eck and McGuire, 2000).

Yet, BORSTAR and the LRP are only two aspects of the broader proactive approach that are possible in addressing migrant deaths. A more

16. A total of 1,859 individual deaths and rescues occurred.

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formal adoption of a prevention program, such as situational crime pre- vention (SCP) or problem-oriented policing (POP), could better inform life-saving efforts. These programs would assist in identifying other ways of preventing deaths through more in-depth understanding of how, when, where, and under what conditions migrant deaths occur. In other words, much more might be done within the harm-reduction orientation.

Like all research, these findings have limitations. The absence of an extended systematically recorded series of migrant death data limits more complete understanding of BSI impact. Instead, the impact analysis of the BSI program is forced to rely on two separate sources of data. As such, caution should be taken when dismissing BSI effectiveness, because the absence of decline in the aggregate analysis may have more to do with data recording than with program impotence. Perhaps one inference is to use the evaluation findings toward informing development of future life- saving operations rather than dismantling current policy and practice. Caution should also be taken in interpreting the findings from the LRP analyses because numbers of migrant deaths become small when disaggre- gated by month. Given these small numbers, findings of effectiveness or ineffectiveness might only be suggestive.

Moreover, it is difficult to identify Border Patrol efforts as the sole cause for any lives saved because several others groups have been active in life-saving campaigns along the border. Many groups concerned with con- ditions along the border have also carried out rescue operations through the work of volunteers and have provided medical treatment, distributed water and food, and even conducted medical evacuations to those in need. Such groups include No More Deaths, the Border Action Network, Bor- der Links, Derechos Humanos, Humane Borders, Healing Our Borders, and numerous religious organizations among others. Even so, whether lives were saved by volunteer groups or Border Patrol agents, they both have employed proactive life-saving measures. The end result then is the same: The development and refinement of proactive harm-reduction strat- egies can prevent deaths.

This finding raises another point. In the past, the Border Patrol has been oppositional to those groups providing humanitarian assistance to migrants in distress. Some have even been prosecuted for federal immigra- tion crimes.17 Yet, it would better serve the Border Patrol to form alli- ances with such groups and work in concert with them rather than criminalizing their actions. Doing so would provide the benefit of acting as

17. In July 2005, two volunteers for No More Deaths were arrested by the U.S. Border Patrol and prosecuted for medically evacuating 3 illegal migrants in critical con- dition from the Arizona desert where temperatures were 105 degrees. The volunteers were said to follow established protocols of the organization by consulting medical pro- fessionals who advised them to evacuate the critically ill men to a medical facility and

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a force multiplier for the government’s life-saving campaign and would assist in fostering better community acceptance of the Border Patrol, at least among those sympathetic to the illegal migrant.

Despite the above constraints, this study does provide evidence that some of the life-saving efforts undertaken by the U.S. Border Patrol have been worthwhile. Continued refinement of life-saving practice may not eliminate all deaths, but it is better than no action at all and the obligation to improve life-saving practice falls with government (Guerette, 2006). Many have claimed that the only way to reduce migrant deaths along the border is through abandonment of current immigration policy and border enforcement. However, until the threat of international terrorism recedes, it is unlikely that any relaxing of border security will take place. Nor is it clear that revamping anti-immigration efforts that began in the 1990s will solve the death problem, considering that deaths frequently occurred prior to this period (Eschbach et al., 1999). Little doubt exists that federal policy makers need to address the multitude of issues that surround illegal immi- gration, but the strong polarity of opinions on these matters is sure to result in incremental changes at best. In the mean time, migrants will con- tinue to die. Given this, continued refinement and application of proactive life-saving measures may be the only immediate hope.

REFERENCES

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Rob Guerette is an assistant professor in the School of Criminal Justice at Florida International University, Miami, FL. His primary research interests include situational crime prevention, illegal immigration and border security, and public policy related to crime. His work has appeared in the Journal of Criminal Justice, Security Journal, and the European Journal on Criminal Policy and Research. He is co-editor of the book Migration, Culture Conflict, Crime and Terrorism (Ashgate Publishing, 2006). He holds a doctorate from Rutgers University-Newark and was a Fellow at the Eagleton Institute of Politics, Rutgers University-New Brunswick.

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APPENDIX A series of coefficients was computed to evaluate the outcome of the

2003 BSI LRP based on the work of Bowers and Johnson (2003). These coefficients include the computation of the gross effect (GE), net effect (NE), the total net effect (TNE), and the weighted displacement quotient (WDQ). The gross effect (GE) and the net effect (NE) are defined as

GE = Rb - Ra (1) whereas

NE = (Rb/Cb) - (Ra/Ca) (2)

The WDQ was used to determine displacement or diffusion effects and is designated as

WDQ = Da/Ca – Db/Cb (3)

Ra/Ca – Rb/Cb

Additionally, the overall impact of the LRP was determined using the TNE model, which is defined by the relationship

TNE = [Rb(Ca/Cb)-Ra] + [Db(Ca/Cb)-Da] (4)

where Da is the death rate in the buffer area during the LRP, Db is the death rate in this area during the same time period the previous year, Ca is the death rate in the comparison area during the LRP, Cb is the death rate in this area during the same time period the previous year, Ra is the death rate in the treatment area during the LRP, and Rb is the death rate in this same area during the same time period the previous year.

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