Georgia Institute of Technology
This paper explores aspects of highway safety with a focus on crashes involving older drivers. As the "baby boomers" age and move into retirement, a larger proportion of older drivers will be using the nation's roads. The analysis here develops and estimates econometric models using a panel dataset that includes each county in California and spans an 18-year period, 19811998. The models are estimated using feasible generalized least squares techniques that account for cross-section heterogeneity, adjust for county-specific first-order serial correlation, and correct for nonconstant variances due to the large differences in county sizes across the state. The results indicate that the set of explanatory variables for crashes involving older drivers is not identical to the set for crashes involving younger drivers. Among the factors that have large effects on older driver crashes are risk exposure, energy and alcohol prices, alcohol availability, and increased speed limits on higher speed roads.
As the U.S. population ages, the proportion of older drivers on our nation's highways increases. Between 1986 and 1996, the total number of older drivers grew by 45% in comparison with a 13% increase in the total number of licensed drivers. Although we would expect a higher proportion of older drivers to affect the distribution of crashes, existing literature does not address this subject in great detail. It is well known, for example, that older drivers have less exposure and, accordingly, fewer crashes. At the same time, physical disabilities, a greater consumption of legal medication, and slower reaction times have all led to higher crash rates among the elderly relative to their younger driver counterparts (McCloskey et al. 1994; Hu et al. 1998; Lundberg et al. 1998). In order to continue developing public policy that is relevant to current and future characteristics of highway users, policymakers can benefit by gaining a better understanding of the causes of crashes among older drivers and how changes in policies may affect the distribution of crashes in this group.
The broad objective of this research is to study the relationship between highway safety public policy and highway crashes among older drivers. More specifically, this study focuses on the policies related to increased speed limits and those affecting the monetary and time (i.e., resource) costs associated with driving under the influence of alcohol.
A number of papers have analyzed the deterrent effects of legislation that have increased the penalties associated with drinking and driving or the enforcement of drinking and driving laws. Among the more recent analyses, Chaloupka et al. (1993) found that restrictive administrative per se (APS) laws significantly reduced alcohol-related crashes. Under APS laws, a driver's license is revoked or suspended if his or her blood alcohol concentration (BAC) level equals or exceeds the state legal limits, a sanction that is independent of other penalties if the driver is convicted. Other per se sanctions (mandatory jail sentences and community service laws) were ineffective. Legge and Park (1994) concluded that APS and other per se laws have the largest impact on single-vehicle nighttime crashes, whereas laws requiring some jail time for a first conviction or a fine for a first offender had no effect. Zador et al. (1989) also found that APS and other per se laws reduced fatal crashes. Peck (1991) found California's license suspension program has been more effective than alcohol rehabilitation programs in reducing crash risk for driving under the influence (DUI). Rogers (1995) concluded that reductions in the BAC level were effective. In contrast to most of this literature, Evans et al. (1991) found no evidence that sanctions contained in "punitive legislation" were effective deterrents of traffic fatalities.
There is also a significant literature on the highway safety effects of raised speed limits on higher speed roads (e.g., U.S. Interstate highways and the German autobahn), much of which is summarized in two Transportation Research Board reports (1984, 1998). As a result of the 1970s energy crisis, maximum speed limits on U.S. Interstates were federally set in 1975 at 55 mph. Complementing the savings in energy, this policy reduced fatal crashes, and the 55 mph speed limit continued long after the energy crisis was over. In 1987, Congress passed legislation that permitted states to raise the speed limit to 65 mph on rural Interstate highways. U.S. speed limits were again relaxed in 1995, when Congress ceded to states the authority to set speed limits on higher speed roads. Existing literature indicates that higher speed limits increase average speeds, but the speed increase is typically less than the increase in limits (e.g., the 10 mph increase in 1987 speed limits generally resulted in a 4 mph increase in average speeds). The extensive literature on the 1987 increase and the available, but more minimal, literature for the 1995 relaxation indicate that higher limits produce more fatal crashes and fatalities on the affected roads (McCarthy 2000). However, there is much less certainty about the systemwide effects of raising speed limits on higher speed roads due to "tainting" and "diversion" effects.1
Notwithstanding the extensive literature on the effects of alcohol-related and speed limit policies, with some focus on the younger driver, these studies say little about the impact of highway safety policy on older drivers.
This analysis uses the state of California as a case study for evaluating highway crashes among older drivers. For this analysis, an older driver is defined as a driver who is 60 years of age or older. The cross-section unit of observation in the analysis is a California county and the time period is one year. In total, the analysis includes 58 counties over an 18-year period (1981 through 1998), resulting in a total of 1,024 observations. Among the sources of data for this study were the California Highway Patrol (crash data), the California Bureau of Criminal Statistics (arrest data), the California Department of Alcohol Beverage Control (alcohol license data), the California Department of Finance (demographic data, price indexes, per capita county income), and the California Department of Labor (unemployment rates).
Table 1 provides definitions of the variables used in this study. Table 2 gives descriptive statistics for the dependent variables.2 Each of these variables is subdivided into two broad age groupsthose involving drivers 60 years of age or older ( older drivers) and those involving drivers less than 60 years of age ( younger drivers).
Included in table 2 is the overall mean of the variable in the sample and three measures of variation. The overall measure is the standard deviation across all groups and time periods. The "across-counties" measure is the standard deviation across the 58 counties (i.e., averaging over the 18-year period for each county and then calculating the measure of variation), and the "across-years" measure is the variation across the 18-year period (i.e., averaging all counties for each year and then calculating the measure of variation over the period).
Looking at the means, we see that younger drivers were involved in over six times as many crashes per county per year as older drivers, 7,492 versus 1,195. (The younger population is also about 6 times the size of the older population, but younger drivers account for 7.6 times as many vehicle-miles traveled (vmt) as older drivers.) This ratio was also true for fatal crashes. On average, there were 61 fatal crashes per county-year involving younger drivers compared with 11 fatal crashes involving older drivers. Nonfatal injury and property damage only (PDO) crashes show similar patterns between the two groups of drivers. Also not surprisingly, the overall and across-counties measures of variation are very similar, whereas the across-years variation is an order of magnitude smaller. An across-counties measure that virtually mimics the overall measure is not surprising, because it reflects the large variation in population and vmt across counties, as does the overall measure.
In contrast, the across-years measure reflects the average variation across the time period. We would expect that for any given county, the year-to-year variation in crashes would be relatively small, which is consistent with the results reported in table 2.
Table 3 provides summary statistics for the explanatory variables used in the econometric analysis.3 For the entire panel, average per capita income was $13,736 and the annual countywide unemployment rate was relatively high at 10%. The mean price index for gasoline was close to its base index value of 100, whereas the mean price index for alcohol was 28% above the base level.
Looking at the exposure-related variables, annual estimated per-county travel for older drivers, who made up 16.8% of the population, averaged 501 million vmt, whereas estimated per-county average vmt for younger drivers was substantially higher at 3.8 billion vmt. Population density averaged 560 persons per square mile.4
In addition to the price index for alcohol, the analysis includes two alcohol-related variablesthe number of retail establishments selling alcohol and the number of misdemeanor and felony arrests for DUIs. Overall, there are over 14,000 licenses to sell alcohol per county, but the overall and across-counties standard deviations are quite high. This reflects the large variation in population, and, therefore, alcohol consumption, across counties. On the other hand, if we normalize for population, as is done for per capita DUI arrests, we see that, based on an overall mean of 0.013 arrests per capita, the across-counties and across-years variations are equal0.005 in each case.
The model also includes four regulatory variables that are specific to driving under the influence of alcohol and to highway speeds. These variables do not have an across-counties measure, which reflects the fact that these are statewide rather than county laws so there is only temporal and no cross-section variation in these variables.
Assembly Bill 541 (AB541) was an omnibus bill that increased various penalties for driving under the influence of alcohol. Senate Bill 1623 (APS) enacted an administrative per se BAC level at 0.08 under which a driver's license is immediately revoked upon arrest for driving with a BAC equal to or greater than 0.08 regardless of whether the person demonstrates any behavioral signs of alcohol impairment.5 Respectively, AB541 and APS were active for 94% and 50% of the time period covered in this analysis.
In addition to these laws, California relaxed speed limits on its high-speed roads. In 1987, California increased speed limits on rural Interstates from 55 mph to 65 mph, and, on selected roads, it raised speed limits from 65 mph to 70 mph in 1995. These two laws were active 66% and 16.6% of the time during the 18-year period.
The econometric formulation for this study assumes that crashes among older drivers, yit , are a function of a set of explanatory variables, xit , and can be expressed as
yit = α + β' χit = ui + eit i = 1,....,58; t = 1981,...,1998 (1)
where i indexes the county and t indexes the year. α is a scalar parameter and β is a parameter vector, both of which are to be estimated. eit is an error term assumed to have a mean of zero and a constant variance. For a given county, i , the term ui is constant over time but is assumed to vary by county. Depending on the distribution assumption associated with u i , the resulting statistical model will either be a fixed-effects or a random-effects model. If ui ( i = 1,..., I ) is assumed to be a fixed parameter, then, in addition to α and β, the model estimates each effect ui (normalizing on one of the cross sections). The estimator for this model is also referred to as the across-years estimator because it is equivalent to estimating the
(i = 1,...,I ; t = 1,...,T ).
Alternatively, if ui is assumed to vary randomly (e.g., the cross-section units are a sample from a larger set of cross-section units), then the model's error term becomes ( ui + eit ), which is assumed to satisfy the standard assumptions of a zero mean, constant variance, and zero correlation with the explanatory variables. The choice between fixed effects and random effects specification generally revolves around the correlation between ui and xit in the random effects specification. In particular, if the random effect ui is correlated with the vector of explanatory variables xit (i.e., corr( ui , xit ) ≠ 0), then the parameter estimates are unbiased, but the standard errors are biased and we have no confidence in our t -statistics.
How can we determine whether the independence assumption between ui and xit is reasonable? Theoretically, the issue hinges on whether there are unobserved time-invariant effects that are correlated with a subset of the included variables. In a fixed effects specification, ui is a fixed parameter and the correlation between ui and xit does not affect the model's properties. However, in a random effects specification, ui reflects time-invariant effects that become part of the error structure. If these effects are correlated with the set of explanatory variables, biases in the standard errors arise. As an example, consider a county's topography, which is time invariant. Counties with less mountainous terrains will likely have greater vmt. Thus, a random effects specification will not be able to determine the extent to which higher crashes are due to more traveling and how much are due to unobserved topography.
In general, ui captures county heterogeneity, which means that it reflects the net effect of unobserved variables (e.g., topography in the above example or the presence of "through routes") on the dependent variable. Thus, in ui's picking up the influence of a variable that is correlated with an explanatory variable in the model, the independence assumption is violated and a random effects specification is not valid.
In addition to a fixed or random effects specification, panel data may suffer from serially correlated errors if the time span is sufficiently long and from heteroskedastic errors if the cross-section units have different scales. It is likely that the dataset for this analysis includes both problems, given the 18-year time horizon for these data and the fact that some counties in California are heavily populated (e.g., Los Angeles, San Diego, and San Francisco), whereas other counties have considerably smaller populations (e.g., Alpine and Tulare counties) and, accordingly, many fewer highway crashes. To account simultaneously for serial correlation and heteroskedasticity, a feasible generalized least squares (FGLS) approach provides an alternative estimator. The model for this estimator is
yit = αi + β' χit + eit i = 1,....,I; t = 1,...,T
eit = ρiei,t-1+ εit i = 1,...,I; t = 1,...,T
var(εit ) = σ2i i = 1,...,I; t = 1,...,T (2)
which accommodates fixed effects, first order serial correlation, and cross-section heteroskedasticity.6
For this study, fixed effects, random effects, and FGLS models were estimated. Since, theoretically and empirically, an FGLS specification provided the best fits to the data for older drivers, only these results will be reported.7 For each of the FGLS models, the estimation results and marginal effects of selected variables will be discussed. In addition to reporting results for older driver involved crashes, similar results will be reported for highway crashes involving drivers less than 60 years of age.
For crashes involving older drivers, table 4 and table 5 report the FGLS estimation results. In addition to estimating separate autocorrelation coefficients for each county and county-specific variances, these models include a full set of fixed effects for 57 of the 58 counties in California, normalizing on Yuba County. With regard to serial correlation, note that average estimated ρ varies across crash types and there is significant variation across counties, as reflected in the range of estimates for each crash type. For example, the estimated range of correlation coefficients varied from 0.46 to 0.47 for fatal crashes (with an average of 0.02), whereas the estimated range was 0.18 to 0.95 for PDO crashes (with an average of 0.71). This indicates there is likely to be significant bias in the variance estimates if the serial correlation is ignored.
Overall, the results reported in table 4 column (a) are consistent with expectations. For total crashes, an increase in real per capita income (Rpcinc) or unemployment rate (Uerate) has relatively little effect on crashes involving older drivers. But to the extent that an effect is present, a weaker economy is seen to increase the frequency of crashes. On the other hand, the price indexes for alcohol (Cpialc) and gasoline (Cpigas) have strong negative effects on total crashes. If all else remains constant, an increase in the consumption price of gasoline or alcohol reduces crashes involving older drivers.
As expected, risk exposure produces more crashes. From the results, we see that a 100 million vmt increase by older drivers (Vmtge60) leads to 39 more crashes involving older drivers. Further, we see that younger driver exposure has a similar effect on older driver crashes. Specifically, a 1 billion vmt increase in younger driver exposure (Vmtlt60) produces 33 additional total crashes involving older drivers. Also, the greater the share of the population that is older than 60 (Pctge60), the greater the number of crashes. Given that vmt is constant, this result is consistent with older drivers having reduced driving skills relative to their younger driver counterparts. However, as reported below, the share of the population that is older than 60 has a negative and significant impact on younger driver crashes. The positive sign for older (negative for younger) involved crashes suggests that this variable may be capturing an aspect of vmt exposure that is not reflected in the included aggregate vmt variable.8 Increases in population density are also associated with fewer older driver crashes. A 100-person increase per square mile (Popden) leads to 17 fewer crashes.
The last set of variables in table 4 column (a) relates to statewide alcohol and highway speed policies. First, and consistent with other research, alcohol availability (Alclic) is detrimental to highway safety, producing 1.6 additional crashes per 100 increase in the number of licenses. Second, the model includes two major pieces of alcohol-related legislation passed in California. AB541 was an omnibus bill that raised the cost of driving under the influence of alcohol in various ways and was California's first major effort at reducing drinking-and-driving crashes. The net effect on crashes was in the desired direction, leading to an average of 2.9 fewer crashes per county-year. On the other hand, APS, which implemented a 0.08 administrative per se law, has had no identifiable effect on total crashes.
DUI enforcement, defined as per capita arrests (Pc_dui), is significant but has an unexpected positive sign. There are three possible explanations for this. First, per capita arrests are the product of the probability of being stopped and the probability of being arrested given that one is stopped. Thus, a positive sign could result if an increase in arrests per stopped driver (reflecting, for example, police targeting DUI drivers) is associated with a contemporaneous decline in overall traffic enforcement (which reduces the likelihood of being stopped). Second, the effect on total crashes may reflect a net distribution effect on the different types of crashes. By inducing drinking drivers at the margin to behave less recklessly (e.g., consume fewer drinks, drive slower), more stringent enforcement, for example, could result in fewer fatal crashes but an increasing number of nonfatal crashes. Third, there may be an endogeneity problem in that an increase in crashes today leads to higher enforcement. Using a Hausman specification test statistic to test for endogeneity, the null hypothesis that Pc_dui was exogenous could not be rejected.9
The last two variables in table 4 column (a) identify the estimated effect of higher speed limits on crashes involving older drivers. The 65 mph speed limit (Slmt_65) had a positive but statistically insignificant effect on total crashes, whereas the more recent relaxation of speed limits (Slmt_70) produced a strong effect, generating four additional older driver crashes.
Column (b) in table 4 reports the FGLS estimation results for fatal crashes involving older drivers. Although the results are similar, there are some interesting differences. First, the state of the economy, whether it is measured by per capita income (Rpcinc) or the unemployment rate (Uerate), has a similar and somewhat stronger effect on fatal crashes than total crashes. Moreover, the effects are symmetric. Gains in per capita income and reductions in the unemployment rate both reduce fatal crashes. In that increases in income allow drivers to spend more on safer vehicles, better tires, and so forth to increase their level of safety (assuming that safety is a normal good) but drive faster and hence less safely (reflecting an increase in the value of time), the negative sign on Rpcinc implies that the safety effect dominates. And increases in gasoline (Cpigas) and alcohol prices (Cpialc) lead to fewer fatal crashes involving older drivers.
As expected, greater risk exposure produces more fatal crashes, where the results indicate that an increase of 10 billion vmt in total vmt produces an additional 2.8 fatal crashes among older drivers.10 But in contrast to the results in table 4 column (a), neither the share of older drivers nor the population density has significant effects on fatal crashes.
Turning to the regulatory variables, alcohol availability significantly increases the number of older driver-involved fatal crashes, but neither AB541 nor APS had an identifiable effect. At the same time, and in contrast to the results in column (a), increases in per capita DUI arrests reduce fatal crashes but the result was not statistically significant.11
Also in contrast to the results for total crashes, the effect of higher speed limits has opposite implications for fatal crashes. Although the 1987 speed limit relaxation had a marginal effect on total crashes, its effect on fatal crashes involving older drivers was stronger and significant, leading to a 0.71 additional fatal crash involving older drivers per county-year (or 41 annual fatal crashes statewide). The 1997 law, however, which allowed states to raise limits above 65 mph, although significantly increasing total crashes involving older drivers, had no effect on fatal crashes.
Table 5 columns (a) and (b) summarize the estimation results for nonfatal injury and PDO crashes. The results reported in column (a) for nonfatal injury crashes are similar to the results in table 4 column (a) for total crashes with a few exceptions. First, per capita DUI arrests has no effect on nonfatal injury crashes. Second, APS has a positive sign and is statistically significant, indicating that passage of the 0.08 administrative per se law actually increased nonfatal injury crashes involving older drivers. Theoretically, APS is expected to reduce crashes. The law mandates that police revoke the license of a driver arrested for a DUI offence and issue a 30-day temporary driving permit. Drivers pay minor fees to get their licenses reinstated. Also, other legislation passed in early 1990 reduced the BAC level from 0.10 to 0.08 as per se evidence of impaired driving and increased various sanctions for a DUI offense. By raising the expected cost of a DUI event, we would expect these laws to reduce the incidence of crashes, all else being constant. Although APS had little impact on total crashes, the positive and significant effect identified in table 5 column (a) is inconsistent with higher expected costs and may reflect the laws' distribution effects in the post-1990 driving environment.
Finally, table 5 column (b) reports the results for older driver PDO crashes. These crashes are most sensitive to the price index for gasoline, population density, the share of drivers 60 years of age or older, and the number of alcohol licenses. In addition, the best fit included total vmt, which found that a 100 million increase in vmt would lead to four additional PDO crashes involving older drivers. In this case, both AB541 and APS reduced the number of PDO crashes involving older drivers. Recall that APS was not significant for total crashes but was positive and significant for nonfatal injury crashes. In contrast to this latter result, in table 5 column (b), APS significantly reduces PDO crashes, which is consistent with expectations.12
For purposes of comparison, FGLS models were estimated for county crashes involving younger drivers. One difference in these models from those for the older drivers is that including a full set of fixed effects led to poorer model fits. In order to control for major sources of cross-section heterogeneity without including a full set of fixed effects parameters, the results in table 6 and table 7 include fixed effects for those counties that are part of a consolidated metropolitan statistical area (CMSA). In total, the models include 24 fixed effects parameters in addition to autocorrelation and variance parameters associated with each of the 58 counties.13 Similar to table 4 and table 5, the results in table 6 and table 7 reflect large variation in the average as well as the range of estimated serial correlation coefficients.
Table 6 columns (a) and (b) give the results for total and fatal crashes involving younger drivers. From a statistical perspective, the results are stronger in that the z -statistics for the significant variables reject the null hypothesis at higher levels of significance. There are a number of differences in total crash results between older and younger involved drivers. Some differences are:
A similar comparison of fatal crash determinants in table 4 column (b) for older involved drivers with that of younger involved drivers in table 6 column (b) also reveals a number of differences. In particular:
In the fatal crash equation, the two results that were unexpected but yet were robust to alternative specifications were the positive sign on APS and the positive sign on per capita DUI arrests. As noted earlier, the expectation was that APS would have a negative effect. Yet for total and fatal crashes for younger involved drivers, the sign and significance were robust.
For per capita DUI arrests, there is the possibility of endogeneity problems. This was explored in some detail for per capita arrests. Neither alternative variable specifications nor using "predicted per capita arrests" (based on a panel regression of per capita DUI arrests on the set of explanatory variables in the model) altered the finding in table 6 column (b). Further, fatal crashes were not found to be a significant determinant of per capita arrests in a panel regression analysis of arrests. This suggests that endogeneity is not a large problem. In contrast to expectations that per capita arrests decrease the most serious crashes at the cost of less serious crashes, there is some evidence that the reverse may have occurred. As seen in table 7 column (b), per capita arrests was negative and statistically significant, which, when combined with the fatal crash results, suggest a redistribution from less serious to more serious crashes. A possible explanation is that the police are targeting the wrong group in their DUI enforcement efforts.
Table 7 columns (a) and (b) summarize the estimation results for nonfatal injury and PDO crashes among younger drivers involved in crashes. For each of these models, the results generally have similar implications with respect to price, exposure, population density, the share of older persons in the population, alcohol availability, and regulatory variables. But there are qualitative differences regarding the effects of real per capita income (reducing injury but increasing PDO crashes) and the unemployment rate (which has no effect on injury crashes).14
Table 8 and table 9 report sensitivity measures associated with model variables in the older and younger driver groups, respectively. For crashes involving older drivers, table 8 provides several interesting insights. First, fatal crashes are an order of magnitude more sensitive to changes in gasoline and alcohol price indexes than are less serious crashes. A 10% increase in energy prices, for example, reduces fatal crashes 1.3% in comparison with an approximate 0.2% decrease in injury and PDO crashes. Second, older drivers are most likely to be involved in PDO crashes and least likely to be involved in a fatal crash as their risk exposure increases.15 Third, and consistent with the higher alcohol price sensitivity, fatal crashes among older drivers are more than twice as sensitive to alcohol availability in comparison with less serious crashes. A 4% increase in the number of retail licenses to sell alcohol results in an approximate 1% increase in injury and PDO crashes but a 2% increase in fatal crashes among older drivers. Fourth, the higher speed limits enacted in 1987 were detrimental to older drivers in that all types of crashes increased. However, the 1995 relaxation has had, to date, no impact on fatal crashes involving older drivers.
Table 9 reports the sensitivity measures for younger drivers involved in crashes. In this table, there are some interesting similarities and contrasts to those reported in table 8. First, crashes among younger drivers show sensitivities to gasoline and alcohol that are similar to those observed in table 8. Fatal crashes were most sensitive and an order of magnitude more sensitive than less serious crashes.
Second, although PDO crashes among younger drivers were most sensitive to increased exposure, there was a much smaller difference in fatal, nonfatal injury, and PDO crash sensitivity than was seen for older drivers.16 A further contrast with table 8 is that, in table 9, vmt elasticity for each crash type is almost an order of magnitude smaller. Crashes involving younger drivers were much less sensitive to risk exposure than those among older drivers.
Third, table 9 shows that an increased share of older persons in the population reduced all crashes and the largest effect is associated with fatal crashes. Combined with the results in table 4 and table 5, an increased share of older persons in the population redistributed crashes away from younger involved and toward older involved drivers.
Fourth, highway safety among younger drivers was sensitive to the availability of alcohol, as in the older driver group. For younger drivers, the pattern was similar to that for older drivers in that fatal crashes were most sensitive to alcohol availability. The difference in the level of sensitivity for younger involved drivers was approximately double that for older involved drivers.
Fifth, and also in contrast to the older driver results, AB541 was beneficial to younger driver highway safety regardless of severity level. Last, neither the 1987 nor the 1995 higher speed limits increased fatal crashes involving younger drivers, although the 1987 relaxation did increase the incidence of nonfatal injury crashes.
The objective of this analysis was to obtain some insights on economic and regulatory factors that are important determinants of highway crashes involving older drivers. With the "graying of America," older drivers will make up a larger proportion of the traveling population, and it is important to understand the impact this is likely to have on highway crashes, particularly those involving fatalities or injuries. Further, the study analyzed younger drivers in order to identify differential impacts that public policy may have on older versus younger driver-involved crashes. The major conclusions that are evident from this study are as follows.
Two modeling implications flow from this analysis. First, relative to fixed effects negative binomial methods, FGLS was used to estimate the models reported in this analysis. FGLS estimation comes at the cost of not directly accounting for overdispersion that is typical in crash data. For the models reported, normality tests were conducted on the errors and these tests uniformly rejected the null hypothesis, which likely reflects remaining problems with overdispersion.17 At the same time, negative binomial models that do not adequately account for heteroskedasticity and serial correlation are inefficient and will produce incorrect standard errors that invalidate standard hypothesis tests. Additional research needs to be done to better understand the tradeoffs and empirical importance in using alternative panel data estimation techniques.
Second, all of the models reported in this analysis focused on the impact that alternative explanatory variables had on the number of highway crashes. Alternatively, the focus could be on crash rates rather than levels. Each of the models reported in table 4, table 5, table 6 and table 7 were re-estimated using crash rates rather than levels.18 Qualitatively, the estimation results were broadly, but not uniformly, consistent with the results reported in these tables. Alcohol and gasoline price indexes had similar effects to that identified in this analysis. With respect to the alcohol policy variables, AB541 was uniformly negative in the rate equation, whereas APS had similar effects on crash rates as it did on levels, but these were not consistent. For crashes involving older drivers, the effects of the 1987 and 1995 speed limit increases were generally consistent with those for crash levels. This was not true for the younger group.19 Further, the effect on crash rates of an increase in the number of alcohol retail licenses was uniformly negative and always significant.
Further study is needed to establish the relationships between the effects that determining factors have on crash levels vis-à-vis crash rates. For example, consistent with expectations, increasing the number of alcohol licenses is expected to increase the number of crashes (all else remaining constant), because a larger number of licenses is expected to reflect greater alcohol consumption. However, an increase in the number of licenses could increase or decrease crashes per vmt, because crash rates are not controlling for vmt. In order to set appropriate highway safety policy for a growing older population, it is important to understand the effects that policies have on alternative measures of highway safety.
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Chaloupka, F., H. Saffer, and M. Grossman. 1993. Alcohol Control Policies and Motor Vehicle Fatalities. Journal of Legal Studies 22:161186.
Evans, W.N., D. Neville, and J.D. Graham. 1991. General Deterrence of Drunk Driving: Evaluation of Recent American Policies. Risk Analysis 11(2):279289.
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Legge, J.S. and J. Park. 1994. Policies To Reduce Alcohol-Impaired Driving: Evaluating Elements of Deterrence. Social Science Quarterly 75:594606.
Lundberg, C., L. Hakamies-Blomquist, D. Almkvist, and K. Johansson. 1998. Impairments of Some Cognitive Functions are Common in Crash-Involved Older Drivers. Accident Analysis and Prevention 30(3):371377.
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The research reported in this paper was sponsored by the National Institute on Alcohol Abuse and Alcoholism, National Institutes of Health, Grant #5R03AA012148-03. A previous version of this paper was presented at the 1st International Congress on Transportation Research in Athens, Greece, in February 2002. I would like to thank three anonymous referees and the Journal's Editors for their constructive comments and suggestions. I would also like to thank Aruna Srinivasan, a graduate research assistant in the School of Economics, who estimated the models reported in this paper.
Author address: Patrick McCarthy, School of Economics, Ivan Allan College, Georgia Institute of Technology, Atlanta, GA 30318. Email: firstname.lastname@example.org.
KEYWORDS: older driver, highway safety, public health, speed limits, alcohol policy.
1. Speed limit tainting effects occur when changes in speed limits on one set of roads (e.g., Interstate highways) not only induce increased actual speeds on the affected roads but also lead to speed increases on non-affected roads (e.g., arterials), that is, roads where speed limits did not change. Speed limit diversion effects occur when changes in speed limits on one road divert traffic to other roads, including the affected road. For example, a higher speed limit on rural Interstates is expected to divert some traffic from slower roads where speed limits have not changed to the Interstate highway's increased speed limit.
2. The dependent variable is defined in levels (i.e., number of crashes) in order to estimate the sensitivity of older and younger driver-involved crashes to changes in vehicle-miles traveled (vmt) exposure, which is not possible when the dependent variable is defined as a rate (e.g., crashes per 100 million vmt). Table 7 and table 8 show that crash sensitivity to vmt varies by age group as well as by crash type, which is discussed in more detail later in this paper.
3. A correlation analysis indicates that the explanatory variables are not in general highly correlated. With two exceptions, correlation coefficients are less than 0.50. Vmt measures, not surprisingly, are highly correlated. Also, the number of retail alcohol licenses is highly correlated with exposure measures, which reflects the relationship between population and alcohol licenses.
4. Because countywide vmt data do not exist for California, a methodology was developed to estimate age-gender vmt data by county from available aggregate annual vmt data for California. The procedure included the following steps: 1) using aggregate annual data, "vmt per driver" was regressed on a constant term, "% of statewide drivers ≥60," "% of statewide drivers ≤24," and "#persons per driver" ( R2 = 0.97 from this regression); 2) using countywide values for each of these explanatory variables, the regression model coefficients were used to predict the countywide vmt per driver; 3) countywide vmt was obtained by multiplying the number of drivers in each county by the estimated countywide vmt per driver. In order to allocate the estimated countywide vmt to various age-gender specific groups, data on the proportion of annual vmt per driver, disaggregated by alternative age-gender categories, were obtained from the Nationwide Personal Transportation Survey (NPTS) for 1983, 1990, and 1995. These data were then used to scale the estimated countywide vmt data. Specifically, NPTS data for 1983 (1990; 1995) were used to develop the weights for observations in this study during the period 19811986 (19871993; 19941998) to obtain vmt in each county for different age-gender groups.
7. A commonly used alternative methodology is a negative binomial model that accounts for the overdispersion property typically seen in highway crash data (and the data for this analysis are no exception) by relaxing the mean-variance equivalence property of the Poisson model. Fixed effects negative binomial models generally account for cross-section heterogeneity and overdispersion but not heteroskedasticity and serial correlation. FGLS, on the other hand, accounts for cross-section heterogeneity, heteroskedasticity, and serial correlation but does not address the overdispersion problem. As will be seen later, the estimated serial correlation coefficients varied across crash types and varied significantly across counties, which indicates that in models that fail to adjust for serial correlation, the coefficient estimates are inefficient and the estimated variances of the coefficients will be biased.
9. For a discussion of the Hausman specification test, see Pindyck and Rubinfeld (1991, p. 303304). Instrumental variables for per capita arrests included other explanatory variables in the model. As noted by the editors, in the present framework, endogeneity is a problem if an increase in the incidence of alcohol-related crashes leads to more enforcement, However, if the level of enforcement is determined independently by the extent of drinking and driving rather than crashes, then enforcement is an instrumental variable for drinking and driving and the positive sign is consistent with expectations. It is likely that both effects are operating to some degree, which is consistent with the mixed results obtained from the Hausman specification test.
10. In preliminary models, various vmt specifications were employed, including total vmt, older driver vmt, younger driver vmt, and logarithmic transformations. The results reported represent the best model fits. In contrast to the total crashes results reported in table 4 column (a) often the inclusion of both younger and older driver vmt led to robustness problems due to the high level of collinearity between these exposure measures.
11. For the fatal crashes equation, the hypothesis that Pc_dui was exogenous could be rejected at the 0.05 level. In this case, Pc_dui was regressed on a set of explanatory variables and the predicted value included in the fatal crashes equation.
12. As will be seen below for younger drivers, APS has strong positive effects across all crash types, which is consistent with the results for injury crashes among older drivers but inconsistent with expectations. Further research is needed to isolate the mechanisms through which APS affects crash frequency and severity.
13. In preliminary runs of the model, a full set of fixed effects for all but the normalized county led to convergence problems. Because many differences among counties are expected to reflect factors related to urbanization, a separate fixed effect was included for each CMSA county in order to capture this heterogeneity. For the reported models, the interpretation of the CMSA fixed effect parameters is the impact on crashes relative to all rural counties in California.
14. Similar to the total and fatal crash equations involving younger drivers, the effect of motorcycle registrations was consistently negative and significant in the PDO equations. Given the high fatality rate among motorcyclists (e.g., the number of fatalities per vmt was 26 times higher than passenger car occupants (USDOT 2002)), this result was unexpected and may be capturing part of the smaller total exposure among the motorcycle population in comparison with that of the motor vehicle population.
19. The results were robust for fatal crashes. However, in the level model for total crashes, the 1987 law coefficient was positive and significant (for the rate model it was negative and insignificant) and the 1995 law coefficient was negative and significant (positive and significant for the rate model). For injury crashes, the 1987 and 1995 laws carried opposite signs in the rate relative to the level models and were significant at a 0.10 level. For PDO crashes, the 1987 and 1995 laws in the rate model also had opposite signs from those in the level models, but only in the 1997 case was the coefficient statistically significant.