THEEFFECTSOFMANDATORYSEATBELTLAWSONDRIVING BEHAVIORANDTRAFFICFATALITIES AlmaCohen and Liran Einav*

Abstract—This paper investigates the effects of mandatory seat belt laws vation period, all other U.S. jurisdictions, except New on driver behavior and trafŽc fatalities. Using aunique panel data set on 1 2 seat belt usage in all U.S.jurisdictions, we analyze how such laws, by Hampshire, gradually adopted seat belt legislation. This inuencing seat belt use, affect the incidence of trafŽc fatalities. Allowing pattern of adoption makes it possible to obtain aclean for the endogeneity of seat belt usage, we Žnd that such usage decreases identiŽcation of the effectsof these laws, controlling for overall trafŽc fatalities. The magnitude of this effect, however, is signif- icantly smaller than the estimate used by the National Highway TrafŽc year and state Žxed effects.Given the wide variation in Safety Administration. In addition, wedo not Žnd signiŽcant support for usage ratesacross states, wecan also allow the effectof the compensating-behavior theory, which suggests that seat belt use also mandatory seat belt legislation to depend on the usage rate has an indirect adverse effect on fatalities by encouraging careless driving. Finally,weidentify factors, especially the type of enforcement used, that that prevailed when the lawwas passed. make seat belt laws more effective in increasing seat belt usage. The seat belt usage ratedata also allow fora direct investigation of the compensating-behavior theory (Peltz- I.Introduction man, 1975). According to this theory,because drivers wear- ing seat belts feelmore secure, they drive less carefully, RAFFIC accidents area majorsource of fatalitiesand leading to moretrafŽ c accidents. Thus, although the use of Tserious injuries. Every day morethan 100 Americans seat belts decrease fatalitiesamong drivers wearing them, arekilled in motor vehicle crashes. One important policy fatalitiesamong other individuals go up, offsetting the tool that has been used to combat this problem is the beneŽcial effects of seat belts. To test the compensating- passage of mandatory seat belt laws. Indeed, the federal behavior theory,it is necessary to identify the effectsof an government set in 1997 an ambitious goal of increasing seat increase in usage rateon driving behavior. belt usage fromthe 1996 national level of 68% to 85% by Wedistinguish, following the literature, between fatali- the year 2000 (atarget that was not achieved) and to90% by ties among caroccupants, who maybe directly affectedby 2005. To increase seat belt usage, the federalgovernment using seat belts, and fatalitiesamong nonoccupants (pedes- has been encouraging states to adopt stronger mandatory trians, bicyclists, and motorcyclists), who do not use seat seat belt laws. belts and can thus be affectedby seat belt use only indi- The aimof this paper is to empirically investigate the rectly.The compensating-behavior theory suggests that traf- effectiveness of mandatory seat belt laws in reducing trafŽc Žcfatalitiesare in uenced by seat belt use in two ways: the fatalities. Weuse aunique data set on state-level seat belt direct effect,which operates to reduce the probability that a usage that enables us to improve upon previous work. This caroccupant wearing aseat belt will be killed in the event data set allows us to break up the effectsof mandatory seat of an accident, and the indirect effect,which operates to belt laws into two components: the effectiveness of the laws increase the incidence of accidents by inducing less careful in increasing seat belt usage and the effectiveness of seat driving. Whereas caroccupants might be subject to both of belt use in reducing trafŽc fatalities. Using the seat belt laws these effects,nonoccupants aresubject only to the indirect as instruments forthe usage rate,this work is the Žrst to effect.Thus, the compensating-behavior theory predicts address the endogeneity of usage. Our Žndings have sub- positive correlation between seat belt usage and fatalities stantial implications forpolicymaking in this area. among nonoccupants. Our data set contains panel data on the 50 U.S. states and Our Žndings indicate that seat belt use signiŽcantly re- the District of Columbia forthe years 1983 to 1997. Al- duces fatalitiesamong caroccupants, but does not appear to though mandatory seat belt laws wereadopted in Europe have any statistically signiŽcant effecton fatalitiesamong and Australia as early as the 1970s, it was not until Decem- nonoccupants. Thus, wedo not Žnd signiŽcant evidence for ber 1984 that such laws wereadopted in the United States, compensating behavior. In the course of our analysis, we NewY ork being the Žrst state to do so. During our obser- replicatesome of the Žndings of studies that concluded that such behavior exists, and weshow that, once weallow for Received for publication October 30, 2001. Revision accepted for the endogeneity of usage, the effectsof seat belt use on publication July 11, 2002. *National Bureau of Economic Research and Stanford University, nonoccupant fatalitiesis insigniŽcant. respectively . Overall, weŽ nd that seat belt legislation unambiguously This paper was written while both authors were graduate students at reduces trafŽc fatalities. SpeciŽcally ,weestimate that a Harvard University.Weare grateful to Lucian Bebchuk, Gary Chamber- lain, David Cutler, John Graham, Shigeo Hirano, Caroline Hoxby, Law- rence Katz, Ariel Pakes, Jack Porter, Manuel Trajtenberg, Kip Viscusi, 1 In fact, NewHampshire passed amandatory seat belt law with seminar participants at Harvard University and at “Econometrics in secondary enforcement in 1999, but it requires only drivers and passen- Tel-Aviv,”two anonymous referees, and the editor for helpful comments. gers under the age of 18 to wear seat belts. We thank the NHSTAand the Highway Safety OfŽces of many states for 2 Within this period, in the late 1980s, four states—Massachusetts, providing us with the data on seat belt usage. Any remaining errors are our Nebraska, North Dakota, and Oregon—passed amandatory seat belt law, own. repealed it, and reinstated it again after ashort period (up to two years).

TheReview ofEconomicsand Statistics, November2003, 85(4): 828– 843 © 2003by the President and Fellows of HarvardCollege and the Massachusetts Instituteof Technology THE EFFECTS OFMANDATORY SEATBELTLAWS 829

1-percentage-point increase in usage saves 136 lives (using ities might be insigni Ž cant or even positive. This argument alinear speci Ž cation), and that a1% increase in usage was put forwardby Peltzman (1975), who argued that seat reduces occupant fatalitiesby about 0.13% (using alog-log belt use might produce carelessdriving and in turn greater speciŽ cation). To illustrate, this implies that moving from risks fornonoccupants. Asaresult, mandatory seat belt laws the 68% national usage level to the 90% target level will might increase total fatalitiesrather than reduce them. 3 save annually about 1500 –3000 lives (4% to 8% of all Thereis alarge empiricalliterature that triesto estimate trafŽ cfatalities).Interestingly ,although this estimateof the the effectof mandatory seat belt laws on fatalities. Some of effectof increased seat belt usage on saved lives is substan- the existing papers consider the effectof such laws on tial, it is considerably smallerthan the estimateused by the aggregate fatalitieswithout trying to distinguish between federalgovernment, which is 5,536 saved lives annually fatalitiesamong those seated in acarwho can wearseat (approximately 14% of total fatalities). belts (occupants) and those not in acar(nonoccupants). 4 The Ž rst-step regressions of our analysis also allow us to Other papers have tried to test forcompensating behavior by analyze which elements of seat belt legislation makeit making this distinction, which enables focusing on nonoc- effectivein increasing usage rate.The elementthat we Ž nd cupant fatalities. Nonoccupants cannot be affecteddirectly to be most important in this respect is having primary by seat belts but only through changes in driving behavior. enforcement (i.e., allowing the police to stop and Ž ne The studies that used this approach reached mixed results. 5 violators even ifthey do not engage in other offenses) rather The existing empiricalwork has substantial limitations than secondary enforcement (i.e., allowing the police to Ž ne that the present study seeks to overcome. To startwith, violators only when they arestopped forsome other of- many of the papers surveyed use timeseries data and look fense). While observers and policymakers have noticed that states with primaryenforcement have on average higher at trafŽ cfatalitiesbefore and aftera mandatory seat belt law 6 usage rates, weare able to identify and estimatethe effects was passed. Such studies could not take into account other of primaryenforcement in astatistically morereliable way. macroeffects, such as other laws, public campaigns, or We Ž nd that, whereas amandatory seat belt lawwith technological changes, which areunrelated to the manda- secondary enforcement increases the usage rateby about 11 tory seat belt laws but might have affectedthe changes in percentage points, amandatory seat belt lawbacked by the timetrend of fatalities. Second, the results of most primaryenforcement increases usage by about 22 percent- studies cannot be used forfurther policy evaluations, be- age points. This Ž nding supports the recentinitiative under- cause they depend only on one change in the law. 7 As taken by the federalgovernment to encourage states to discussed lateron, the comprehensive panel data that weuse adopt primaryenforcement. Indeed, weestimate that ifall in this paper allow us to overcome many of these limita- 34 states now having secondary enforcement wereto switch tions.8 toprimaryenforcement, the national usage would increase fromthe current 68% to about 77%, producing an annual 3 In the psychology literature, Wilde (1982) takes this argument to an saving in the range of 500 to 1,200 lives. extreme with his theory of risk homeostasis. He argues that individuals adopt a Ž xed target level of fatality risk and adjust their driving accord- The paper is organized as follows. Section IIdiscusses ingly. the literature, section IIIdescribes the data, and section IV 4 McCarthy (1999) Ž nds that amandatory seat belt law increases the discusses and motivates our estimation strategy.Section V number of fatal accidents, whereas Bhattacharyya and Layton (1979) and Houston, Richardson, and Neeley (1995) Ž nd that seat belt laws signi Ž - presents our results and discusses their robustness, and cant reduce traf Ž cfatalities. Derrig et al. (2002) Ž nd no statistically section VIconcludes. signiŽ cant effect. 5 Garbacz (1991), Loeb (1995), and Wagenaar, Maybee, and Sullivan (1988) Ž nd a signiŽ cant effect of mandatory seat belt laws in reducing occupant fatalities, whereas Evans and Graham (1991) and Harvey and II.Literature and Motivation Durbin (1986) Ž nd a signiŽ cant positive effect in increasing nonoccupant fatalities. Asch et al. (1991) Ž nd that, while the number of fatalities per Itis widely agreed that, holding the number of accidents accident decreased after the passage of the mandatory seat belt law, there Ž xed, the direct effectof seat belt use is to reduce fatalities was a signiŽ cant increase in the number of accidents. The most puzzling results are found by Garbacz (1990a, 1990b, 1992) and Risa (1994); they among those wearing seat belts. Asurvey of laboratory Ž nd that seat belt usage is either insigni Ž cant or positively associated with evidence concluded that seat belt use by front seat passen- occupant and nonoccupant fatalities. gers can prevent 40% to 50% of the fatalitiesamong such 6 See, for example, Bhattacharyya and Layton (1979), Garbacz (1991), Harvey and Durbin (1986), and Wagenaar et al. (1988). passengers involved in an accident (Departmentof Trans- 7 The same argument also applies when panel data are used, if the law portation, 1984). Furthermore, most of the empiricalpapers or the change in the law does not vary across the different groups. This is that investigated this direct effectfound results consistent the case, for example, in Risa (1994), Asch et al. (1991), and McCarthy (1999). with the laboratory studies (Evans, 1986, Grahamet al., 8 Evans and Graham (1991), Houston et al. (1995), and Sen (2001) do 1997, and Levitt and Porter, 2001). use the variation in the mandatory seat belt laws across U.S.states or Although it iswidely accepted that seat belt use reduces Canadian provinces. However, these papers do not use data on usage and thus can only analyze the reduced-form, indirect effect of mandatory seat the fatality risk among caroccupants in the event of an belt laws on fatalities. As we discuss next, such analysis may be signi Ž - accident, it has been argued that its overall effecton fatal- cantly improved upon by using data on seat belt usage. 830 THEREVIEW OFECONOMICS AND STATISTICS

Furthermore, and perhaps most importantly,the existing Ž rst-step regressions. This question is of interest to federal empiricalwork has failed to break up the law ’seffect,as we and state ofŽ cials who have been investing agreat deal of do, into the effectof the lawon usage and the effectof usage effortin trying to increase seat belt use. Most of the on trafŽ cfatalities. Mandatory seat belt laws presumably do empiricalstudies focus on the effectsthat the two different not affectfatalities directly but only through their effecton types of enforcement have on usage. The general Ž ndings usage, which in turn affectstraf Ž cfatalities. Thus, to con- arethat laws increase usage, and that primaryenforcement clude that mandatory seat belt laws arebene Ž cial, wemust does it signi Ž cantly better. 11 The existing studies generally Ž rst Ž nd that the laws areeffective in increasing seat belt focus on the short-termeffects of adopting seat belt laws, usage, and then investigate how usage affectsfatalities. By because they do not have panel data sets that aresuf Ž ciently analyzing the two effectsseparately ,asour data permitus to long. Our longer observation period may help generalize do, our approach has several advantages. First, the effectof these Ž ndings also forthe longer run. 12 amandatory seat belt lawmight depend substantially on the Some of the empiricalstudies also investigate how indi- initial seat belt usage atthe timethe lawwas passed. 9 The viduals’ characteristics affectthe individuals ’ decisions typical analysis in earlierstudies, which uses only dummy whether to use seat belts. Itwas found that heterogeneity variables forthe existence of mandatory seat belt laws across individuals is important, and that morerisk-averse restrictsthe lawto have an impact on fatalitiesthat is individuals aremore likely to comply with the law. 13 This constant across differentinitial levels of usage. Incontrast, heterogeneity introduces another dif Ž culty in measuring the by incorporating data on seat belt usage, weallow forthe impactof the law. Itmight suggest, forexample, that the law’seffectto depend on the initial usage level, which individuals who begin to wearseat belts when the usage seemsplausible and important. Moreover, usage data allow increases from40% to 60% areof adifferenttype than the fora moredirect test of the theory of compensating behav- individuals who begin towearseat belts when the usage rate ior. The theory suggests that carelessdriving is associated increases from80% to 100%; this might lead the two with seat belt use, not with the existence of mandatory seat increases to have differenteffects on fatalities. Weaddress belt laws, which can only be used as aproxy.Thus, testing these issues in section V,when weinvestigate different the theory on the basis of usage is preferable. Finally, speciŽ cations and functional forms. separately estimating the effectof seat belt usage on traf Ž c fatalitiesallows us to evaluate the bene Ž ts associated with III. Data other policy measures aimedat increasing seat belt use, such asadvertising campaigns. Weuse apanel of annual state-level variables forall U.S. The fewstudies that used seat belt usage data in their jurisdictions —the 50 states and the District of Columbia. analysis did not take into account that the decision to wear Unless otherwise noted, all variables cover the period be- aseat belt is achoice variable and thereforelikely to be tween 1983 and 1997. The DataAppendix de Ž nes all the endogenous (Garbacz,1990a, 1991, 1992; Risa, 1994). 10 variables, describes their sources and their relevance, and For example, ifthe probability of an accident is high, provides descriptive statistics. In this section wefocus on individuals will be morelikely to protect themselves and to the two most important variables forour analysis, namely, use seat belts. Hence, on regressing fatalitieson usage trafŽ cfatalitiesand seat belt usage. without allowing forthis endogeneity,wewould expect to Weobtained data on the annual number of occupant and Ž nd apositive correlation between the usage and the error nonoccupant 14 trafŽ cfatalitiesfrom the Fatality Analysis term,which would lead to an upward bias in the coef Ž cient Reporting System (FARS). 15 Thereare roughly 35,000 oc- on usage. Indeed, this is probably the reason why Garbacz cupant fatalitiesand 5,000 nonoccupant fatalitiesevery (1990a, 1992) and Risa (1994) obtain positive coef Ž cients year. Figure 1shows the trend in occupant and nonoccupant on usage, leading them to accept the compensating-behavior theory.As weshow lateron, this bias disappears once we 11 See, for example, Campbell (1988), Campbell, Stewart, and Campbell (1986), Dee (1998), Evans and Graham (1991), Wagenaar et al. (1988), allow forthe endogeneity of usage. and Patryka (1987). Finally,awide existing literaturefocuses on the impact of 12 As various writers have emphasized, the long-term effects of the mandatory seat belt laws on seat belt usage, aswedo in our considered legislation might differ from the short-term effects. See, for example, Peltzman (1977), and Evans and Graham (1991). 13 See Center for Disease Control (1986), Dee (1998), Evans (1987), 9 For example, such legislation might have abig effect in states in which Evans and Wasielewski (1983), Hunter et al. (1990), Houston et al. (1995), the seat belt usage was low to begin with, but only asmall effect in states Levitt and Porter (2001), and Singh and Thayer (1992). where everybody was already using seat belts prior to the passage of the 14 We do not distinguish between front seat and rear seat passengers, law. Seat belt usage varies agreat deal across states. In our data set, usage although it may be argued that rear seat passengers, in many states, are not levels in state-years without any mandatory seat belt law vary between 4% required to use seat belt, and hence should be treated as nonoccupants. If and 59%, with amean and median of 30% and standard deviation of about this is the case, then it only makes our results stronger. 13%, implying that wide variation in initial usage levels is likely to lead 15 FARScontains detailed information on all fatal traf Ž c accidents to awide variation in the impact of seat belt laws on traf Ž cfatalities. within the United States. Afatal accident is de Ž ned as any traf Ž c accident 10 See, for example, Traynor (1993), who provides evidence that drivers that results in fatality to avehicle occupant or nonmotorist, or in fatality are more likely to take various precautions, such as wearing aseat belt, from injuries resulting from atraf Ž caccident that occurs within 30 days when driving conditions are bad. of it. THE EFFECTS OFMANDATORY SEATBELTLAWS 831

FIGURE 1.—TOTAL OCCUPANT AND NONOCCUPANT FATALITIES

Thegraph shows the trends in occupant and nonoccupant fatalities in the United States overthe observation period. It can be seen that while total fatalities are roughly constant over the years, there is signi Ž cant trenddownwards once fatalities are normalized by vehicle miles traveled. fatalitiesduring our sample period. Itindicates that there is state-level usage rates, from1990 until 1999, forall no cleartrend over time.Once wenormalize by vehicle mile 51 states. The NHTSAdata that weuse arealso the traveled (VMT),we observe adrop in fatalitiesover the ones used by the federalgovernment toestimatethe sample period forboth occupants and nonoccupants. effectsof seat belt legislation and to allocate the An important and unique elementof our data set is the federalbudget among states. state-level data on seat belt usage. Weobtained such data (iii) Data from the Behavioral RiskFactor Surveillance fromthe following three differentsources: System (BRFSS). These data arebased on astate- level telephone survey conducted by the Center for (i) Data from the Highway Safety OfŽce of each state. Disease Control (CDC). One of the questions asked The states obtain their estimatesof seat belt usage in this survey is: “How often do you use seat belts rateby conducting periodical observational sur- when you drive or ride in acar? ” There are Ž ve 16 veys. Most of the states had separate estimatesfor possible answers: never, seldom, sometimes, almost front seat occupants and forrear seat occupants. We always, and always. Weassigned aweight to each use only the information on front seat occupants, one of the answers 18 and aggregated them by state which is available forall states forwhich wehave over all surveyed individuals, adjusting forsam- data. Consistent with NHTSAguidelines, the data pling weights. 19 The BRFSS data areavailable from arethen weighted to re  ectthe regional sampling 1984 until 1997, with varying numbers of states 17 design and the average daily traf Ž c volume. surveyed each year. 20 (ii) Data from the National Highway TrafŽc Safety Ad- ministration (NHTSA). These data include annual Wecombined the Ž rst two sources of data to obtain a usage data set that is as full as possible, and weused the 16 The way the observational survey is conducted is the following: each state chooses anumber of counties, which usually account for more than BRFSS data mainly forrobustness checks, addressing con- 85% of the population. In each county the survey is held at several chosen cerns about usage measurementfrom the observational sites (intersections). The sites are chosen from alist of potential sites by surveys. To combine the data fromthe Ž rst two sources, we astandard unbiased sampling procedure, which is recommended by the NHTSA.Potential sites are places where the driver has to either slow down or to stop completely,so that the observation is made easier and 18 The weights wehave used were (0, 0.1, 0.3, 0.75, 1). Wetried afew more accurate. After ashort training period, each observer is randomly other quintuplets of weights, without much difference in the results. assigned to aspeci Ž csite and to aspeci Ž ctime of day (the observation 19 The BRFSSis arandom telephone survey. Hence, sampling weights slots are generally a40 –60 min. time window during daylight hours on try to adjust mainly for the number of telephone lines and the number of midweek days). persons in each household. 17 Thirty-seven states provided us with afull set of data that includes 20 One problem with the use of these data is that it limited our number annual usage starting in the year prior to the passage of the law and until of observations substantially .Another problem is that this variable is far 1998, Ž ve states provided us with incomplete data for some of the years from being optimal in that it suffers from all the problems that arise from in our observation period, and nine states provided us with none. self-reporting, and from subjective answers. 832 THEREVIEW OFECONOMICS AND STATISTICS

FIGURE 2.—AVERAGE SEAT BELT USAGE OVER TIME

Thesolid line represents the average (equal weights) of seat beltusage, as reportedby the observational surveys. This variable is theone used in our reported regressions. The dashed line represents the average ofseat beltusage, as impliedby the BRFSS surveyof the CDC. Notethat the averages for 1994 and 1996 are based only on 10 states, as explainedin the text (section III). use as abasis the NHTSAdata and add to them the provide asimilarbut independent set of estimates, enables additional information obtained fromeach state ’s highway us to further verify the robustness of our results. 21 safety ofŽ ce. This seemsreasonable to do in that the two data sources provide similar Ž gures. Comparing the com- IV.EmpiricalStrategy parable Ž gures obtained fromthe two sources, we Ž nd that the differences arenot morethan 1 –2percentage points in As discussed above, during our observation period, all morethan 95% of the cases. Inmost cases, the Ž gures were U.S. states except NewHampshire passed mandatory seat actually identical, which is not surprising, because the belt laws. The variation in our data comes fromthe factthat states’ ofŽ ces aregenerally the source forthe NHTSAdata. states passed such laws atdifferent times and adopted laws Throughout our analysis weuse this combined data set for with differenttypes of enforcement. Another variation the reported results. comes fromthe factthat several states revised their laws, Some questions might be raised with respect to the moving fromsecondary enforcement to primaryenforce- reliability of the Ž gures weobtained fromeach state ’s ment.22 Figure 3displays the number of states with manda- highway safety of Ž ceand the NHTSA.One possible con- tory seat belt laws and the type of enforcement, asit evolved cern is that states might electto report ahigher usage than during our observation period. The factthat the adoption of the actual one in order to win federalbudgets that are mandatory seat belt laws was quite gradual helps us to promised to states that reachthreshold levels. Another identify their effects. concern might be with respect to the comparability of the Our basic approach is to estimatea simple linear equa- usage Ž gures across states and over time;states use obser- tion, with traf Ž cfatalitiesas the dependent variable and with vational methods that vary somewhat even ifthey are usage rate,control variables, and year and state Ž xed effects similarin spirit, and some states have also changed over on the right-hand side. timethe ways in which they conduct their observational surveys. 21 Because the BRFSSdata were obtained independently of our actual Wetake several steps to address some of these concerns. usage data, astrong relationship between the two data sets con Ž rms the reliability of our original usage data and the robustness of the results. First, wetry tomitigate any estimation problems that might Although the BRFSSdata, with the weights we use, suggest signi Ž cantly arisefrom the nature of the usage data by using state and higher usage than the data we end up using, the correlation between the time Ž xed effects.W edo so in order to control forstate- two data sets is remarkably high (correlation coef Ž cients of 0.7 to 0.9 across different dimensions of the data). Figure 2shows the increasing speciŽ cbiases that are Ž xed over time,as wellas forbiases national level of usage over time, with the very similar trend in the usage that might result fromchanges in reporting requirements by as calculated from the BRFSSsurvey . NHTSA. Second, weuse instrumental variables forthe 22 The two other papers that use similar panel data sets did not have such richness, because of the time at which they were written. Evans and usage rate,thereby addressing any nonsystematic measure- Graham (1991) had only data for 1984 to 1987, and Houston et al. (1995) ment errors. Finally,the use of the BRFSS data, which covered the period from 1967 to 1991. THE EFFECTS OFMANDATORY SEATBELTLAWS 833

FIGURE 3.—LEGISLATION OVER TIME

Thenumbers inside the bars are the numbers of states havinga particulartype of law in a givenyear. Alabama switched from secondary to primary enforcement in October 1999 (not re  ectedin the graph). New Hampshireis theonly state thathas no general mandatory seat beltlaw.

We use year Ž xed effectsto control forany time-speci Ž c lower once Ž xed effectsare controlled for, but it might well macro effects that shift the level of traf Ž cfatalitiesfor all not disappear. Conditions in any given state change over states. In our context, such macroeffects might involve time.For example, states that experienced an increase in technological changes that introduced safercars or national trafŽ cfatalitiesmight invest in promoting seat belt use. campaigns that affectedthe behavior of drivers across the Such investments might lead to anincrease in usage, which nation. The timeeffects also capture the increased penetra- again might generate apositive correlation between usage tion of airbags over time. 23 and the errorterm and thereby introduce an upward bias to We use state Ž xed effectsto capture any unobserved state our estimated coef Ž cient. characteristics that are Ž xed over time,such as population Therefore,it is worthwhile instrumenting forthe usage. characteristics, general weatherconditions, traf Ž c condi- Inour case, variables that arerelated to the mandatory seat tions, and so forth. Aspointed out in section II,these state belt laws arenatural candidates forinstrumental variables. Ž xed effectsare important formitigating the upward bias Such laws arelikely to be correlated with usage (afterall, associated with the likely endogeneity of seat belt usage. this is what the laws arefor), and it also seemsreasonable For example, this bias can arisefrom the factthat instates toassume that they arenot correlated with the errorterm. As with moredangerous traf Ž cconditions (due to weather, say, discussed earlier,mandatory seat belt laws arelikely to or road conditions) people aremore likely to use seat belts affect trafŽ cfatalitiesonly through their effecton usage. and arealso morelikely to be involved in atraf Ž c accident. Still, aconcern might remainwith respect to the possible Adding state Ž xed effectscannot, of course, completely endogeneity of the mandatory seat belt laws. Inparticular, it eliminateendogeneity problems. The probable positive cor- might be argued that states that facedan increase in their relation between usage and the errorterm is likely to be trafŽ cfatalitieshad ahigher propensity to pass such laws. Although the above concern might be important forcross- 23 Air bag effects would not be captured completely by the year effects sectional analysis, 24 webelieve that, once wecontrol for if there were cross effects between seat belts and air bags. However, it was suggested that these two protection devices are almost independent, in the sense that each is found useful in different types of accidents. See, for 24 For example, the results in Garbacz (1992) are likely to be driven by example, footnote 19 in Levitt and Porter (2001). such endogeneity bias. 834 THEREVIEW OFECONOMICS AND STATISTICS state and year Ž xed effects,this concern becomes much less important to note that the use of instrumental variables does important. Recall that all states except NewHampshire not only address the endogeneity problem but also solves eventually passed alaw, so that the considered concern any estimation problems that might result fromnonsystem- might ariseonly with respect to the type of lawpassed and aticmeasurement errors in the usage variable (seesection the timeat which it was passed. The passage of the lawis a III). political process that islikely to take some timeand whose Wefollow the existing literatureand estimatethe basic outcome may well depend on various political factors that equation twice. We Ž rst use the number of occupant fatal- areunlikely tobe related tofatalities. 25 ities as the dependent variable, and then the number of The main opposition to the seat belt laws was based on nonoccupant fatalities. In the Ž rst regression weexpect to arguments related to individual rights 26 and to discrimina- obtain anegative coef Ž cient onusage, which would bein tory enforcement, 27 not to trafŽ cfatalities. Thus, political, line with the expected direct effectof seat belts as a administrative, and ideological factors that had little to do protection device. The second regression tests forthe with fatalitiesare likely to have been the primaryfactors compensating-behavior hypothesis. Apositive coef Ž cient that determined the timein which the legislation was passed on usage in the second regression would be consistent with inany given state. Indeed, adetailed survey of the process the compensating-behavior hypothesis, whereas an insignif- producing mandatory seat belt legislation (NHTSA,1999) icant or anegative coef Ž cient would be inconsistent with does not even mention high levels of traf Ž cfatalitiesas the hypothesis. 28,29 having any in  uence on the passage of such legislation. Our Ž rst-step regression, inwhich usage isregressed on Rather, this survey indicates that political and administra- the mandatory seat belt lawvariables (aswell as on the tive factors played adecisive role in the timing of the other controls), also allows us to investigate which elements passage of the law: makeseat belt laws moreeffective. The main difference TrafŽ csafety measures wereintroduced when the among states ’ laws is in the type of enforcement (primaryor agenda forthe legislative session allowed it. Some secondary). In addition, some states have switched their sessions, highly in  uenced by the Governor ’s agenda, type of enforcement fromsecondary to primary,providing werededicated to gun control issues or revenue con- an additional layer of variation in the data. This variation cerns while others wereconcerned with traf Ž c safety across states and over timeenables us to performour measures, making itthe right timefor the introduction analysis. Ofthe 16 states with primaryenforcement, 8states of safety belt laws. Timing of legislative priorities was passed the lawwith primaryenforcement tobegin with, and crucial to passage. In most cases, legislators who 8states switched fromsecondary to primaryenforcement supported traf Ž csafety issues wereable togenerate the afterthe initial adoption (seetable 1). As mentioned earlier, necessary votes foronly alimited number of such there isawide variation inusage ratesamong the different measures inany given legislative session. These issues states. Lawsalso differin which passengers arerequired to included child passenger safety and speed limitinitia- wearseat belts. Most states require only front seat passen- tives. (NHTSA,1999, p. 24) gers to wearseat belts, but asigni Ž cant number of states (13 In general, the procedure involved in passing seat belt at present) require all passengers to do so. Fines also vary legislation is long and complicated, making the timing of across states, from$0 in Rhode Island (verbal warning only) the lawindependent of the errorterm on fatalities. The to $100 in Virginia. In addition, in some states auto insur- independence assumption is especially reasonable once ance coverage foran accident will be reduced ifthe seat belt state and year Ž xed effectsare included. Itis also worth lawwas not complied with atthe timeof an accident. noting that the fatalitiesseries arequite noisy,so that even Therefore,we also estimatehow usage levels areaffected ashort delay in passing the lawis suf Ž cient to makethe by the differentelements of the law, the passage of time actual timing of the passage of the lawsatisfy standard exogeneity requirements. 28 Note that much of the endogeneity problem for usage that is discussed in the text is less severe for the nonoccupant regression than it is for the Although there is no direct statistical test forthe validity occupant one. It is not obvious how an increase in nonoccupant fatalities of the instruments, werun several tests and obtain results would make drivers use more seat belts. However, it is likely that people that areconsistent with the above arguments. Itis also do not always obtain (through the media, for example) separate statistics on trafŽ cfatalities for occupants and nonoccupants. Hence, an increase in nonoccupant fatalities is predicted to affect seat belt decisions in asimilar 25 See Levitt (1996) for asimilar argument, when using prison- way to an increase in occupant fatalities, so endogeneity may still be an overcrowding litigation as an instrument for the number of prisoners. issue. 26 The argument is that unlike other traf Ž cviolations, seat belt law 29 Another way to test the Peltzman effect would be to look at changes violators do not put anyone else at risk, and hence should be free to choose in the number of accidents that result from an increase in the use of seat whether to use aseat belt or not. belt. The past work has not used changes in the number of accidents, 27 The term “driving while black, ” was used in the media to bring because data on the number of accidents are viewed as problematic (in that attention to this. It is argued that police of Ž cers use mandatory seat belt “accidents” are not well de Ž ned). As will be discussed in section V,we laws, and in particular primary enforcement, in order to stop African- also tested the Peltzman hypothesis using alimited panel data set on Americans and harass them. In practice, statistical studies have shown that number of accidents and obtained results consistent with those we ob- this is not true. tained using the number of nonoccupant fatalities. THE EFFECTS OFMANDATORY SEATBELTLAWS 835

TABLE 1.—A SUMMARY OF THE LAWS IN ALL STATES Usage Secondary Primary Before Immediately After Before Change Immediately After State Enforcement Enforcement Law Law in Law the Change In 1998 AK 9/12/90 45% 66% 57% AL 7/1/92 12/10/99 47% 58% 52% AR 7/15/91 34% 52% 62% AZ 1/1/91 55% 65% 62% CA 1/1/86 1/1/93 26% 45% 67% 81% 89% CO 7/1/87 NA NA 66% CT 1/1/86 NA NA 70% DC 12/12/85 10/9/97 NA NA 66% 80% 80% DE 1/1/92 54% 70% 62% FL 7/1/86 34% 55% 57% GA 9/1/88 7/1/96 20% 28% 51% 61% 74% HI 12/16/85 33% 73% 81% IA 7/1/86 18% 43% 77% ID 7/1/86 24% 27% 57% IL 7/1/85 16% 36% 65% IN 7/1/87 7/1/98 20% 37% 62% 62% KS 7/1/86 10% 24% 59% KY 7/1/94 42% 58% 54% LA 7/1/86 11/1/95 12% 35% 59% 63% 66% MA 2/1/94c 34% 52% 51% MD 7/1/86 10/1/97 18% 55% 71% 80% 83% ME 12/27/95 50% 50% 61% MI 7/1/85 26% 46% 70% MN 8/1/86 20% 33% 64% MO 9/28/85 NA NA 60% MS 3/20/90 NA 23% 58% MT 10/1/87 40% 59% 73% NC 10/1/85 26% 42% 77% ND 7/14/94c 32% 42% 40% NE 1/1/93c 33% 54% 65% NH 56% NJ 3/1/85 18% 40% 63% NM 1/1/86 NA NA 83% NV 7/1/87 21% 34% 76% NY 12/1/84 16% 52% 75% OH 5/6/86 19% 49% 61% OK 2/1/87 11/1/97 16% 35% 56% OR 12/7/90c 50% 70% 83% PA 11/23/87 NA NA 58% RI 7/1/91 28% 32% 59% SC 7/1/89 NA 49% 65% SD 1/1/95 40% 40% 46% TN 4/21/86 NA NA 57% TX 9/1/85 NA NA 74% UT 4/28/86 NA NA 67% VA 1/1/88 33% 63% 74% VT 1/1/94 54% 68% 63% WA 6/11/86 36% 52% 79% WI 12/1/87 26% 56% 62% WV 9/1/93 33% 55% 57% WY 6/8/89 NA NA 50% Total 42 16a Average 31% 48% 63% 73% 65%b a 8outof the16 states whichhave primary enforcement Ž rst adoptedsecondary enforcement and then switched to primary enforcement. b Thesample mean is notweighted, and therefore differs from the national usage, which is 68%in 1998. c InMassachusetts, Nebraska, North Dakota, and Oregon mandatory seat beltlaws werepassed, repealed, and reinstated again. In all thesecases thetime period between the original passage of thelaw and its repealdid not exceed two years. The dates provided above refer to the dates of thesecond passage of the law. Although not re  ectedin this table, these changes are taken into account in the empirical analysis. 836 THEREVIEW OFECONOMICS AND STATISTICS

TABLE 2.—THE EFFECT OF SEAT BELT USAGE ON OCCUPANT FATALITIES DependentVariable: OccupantFatalities perVMT log(OccupantFatalities perVMT) IndependentVariable OLS State FE IV OLS State FE IV Seat beltusage 0.0026** 20.0027*** 20.0052*** 0.0011 0.0010 0.0019 log(seatbelt usage) 0.114*** 20.053** 20.133*** 0.029 0.022 0.047 log(medianincome) 20.0162*** 0.0125*** 0.0122*** 20.988*** 0.657*** 0.624** 0.0013 0.0043 0.0044 0.074 0.248 0.254 log(unemploymentrate) 0.0018*** 20.0014*** 20.0015*** 0.072*** 20.126*** 20.132*** 0.0004 0.0005 0.0004 0.026 0.029 0.030 log(meanage) 0.0072** 0.0009 0.0041 0.424** 1.072 1.343* 0.0034 0.0145 0.0151 0.190 0.790 0.810 log(%blacks) 0.0006*** 0.0019 0.0019 0.041*** 0.080 0.075 0.0002 0.0016 0.0016 0.011 0.084 0.086 log(%Hispanics) 0.0003* 20.0010 20.0008 0.012 20.079 20.0803 0.00018 0.0012 0.0012 0.010 0.063 0.065 log(trafŽ cdensityrural) 20.0016*** 20.0022 20.0020 20.130*** 20.191* 20.200* 0.0003 0.0019 0.0020 0.019 0.104 0.106 log(trafŽ cdensityurban) 0.0019** 0.0006 0.0005 0.177*** 20.151* 20.167** 0.0008 0.0013 0.0013 0.046 0.080 0.082 log(violentcrimes) 0.0027*** 20.0005 20.0006 0.151*** 20.037 20.035 0.0005 0.0011 0.0010 0.028 0.055 0.055 log(propertycrimes) 20.0025*** 0.0028** 0.0027** 20.119*** 0.280*** 0.279*** 0.0006 0.0013 0.0013 0.032 0.080 0.081 log(VMTrural) 0.0013*** 20.0043** 20.0042** 0.101*** 0.051 0.100 0.0002 0.0021 0.0021 0.013 0.116 0.118 log(VMTurban) 20.0024*** 20.0082*** 20.0081*** 20.138*** 20.267*** 20.247*** 0.0004 0.0016 0.0016 0.023 0.084 0.085 log(fueltax) 20.0014*** 20.0019*** 20.0019*** 20.112*** 20.110*** 20.114*** 0.0004 0.0005 0.0005 0.024 0.030 0.031 65-mphspeed limit 20.0003 20.0004 20.0003 20.028 20.014 0.0004 0.0003 0.0003 0.026 0.021 0.022 70-mphspeed limit or above 0.0008** 0.0012*** 0.0012*** 0.055** 0.087*** 0.089*** 0.0004 0.0003 0.0003 0.025 0.016 0.017 MLDAof 21years 20.0015** 20.0015*** 20.0014*** 20.048 20.055*** 20.051** 0.0008 0.0005 0.0005 0.034 0.021 0.023 BAC 5 0.08 20.0004 20.0002 20.0002 20.011 20.009 20.012 0.0003 0.0003 0.0003 0.018 0.016 0.017

Year FE Yes Yes Yes Yes Yes Yes State FE No Yes Yes No Yes Yes N 556 556 556 556 556 556 Adj. R2 0.7751 0.9305 0.9294 0.787 0.936 0.934 For exact deŽ nitionsof the variables, refer to the data appendix. ***,**,*:Signi Ž cantat 1%,5%, and 10% con Ž dencelevel, respectively. Thevariables that we used as instrumentsfor the third column are three dummy variables that stand for mandatory seat beltlaws withsecondary enforcement, primary enforcement, and primary enforcement that followsa switchfrom initially adopting secondary enforcement. Robuststandard errors below estimates. As describedin the text, note that the panel is notfull for the early years (before 1990), which is whythe number of observations is 556rather than 765 (51 states over15 years, 1983 –1997). since the adoption of the law, and the initial level of seat belt fourth columns report OLSregressions without controlling usage. Weuse asimple linear speci Ž cation to do so, as for state Ž xed effects.In both speci Ž cations the coef Ž cient suggested by aBox-Cox regression. 30 on usage is positive and signi Ž cant, indicating that higher seat belt usage increases occupant fatalities. As argued V. Results before, this is likely to be the result of strong endogeneity of A.TheEffect of Seat Belt Use onOccupant Fatalities the usage variable. Indeed, once wecontrol forstate Ž xed effects,as reported in the second and Ž fth columns of table Table 2presents aset of linear and log-log regressions of 2, the coefŽ cient on usage changes its sign and becomes occupant fatalitieson usage and other controls. The Ž rst and negative and statistically signi Ž cant. However, the inclusion of state Ž xed effectscorrects only forthat part of the 30 An alternative speci Ž cation would treat seat belt use as adynamic endogeneity problem that arises fromcross-sectional differ- decision by adding to the estimated Ž rst-step equation the lagged usage as a regressor.Webrie  ydiscuss this speci Ž cation in section V.However,note that ences across states. The usage variable is still likely to be when using Ž xed effects one should be concerned that the coef Ž cient on the positively correlated with the errorterm, and hence to be lagged dependent variable would be biased because of the correlation be- tween the lagged usage and the within error term. To remedy the bias, we biased upwards, towards 0. Another potential source of bias instrument for it by using the lagged difference in usage. in the coefŽ cient on usage is that of measurementerrors. THE EFFECTS OFMANDATORY SEATBELTLAWS 837

This source of bias would also lead to abias towards 0in the dangerous than amiletraveled on urban roads, which seems coefŽ cient. plausible. Fortunately,by instrumenting forusage using the dum- miesof mandatory seat belt lawand type of enforcement, B.TheEffect of Seat Belt Use onNonoccupant Fatalities wecan solve both problems. Indeed, asreported in the third and sixth columns of table 2, once instrumented for, the Table 3is identical to table 2except forthe dependent usage coefŽ cient becomes higher in absolute value, with a variable, which is now the nonoccupant fatalities. Again, it negative coef Ž cient of 20.0052 forthe linear speci Ž cation iseasy to notice the dramaticchanges in the coef Ž cient on and elasticity of about 20.13 forthe log-log speci Ž cation.31 usage once wecontrol forstate Ž xed-effects. In the simple The coefŽ cients on the control variables deserve attention OLSregressions, forboth speci Ž cations, the coef Ž cient on usage is positive and statistically signi Ž cant, which could be aswell. Note the extremechange in most of them once we interpreted as an indication of compensating behavior. We move fromthe simple OLSregression in the Ž rst and fourth view this as areplication of the results reported by Garbacz columns to the Ž xed effectsspeci Ž cation in the second and (1992b) and Risa (1994). Once state Ž xed effectsare con- Ž fth columns. Because most of the variation in these vari- trolled for, however, the coef Ž cient on usage becomes ables is between states ratherthan within states (seethe negative (and statistically signi Ž cant in the log-log speci Ž - DataAppendix), the simple OLSresults aredriven by the cation), suggesting the opposite story.This result is consis- cross-state variation, while the Ž xed-effects results are tent with the story that the use of seat belts makes drivers driven by within-state variation. Some of the views ex- moreconscious of safety issues and thereby induces them to pressed in policy discussions seemto be driven by the drive morecarefully .Once wetreat the usage as endoge- cross-sectional variation, and they disappear once state Ž xed nous, the coef Ž cient on usage becomes statistically insig- effectsare controlled for. niŽ cant in both speci Ž cations. Thus, weconclude that the The third and sixth columns of table 2indicate that the effectof usage rateon nonoccupant fatalitiesis nonpositive, coefŽ cient on income is positive and that the coef Ž cient on and that there is no strong support forthe Peltzman effect. unemployment rateis negative. This suggests that traf Ž c Table 3indicates that, whereas many of the coef Ž cients fatalitiesare lower in bad times, which is consistent with on the control variables obtain signi Ž cant coefŽ cients when Ruhm’s (2000) Ž ndings that mortality ratesare lower during wedo not control forstate Ž xed effects,almost all of them recessions. Note, however, that traf Ž cdensity and VMTare become insigni Ž cant once wedo so. This suggests that the controlled for, so Ruhm ’ssuggestion that people drive more within variation in nonoccupant fatalitiesis quite noisy,and during booms cannot fully explain the results. Another it cannot be explained by our control variables. Another possible factormight be that the opportunity cost of timeis possibility is that weneed other controls to explain nonoc- higher during booms, inducing fasterdriving. cupant fatalities, such asthe number of bicyclists or pedes- The coefŽ cients on the other demographic variables are trians ineach state or the level of activity (i.e., the equiva- not statistically signi Ž cant once Ž xed effectsare controlled lent of VMT)per bicyclist and pedestrian in each state. Such for. This result is inconsistent with the widespread percep- data, however, arenot available. The only two controls that tion that African-Americansare involved in morefatal do have signi Ž cant coefŽ cients areon age and the dummy trafŽ caccidents. That popular view shows up in the OLS forhigh speed limits. The latteris positive, suggesting that results, but disappears once wecontrol forstate Ž xed higher speed limits arelikely to lead to morenonoccupant effects. fatalities. The coef Ž cient on age is positive and very high. TrafŽ cdensity,in both ruraland urban roads, has no This maybe the result of higher likelihood of nonoccupant fatalities(mainly of pedestrians) among elderly persons. signiŽ cant effectin the linear speci Ž cation but has anega- Itmight be suggested that bicyclists aresubject to tech- tive effecton fatalitiesin the log-log speci Ž cation. Denser nological changes such asbetter bicycles and the introduc- trafŽ cmight result in slower or morecareful driving and tion of bike helmets in the 1980s. Such changes might affect hence less accidents. The interpretation of the coef Ž cients the interpretation of the results weobtain fornonoccupant on VMTis indirect because VMTis also used in the fatalities. To deal with this concern, weran the above construction of the dependent variable. The effectof urban regressions only forpedestrians, whose activity was pre- VMTis negative, and the effectof ruralVMT is insigni Ž - sumably not subject to technological changes. The coef Ž - cant; this suggests that amiletraveled on ruralroads ismore cient weobtain on usage remainsinsigni Ž cant as before. The Peltzman effectcould in theory be tested also by 31 In fact, our data potentially allow us to distinguish between the two looking atthe effectsof seat belt laws on the number of sources of bias. To eliminate the bias caused by measurement error without changing the endogeneity bias, we use the other measure of usage, accidents ratherthan the number of nonoccupant fatalities. the one obtained from the CDC,as an instrument for the usage rate. By The number of accidents presumably re  ects changes in doing so in the log-log speci Ž cation, weobtain acoef Ž cient of 20.097 on driving behavior. However, data on the number of accidents the usage, suggesting that about half of the bias in the Ž xed-effects OLS coefŽ cient may be attributable to measurement errors, whereas the other areviewed as problematic and have not been used heavily in half comes from endogeneity . the literature, because, unlike fatalities, “accidents” are not 838 THEREVIEW OFECONOMICS AND STATISTICS

TABLE 3.—THE EFFECT OF SEAT BELT USAGE ON NONOCCUPANT FATALITIES DependentVariable: NonoccupantFatalities perVMT log(NonoccupantFatalities perVMT) OLS State FE IV OLS State FE IV Seat beltusage 0.0011*** 20.0001 0.0007 0.0004 0.0004 0.0007 log(seatbelt usage) 0.158*** 20.119** 20.042 0.056 0.058 0.121 log(medianincome) 20.0028*** 20.0018 20.0017 20.981*** 20.303 20.270 0.0005 0.0014 0.0013 0.149 0.555 0.558 log(unemploymentrate) 0.0001 20.0005*** 20.0005 0.108** 20.037 20.031 0.0001 0.0002 0.0005 0.051 0.064 0.065 log(meanage) 0.0051*** 0.0210*** 0.0199*** 0.522 6.089*** 5.833*** 0.0017 0.0065 0.0063 0.456 2.210 2.153 log(%blacks) 0.0002*** 0.0006 0.0006 0.074*** 20.391* 20.386 0.0006 0.0005 0.0005 0.022 0.234 0.236 log(%Hispanics) 0.0007*** 0.0014*** 0.0012** 0.206*** 0.173 0.177 0.0006 0.0004 0.0004 0.018 0.157 0.157 log(trafŽ cdensityrural) 0.0002** 20.0001 20.0001 0.099*** 20.065 20.057 0.0001 0.0008 0.0008 0.034 0.303 0.301 log(trafŽ cdensityurban) 0.0011*** 0.0001 0.0001 0.415*** 20.239 20.223 0.0003 0.0007 0.0007 0.087 0.165 0.170 log(violentcrimes) 0.0008*** 0.0001 0.0001 0.313*** 0.088 0.087 0.0001 0.0003 0.0003 0.053 0.134 0.134 log(propertycrimes) 20.0012*** 20.0001 20.0001 20.452*** 20.250 20.249 0.0002 0.0005 0.0005 0.068 0.179 0.179 log(VMTrural) 20.0002*** 20.0008 20.0008 20.075*** 20.384 20.431 0.00008 0.0007 0.0007 0.024 0.272 0.275 log(VMTurban) 20.0006*** 20.0006 20.0006 20.188*** 0.091 0.072 0.0001 0.0006 0.0006 0.052 0.185 0.187 log(fueltax) 20.0008*** 20.0001 20.0001 20.090* 0.039 0.043 0.0002 0.0002 0.0002 0.049 0.062 0.062 65-mphspeed limit 0.0001 20.0001 20.0001 20.050 20.034 20.047 0.0002 0.0002 0.0002 0.047 0.056 0.059 70-mphspeed limit or above 0.00002 0.0004*** 0.0004*** 0.043 0.177*** 0.174*** 0.0001 0.00009 0.0001 0.054 0.040 0.040 MLDAof 21years 0.00003 0.000008 20.00002 20.016 0.016 0.013 0.0003 0.0002 0.0002 0.075 0.055 0.055 BAC 5 0.08 0.00018* 20.0001 20.00008 0.071 20.050 20.047 0.0001 0.0001 0.0001 0.045 0.037 0.037

Year FE Yes Yes Yes Yes Yes Yes State FE No Yes Yes No Yes Yes N 556 556 556 556 556 556 Adj. R2 0.6805 0.9031 0.9018 0.686 0.881 0.880 For exact deŽ nitionsof the variables, refer to the data appendix. ***,**,*:Signi Ž cantat 1%,5%, and 10% con Ž dencelevel, respectively. Thevariables that we used as instrumentsfor the third column are three dummy variables that stand for MSBL with secondary enforcement, primary enforcement, and primary enforcement that follows a switch frominitially adopting secondary enforcement. Robuststandard errors below estimates. As describedin the text, note that the panel is notfull for the early years (before 1990), which is whythe number of observations is 556rather than 765 (51 states over15 years, 1983 –1997).

well deŽ ned.32 Nevertheless, weused such data to check our C.TheEffect of Mandatory Seat Belt Laws on Seat Belt previous results. Using panel data on 17 states over six years Usage forthe number of accidents (seeData Appendix), we Ž nd that the coef Ž cient on usage was insigni Ž cant. This result is Table 4reports the results of regressing seat belt usage on similarto the results presented in table 3, and it is consistent the lawvariables and differentcontrols. The Ž rst regression with those Ž ndings of ours that suggest that compensating does not use state Ž xed effects,and the second regression behavior does not have asigni Ž cant effect. does. Wealso consider several functional formsfor the usage variable, but aBox-Cox regression, allowing the 32 In this case, for example, what wehave is the count of police accident dependent variable to have  exible functional form,sug- reports. While police are likely to be present at any serious accident, the gests that alinear speci Ž cation is the most suitable func- arrival of police to the scene of aminor accident may depend greatly on the region, the time of day,the day of the week, and many other factors. tional form,with L 5 1.025, insigni Ž cantly differentfrom Many crashes are not reported to police and therefore go undetected in 1 ( p . 0.65). Itis worth noting that the linear speci Ž cation state records. Studies have concluded that these cases make up asizable portion of motor vehicle crashes [see Blincoe and Faigin (1992) and can also be easily seen fromlooking atplots of the usage NHTSA(1994)]. series state by state. THE EFFECTS OFMANDATORY SEATBELTLAWS 839

TABLE 4.—THE IMPACT OF MANDATORY SEAT BELT LAWS ON enforcement and on the switch to primaryenforcement is SEAT BELT USAGE not signiŽ cantly differentfrom the coef Ž cient on primary DependentVariable: Seat Belt Usage enforcement. IndependentVariable OLS State FE Itis also worthwhile reporting the variables that we Secondaryenforcement 0.131*** 0.112*** exclude fromour Ž nal regression. Some researcherssuggest 0.012 0.012 Primaryenforcement 0.286*** 0.219*** that the short-termeffects of mandatory seat belt laws might 0.015 0.024 differfrom the long-term effects.W ethereforede Ž ned new Secondaryto primary enforcement 0.122*** 0.135*** variables that wereequal to the timepassed since the law 0.023 0.017 log(medianincome) 0.259*** 0.015 was adopted foreach one of the enforcement types. None of 0.043 0.158 these variables was found to be signi Ž cant. Thus, the effect log(unemploymentrate) 0.038*** 0.006 of the lawappears to be immediate and permanent. This 0.015 0.024 log(meanage) 0.111 0.418 phenomenon can also be veri Ž edby looking atusage plots 0.092 0.508 state by state. log(%blacks) 20.008 0.048 Wealso tested the signi Ž cance of other components of the 0.007 0.052 log(%Hispanics) 20.003 20.016 law. Wefound that the coef Ž cient on who is required to use 33 0.005 0.052 seat belts is not signi Ž cant. Similarly,the coef Ž cients on log(trafŽ cdensityrural) 20.022** 0.067 whether or not wearing aseat belt will reduce insurance 0.009 0.094 log(trafŽ cdensityurban) 0.112*** 0.025 coverage in the event of anaccident, and the coef Ž cient on 0.021 0.060 the amount of the Ž ne, turn out to be insigni Ž cant aswell. log(violentcrimes) 20.008 20.036 In addition, most of our control variables lose signi Ž - 0.015 0.032 log(propertycrimes) 0.055*** 20.033 cance once state Ž xed effectsare included. Moreover, the 0.018 0.051 percentage of African-Americansor Hispanics is not signif- log(VMTrural) 0.024*** 0.087 icant, even when state Ž xed effectsare not included. This 0.006 0.092 log(VMTurban) 0.015 0.027 contradicts the common view that minorities aremore likely 0.013 0.055 not to use seat belts and hence should be speci Ž cally log(fueltax) 20.007 20.043** targeted in seat belt campaigns. 0.015 0.022 65-mphspeed limit 0.052*** 0.023 Although traf Ž cfatalitiesseem to be astatic variable, seat 0.018 0.015 belt usage might have some dynamic effectsas well. There- 70-mphspeed limit or above 20.014 20.005 fore, wealso estimated aregression using lagged seat belt 0.014 0.012 MLDAof 21years 20.024 0.011 usage as an explanatory variable. We Ž nd that the lagged 0.022 0.025 usage variable turns out to be signi Ž cant, taking about BAC 5 0.08 0.012 20.007 one-third of the explanatory power fromthe law-related 0.011 0.013 dummies, and suggesting some habitual behavior. However, Year FE Yes Yes given that the laws generally moved in one direction, from State FE No Yes not having alawto having one or fromhaving secondary N 556 556 Adj. R2 0.803 0.912 enforcement to having primaryenforcement, it isnot clear For exact deŽ nitionsof the variables, refer to the data appendix. that our data can distinguish between dynamic and static ***,**,*:Signi Ž cantat 1%,5%, and 10% con Ž dencelevel, respectively. effects.Ideally ,one would use individual-level data to make Inunreported regressions we run identical regressions using the CDC usagedata and obtain similar results. that distinction. Alternatively,one maywant to examine the As describedin the text, note that the panel is notfull for the early years (before 1990), which is why thenumber of observations is 556rather than 765 (51 states over15 years, 1983 –1997). four cases in which the lawwas repealed. In all those cases, ABox-Coxregression (as well as inspectionof the graphs) suggests that a linearspeci Ž cationof the unfortunately,the timebetween the changes did not exceed dependentvariable is muchmore appropriate. two years, which precluded using it foridenti Ž cation given our annual usage data. Still, the fewdata fromthese epi- As expected, mandatory seat belt laws signi Ž cantly in- sodes areconsistent with the view that static decisions are creasethe seat belt usage rate,and primaryenforcement moreimportant than dynamic habits; usage ratesdropped does this moreeffectively than secondary enforcement. drastically with the repealof the laws and increased imme- Primaryenforcement increases usage by about 22 percent- diately afterthe laws werereinstated. age points, whereas secondary enforcement increases it by only half as much. Switching fromsecondary to primary D.Robustnessand Speci Ž cationT ests enforcement increases the usage by about 13 percentage points. Our results suggest that adopting primaryenforce- Wehave used differentspeci Ž cations and have run dif- ment fromthe beginning has asimilarultimate effecton ferenttests to check whether our results arerobust. Wehave usage to that of Ž rst adopting secondary enforcement and then switching to primaryenforcement. Indeed, wecannot 33 Recall that our usage data are on front seat passengers only,so this result is not very surprising. It is quite likely that this component of the rejectthe hypothesis that both strategies have the same law would affect the usage rate of rear seat passengers, but the available ultimate effect —the sum of the coef Ž cients on secondary data do not allow us to test this. 840 THEREVIEW OFECONOMICS AND STATISTICS also done so to examine whether our assumptions regarding TABLE 5.—REDUCED-FORM REGRESSION the validity of the instruments and the functional formare DependentVariable: Fatalitiesper VMT log(Fatalities per VMT) 34 supported by the data. Independent Occupant Nonoccupant Occupant Nonoccupant First, wetested differentsets of controls by omitting and Variable Regression Regression Regression Regression adding variables to the set of controls reported in tables 2 Secondarydummy 20.0007***0.00007 20.042***0.0005 and 3. Additional controls wereproxies forthe state popu- 0.0002 0.000090.013 0.032 lation’slevel of risk aversion, such as diet, smoking habits, Primarydummy 20.0012*** 20.0001 20.061***0.084** 0.0005 0.00020.022 0.042 and frequency of athletic exercising, that wereobtained Secondaryto fromthe BRFSS data. Other controls that weincluded are primarydummy 20.0002 0.0003 20.030 0.086 the number of licensed drivers and registered vehicles. We 0.0004 0.00020.024 0.063 also included the fraction of new carregistrations in order to N 765 765 765 765 capture differences in the safety level of carsresulting from Adj. R2 0.9227 0.88490.929 0.875 differentdistributions of vintages of carsacross states, and Theregressions are identical to those reported in tables 2 and3, butuse the instrumental variables (the lawdummies) as regressors,rather than the (endogenous) seat beltusage. All othercontrol variables and the fraction of trucks among all registered vehicles. None of state Ž xed-effectsare included. ***,**,*:signi Ž cantwith 1%, 5% and 10% con Ž dencelevel, respectively. the additional controls signi Ž cantly in uenced our esti- Robuststandard errors below estimates. mates.W ealso ran the samespeci Ž cation afterreplacing our usage data with those of the BRFSS. The results had the samepatterns forthe coef Ž cients, as wellas similarpoint the differenttime windows, and arequite similarto those estimates. In addition, weran a Ž rst-differenceregression obtained in our reported regressions (third and sixth col- instead of a Ž xed-effects regression to take into account umns of tables 2and 3). This is also the case ifweomit from serialcorrelation problems, and the results werenot much our sample the years around the law, which addresses any changed (although their signi Ž cance levels decreased). possible concern that the exact timing of the lawis not well Wehave also devoted attention to the issue of functional identiŽ edby the annual level dummy variable. form.Earlier studies showed that less carefuldrivers areless Wealso investigate statistically the validity of the instru- likely to use seat belts. Thus, drivers that areleast likely to ments. Weargued earlierthat the timing of the passage of use seat belts might be those that aremore likely to be the lawis exogenously determined and is unrelated to involved in an accident. Ifthis is the case, then it can be preceding trends in fatalities. To test this, werun different expected that increasing seat belt usage from,say ,80% to hazard models, looking fora relationship between the pas- 90% will save morelives than the lives saved by increasing sage of the lawand some trend in fatalitiesthat may have usage from20% to 30%. Inother words, it might be argued preceded it (controlling forobservable variables and state that the relationship between fatalitiesand usage rateis Ž xed effects).W e Ž nd no statistically signi Ž cant evidence concave. In contrast, our log-log speci Ž cation assumes a that such arelationship exists, which is consistent with our convex relationship; the log-log speci Ž cation implies that discussion in section IVand with the assumption that the the samepercentage point increase in usage ismoreeffec- timing of the passage of seat belt legislation is exogenous. tive atlow levels of usage. In examining whether this poses Similarly,one might be concerned that mandatory seat aproblem forour conclusions, note Ž rst that the linear belt laws have effectson fatalitiesother than their effect speciŽ cation provides very similarresults to the log-log through the increase inusage. For example, the passage of speciŽ cation. Moreover, as atest, weincluded in our log-log mandatory seat belt laws might be accompanied by agen- speciŽ cation two morevariables —alinear termfor usage, eralcampaign fortraf Ž csafety,thus making drivers more and the logarithm of 1minus the usage. The coef Ž cients on attentive to safety issues. Although there is no formaltest to these variables turned out to be very low and completely check whether this is the case, table 5reports the reduced- insigniŽ cant, without much change in the estimated coef Ž - form coefŽ cients when fatalitiesare regressed directly on cient on the original logarithmic term,thus providing sup- the instruments, namely the lawdummy variables. Ifthe port forthe log-log speci Ž cation. assumptions arecorrect and the laws affectfatalities only Another possible concern is that our identi Ž cation forthe through seat belt usage, then it will be possible to approx- usage variable might be driven by long-term within-state imatetheir effecton fatalitiesby calculating it indirectly differences and not by the actual change in the mandatory through the effecton usage (ascan be calculated fromthe seat belt laws. In unreported regressions weestimate the results reported in tables 2, 3, and 4). Indeed, back-of-the- coefŽ cients on usage forboth occupant and nonoccupant envelope calculations suggest that there is no majordiffer- regressions fordifferent choices of timewindows around ence in the order of magnitude of the average effectof the the passage (orchange) of the mandatory seat belt law. lawif wecalculate itfromthis regression ratherthan from Although the coef Ž cients arenaturally not the same,their the results reported in tables 2, 3, and 4. magnitude and their signi Ž cance level arequite stable over The only remaining puzzle concerns the positive and highly signi Ž cant coefŽ cient on the primaryenforcement 34 Full regression reports of these tests will be provided by the authors dummy forthe nonoccupant regression in the logarithmic upon request. regression reported in table 5. This coef Ž cient seemsquite THE EFFECTS OFMANDATORY SEATBELTLAWS 841 robust, even when weinclude usage in the regression, as better guide forpolicymaking in this areathan the estimates wellas fordifferent choices of subsamples. 35 Taken atface currently used by policymakers. value, this coef Ž cient might suggest that some sort of Finally,our work enables us to identify and measurethe Peltzmaneffect does exist, and it replicates some of the effectsof various featuresof mandatory seat belt laws on the results in the existing literature. However, the result disap- laws’ effectiveness in increasing seat belt use. In particular, pears with alinear speci Ž cation, and given our results for having primaryenforcement can considerably enhance this usage, it seemsthat this is not the right interpretation, but effectiveness. Our estimatesindicate that the national usage ratherthat there is something else, leftunexplained, that would increase from68% to 77%, and 500 –1200 lives makes nonoccupant fatalitiesgo up when primaryenforce- would be saved annually,ifall states now having secondary ment laws arepassed. This highlights the importance of our enforcement moved to primaryenforcement. Thus, the re- point that incorporating usage data isessential fora rigorous cent initiative by the federalgovernment to encourage states test of the Peltzman effect. toadopt primaryenforcement is worthwhile.

REFERENCES VI.Conclusions Asch, Peter, David T.Levy, Dennis Shea, and Howard Bodenhorn, “Risk Compensation and the Effectiveness of Safety Belt Use Laws: A This paper uses aunique data set on seat belt usage in Case Study of NewJersey , ” Policy Sciences 24:2 (1991), 181 –197. order to estimatethe effectiveness of mandatory seat belt Bhattacharyya, M.N.,and Allan P.Layton, “Effectiveness of Seat Belt laws. Incontrast to earlierwork, weanalyze separately the Legislation on the Queensland Road Toll —An Australian Case Study in Intervention Analysis, ” Journal of the American Statisti- effectof such laws on seat belt usage levels and the effects cal Association 74:367 (1979), 596 –603. of usage on fatalities, weallow forthe endogeneity of Blincoe, Lawrence J., and B.M.Faigin, “The Economic Costs of Motor usage, and wetake advantage of the variation in the laws Vehicle Crashes 1990, ” HS 807-876, U.S. Department of Trans- portation (1992). across states. Along the way, wereplicate certain results Campbell, B.J., “The Association between Enforcement and Seat Belt obtained in past work and show why the inference of Use,” Journal of Safety Research 19 (1988), 159 –163. signiŽ cant compensating behavior drawn fromthem was Campbell, B., J.Richard Stewart, and Frances A.Campbell, “Early Results of Seat Belt Legislation in the United States of America, ” not always warranted. University of North Carolina Highway Safety Research Center Our data set and empiricalstrategy enable us to test working paper no. A-123, Chapel Hill, NC(1986). Center for Disease Control, “Behavioral Risk Factor Surveillance — directly the theory of compensating behavior suggested by Selected States, 1984, ” Morbidity and Mortality Weekly Report 35 Peltzman (1975). Incontrast to the predictions of the theory, (1986), 253–254. we do not Ž nd any evidence that higher seat belt usage has Dee, Thomas S., “Reconsidering the Effects of Seat Belt Laws and Their Enforcement Status, ” Accident Analysis and Prevention 30 (1998), a signiŽ cant effecton driving behavior. 1–10. Our results indicate that, overall, mandatory seat belt Department of Transportation, “Regulatory Impact Analysis of FMVSS laws unambiguously reduce traf Ž cfatalities. Weestimate 208: Occupant Crash Protection, ” Washington, DC(1984). Derrig, Richard A., Maria Segui-Gomes, Ali Abtahi, and Liu Ling-Ling, that a1-percentage-point increase in usage saves 136 lives “The Effect of Population Safety Belt Usage Rate on Motor annually (using alinear speci Ž cation), and that a1% in- Vehicle–Related Fatalities, ” Accident Analysis and Prevention 34 creasein usage reduces annual fatalitiesby about 0.13% (2002), 101–110. Evans, Leonard, “The Effectiveness of Safety Belts in Preventing Fatal- (using alog-log speci Ž cation). These estimates imply that ities,” Accident Analysis and Prevention 18 (1986), 229 –241. about 1500–3000 lives would be saved annually ifthe “Belted and Unbelted Drivers Accident Involvement Rates Com- national seat belt usage wereto increase from68% to the pared,” Journal of Safety Research 18 (1987), 57 –64. Evans, Leonard, and Paul Wasielewski, “Risky Driving Related to Driver (still unattained) target level of 90%. and Vehicle Characteristics, ” Accident Analysis and Prevention 15 Our estimates of the potential savings in lives from (1983), 121–136. increased seat belt usage areless than half of the estimate Evans, William N.,and John D.Graham, “Risk Reduction or Risk Compensation? The Case of Mandatory Safety-Belt Use Laws, ” used by the National Highway Traf Ž cSafety Administration Journal of Risk and Uncertainty 4:1 (1991), 61 –73. (NHTSA).The signi Ž cant differencebetween these esti- Garbacz, Christopher, “Estimating Seat Belt Effectiveness with Seat Belt Usage Data from the Center for Disease Control, ” Economics matesresults fromthe factthat the NHTSAuses 45% as the Letters 34 (1990a), 83 –88. estimated elasticity of seat belt usage. This value is based on “HowEffective is Automobile Safety Legislation? ” Applied the actual usage asestimated fromthat of drivers involved Economics 22 (1990b), 1705 –1714. “Impact of the NewZealand Seat Belt Law, ” Economic Inquiry 29 in trafŽ cfatalities. This estimatediffers from the one cal- (1991), 310–316. culated in observational studies and used forthe calculation “More Evidence on the Effectiveness of Seat Belt Laws, ” Applied of the national usage rate.Thus, our estimates provide a Economics 24 (1992), 313 –315. Graham, John D., Kimberly M.Thompson, Sue J. Goldie, Maria Segui- Gomez, and Milton C.Weinstein, “The Cost-Effectiveness of Air 35 In fact, the signi Ž cance of the primary dummy in the nonoccupant Bags by Seating Position, ” Journal of American Medical Associ- regression, together with the insigni Ž cance of the usage rate in the IV ation 278:17 (1997), 1418 –1425. regression, makes the primary dummy invalid as an instrument in the Harvey,Andrew C.,and James Durbin, “The Effect of Seat Belt Legis- nonoccupant regression that is reported in table 3. Still, the secondary lation on British Road Casualties: ACase Study in Structural Time dummy remains avalid instrument, and using it alone as an instrument for Series Modeling, ” Journal of the Royal Statistical Society Series the nonoccupant regression does not alter the results. A—Statistics in Society 149:3 (1986), 187 –210. 842 THEREVIEW OFECONOMICS AND STATISTICS

Houston, David J., Lilliard E.Richardson Jr., and Grant W.Neeley, c % Hispanics—the percentage of people of Hispanic origin in the “Legislation Traf Ž cSafety: APooled Time Series Analysis, ” Social state population. Science Quarterly 76:2 (1995), 328 –345. c Mean age—in years. Hunter, William W.,Jane C.Stutts, J. Richard Stewart, and Eric A. c Median income —in current U.S.dollars. Rodgman, “Characteristics of Seat Belt Users and Non-users in a State with aMandatory Belt Use Law, ” Health Education Re- search: Theory and Practice 5(1990), 161 –173. 2.b Data obtained from the annual publication Highway Statistics Insurance Information Institute, The Fact Book: Property/Casualty Insur- ance Facts, Annual Publication (1990 –1998). Levitt, Steven D., “The Effect of Prison Population Size on Crime Rates: c TrafŽ cdensity rural —registered vehicles per unit length of rural Evidence from Prison Overcrowding Litigation, ” The Quarterly roads in miles. Journal of Economics 111:2 (1996), 319 –351. c TrafŽ cdensity urban —registered vehicles per unit length of urban Levitt, S.D., and J. Porter, “Sample Selection in the Estimation of Air roads in miles. Bags and Seat Belt Effectiveness, ” this REVIEW 83:4 (2001), 603 – c VMT rural—vehicle miles traveled on rural roads. 615. c VMT urban—vehicle miles traveled on urban roads. Loeb, Peter D., “The Effectiveness of Seat Belt Legislation in Reducing Injury Rates in Texas, ” Economic Analysis of Safety and Health Regulation 85:2 (1995), 81 –84. 2.c Data obtained from the Bureau of Labor Statistics (BLS) McCarthy, Patrick S., “Public Policy and Highway Safety: ACity-Wide

Perspective, ” Regional Science and Urban Economics 29 (1999), 36 231–244. c Unemployment rate. National Highway Traf Ž cSafety Administration, Estimating the Bene Ž ts from Increased Safety Belt Use (Washington, DC,Department of Transportation, 1994). 2.d Data obtained from the Department of Justice Legislative History of Recent Primary Safety Belt Laws (Wash- ington, DC,Department of Transportation, 1999). c Violent crimes —number of violent crimes per capita (homicide, Patryka, S., “Mandatory Belt Use Laws in 1985, ” Journal of The Amer- rape, and robbery). 37 ican Association for Automotive Medicine 9(1987), 10. c Property crimes —number of property crimes per capita (burglary, Peltzman, Sam, “The Effects of Automobile Safety Regulation, ” Journal larceny,and auto theft). 37 of Political Economy 83 (1975), 667 –725.

“The Effects of Automobile Safety Regulation: Reply, ” Journal of 38 Economic Issues 11:3 (1977), 672 –678. 3. Other Related Laws Risa, Alf Erling, “Adverse Incentives from Improved Technology: Traf Ž c Safety Regulation in Norway, ” Southern Economic Journal 60:4 3.a Data obtained from Insurance Information Institute (1990 –1998) (1994), 844–857. Ruhm, Christopher J., “Are Recessions Good for Your Health? ” The c 65 mph speed limit —adummy variable that is equal to 1for 65-mph Quarterly Journal of Economics 115:2 (2000), 617 –650. Sen, Anindya, “AnEmpirical Test of the Offset Hypothesis, ” Journal of top speed limit in the state (55 mph is the base category). c 70 mph speed limit or above —adummy variable that is equal to 1 Lawand Economics 44:2 (2001), 481 –510. Singh, Harinder, and Mark Thayer, “Impact of Seat Belt on Driving for 70-mph or higher top speed limit in the state (55 mph is the base category). Behavior,” Economic Inquiry 30 (1992), 649 –658. Traynor, Thomas L., “The Peltzman Hypothesis Revisited: An Isolated c BAC is 0.08—adummy variable that is equal to one for amaximum of 0.08 blood alcohol content (0.1 is the base category). Evaluation of Offsetting Driver Behavior, ” Journal of Risk and Uncertainty 7:2 (1993), 237 –247. c Fuel tax—the tax on fuel (in current cents). c MLDAof 21 years —adummy variable that is equal to one for a Wagenaar, Alexander C., Richard G.Maybee, and Kathleen P.Sullivan, “Mandatory Seat Belt Laws in Eight States: ATime-Series Eval- minimum legal drinking age of 21 years (18 years is the base category). uation,” Journal of Safety Research 19 (1988), 51 –70. Wilde, Gerald J.S., “The Theory of Risk Homeostasis: Implications for Safety and Health, ” Risk Analysis 2(1982), 209 –225. 4. Elements of the Mandatory Seat Belt Law

DATA APPENDIX 4.a Data obtained from Insurance Information Institute (1990 –1998)

In this appendix, we describe all the variables used in the analysis c Secondary dummy —adummy variable that is equal to 1for the (those which are used in the reported regression and those which were periods in which the state had asecondary-enforcement mandatory eventually excluded), motivate their use when necessary, and provide descriptive statistics for the continuous variables. 36 State-level data on unemployment rates are supposed to capture general economic conditions, and they indeed proved to be important in 1. Fatalities previous papers in explaining fatalities. 37 We obtained data on crime (split between violent crime and property 1.a Data obtained from the Fatalities Analysis Reporting System crime) in order to capture unobserved characteristics of the population, as (FARS) well as police activity or law enforcement level. There can be two different interpretations for the crime data as aproxy for police activity. c Nonoccupant fatalities —the number of traf Ž cfatalities of pedestri- One might suggest that ahigher crime rate is likely to be associated with ans and bicyclists. alarger police force, which in turn makes violating the traf Ž c laws more c Occupant fatalities —the number of traf Ž cfatalities of drivers and difŽ cult. One might also suggest that ahigher crime rate shifts police passengers (of any seating position) of amotor vehicle in transport. away from enforcement of traf Ž claws, and hence makes violations easier. Given that we use the crime rate only as acontrol variable, we do not 2. Controls discuss these two effects. 38 We obtained data on the status of other relevant laws —such as speed 2.a Data obtained from the U.S. Census limits, limits on alcohol drinking while driving, minimum legal drinking age, and tax on fuel —in order to isolate the effect of mandatory seat belt c % Blacks—the percentage of African-Americans in the state popu- laws from those of other laws that might have adirect or indirect effect on lation. driving. THE EFFECTS OFMANDATORY SEATBELTLAWS 843

TABLE A1.—DESCRIPTIVE STATISTICSFOR THE CONTINUOUS VARIABLE Within Number of Variable Mean Std. Dev. Min Max Std. Dev. Observations a % Blacks 10.79% 12.05% 0.25% 68.86% 0.43% 765 % Hispanics 5.44% 7.45% 0.47% 39.92% 0.85% 765 Mean age 35.14 1.70 28.23 39.17 0.68 765 Medianincome 17,992 4,811 8,372 35,863 3,852 765 TrafŽ cdensityrural 0.33 0.22 NAb 1.11 0.05 765 TrafŽ cdensityurban 1.52 0.52 0.62 3.74 0.15 765 VMT rural 16,566 12,588 NAb 64,939 2,252 765 VMT urban 24,882 33,246 980 230,541 6,108 765 Unemploymentrate 6.25 2.05 2.23 18.02 1.53 765 Violentcrimes c 0.30 0.65 0.02 5.06 0.14 765 Propertycrimes c 3.00 5.71 0.13 42.78 0.53 765 Fuel tax 16.24 4.96 5.00 39.00 3.60 765 Seat beltusage 52.89% 17.02% 6.00% 87.00% 13.43% 556 CDC usage 71.04% 15.50% 27.78% 95.24% 11.62% 485 Occupantfatalities 707.85 695.80 24.00 4,398.00 101.38 765 Nonoccupantfatalities 139.12 188.96 3.00 1,220.00 26.20 765 Occupantfatalities perVMT d 18.34 5.53 6.34 37.52 3.41 765 Nonoccupantfatalities perVMT d 3.15 1.63 0.46 10.27 0.94 765 a All variableshave 765 observations, which stand for 15 years(1983 –1997),in the 51 states. Theseat beltusage is theonly exception, and is notfully covered for the early years (see section III). b Thereare no rural areas in the District ofColumbia. c Numberof crimesper 1,000 people. d Fatalities per1,000 vehicle miles traveled.

seat belt law, or aprimary-enforcement law that preceded by a 5. Usage secondary-enforcement law (no seat belt law is the base category). 5.a Data obtained from states ’ observational surveys, from the c Primary dummy —adummy variable that is equal to 1for the periods National Highway Traf Ž cSafety Administration (NHTSA), and in which the state had aprimary-enforcement mandatory seat belt from the Center for Disease Control (CDC)(for more details see law that was not preceded by asecondary-enforcement law (no seat Section III). belt law is the base category). c Secondary-to-primary dummy —adummy variable that is equal to 1 c CDCseat belt usage —the frequency of seat belt usage, as self- for the periods in which the state had aprimary-enforcement reported by state population surveyed. mandatory seat belt law that was preceded by asecondary enforce- c Seat belt usage —the observed percentage of front-seat passengers ment law (no seat belt law is the base category). who use seat belts.