The effectiveness of vehicle safety inspections: an analysis using panel data.

Sutter, Daniel

1. Introduction

Economists have extensively analyzed the efficacy of policies intended to improve traffic safety. These policies include mandatory seat belt use, the speed limit, motorcycle helmet laws, the drinking age, and vehicle safety inspections. In this paper, we present new evidence on the effectiveness of state vehicle inspections. Since vehicle maintenance can confer an external benefit to other drivers by reducing the accident rate, individuals may voluntarily provide less than the efficient level of maintenance. Safety inspections attempt to correct the externality by ensuring that vehicles meet a specified maintenance standard. To examine the effect of inspection laws on fatality and injury rates, we used a panel of the 50 states for the years 1981-1993. Our empirical approach paid particular attention to the problem of omitted variables. Many factors causing driving conditions to vary across states can be difficult to quantify or may escape the attention of the researcher. The panel allowed us to control for these state-specific factors by estimating a fixed-effects model. In contrast, previous studies of safety inspections have not allowed for state-specific effects and are therefore vulnerable to omitted variables bias.

Contrary to a number of existing studies, our results indicated that inspections fail to significantly reduce fatality rates. We also went beyond the typical approach by estimating the effect of inspections on nonfatal injuries. Again, we found inspections ineffective. These results held whether the models used variables in their levels or in first differences. While our main empirical innovations pertain to inspections, our results also provide evidence of the effects of other policy variables such as speed limits and seat belt laws. We also found support for the Peltzman (1975) hypothesis that income and wealth increase accidents by stimulating driving "intensity" (heedlessness and speed).

Our estimates demonstrate the importance of modeling state-specific effects. The estimated fixed effects differ very significantly from zero and can affect inferences regarding the effectiveness of inspections. Specifically, if our empirical model omits fixed effects in the levels, the estimates attribute a significant reduction in fatalities to systematic inspections; this result disappears, however, if the model includes fixed effects.

This paper is organized as follows. Section 2 presents the econometric model. It also includes a brief history of state inspection programs and describes previous studies of safety inspections. Section 3 presents our results, and section 4 provides some estimates of the cost of annual inspections and discusses some implications of our research.

2. Modeling State Safety Inspection Programs

Two types of inspection programs exist: mandatory annual inspections and spot inspections, where law enforcement officers can at their discretion stop and inspect a vehicle. Annual inspections take place at a state-licensed repair shop, usually for a fee set by the state. In addition to the fee, drivers bear a time cost of inspection that includes queuing and the inspection itself (and reinspection if the vehicle fails). The inspection typically requires safety features such as headlights, turn signals, horn, and brakes to meet designated standards.(1)

Many states initiated spot or annual inspections after Congress in 1966 mandated withholding federal highway funds from states failing to adopt vehicle inspection programs. In 1977, Congress eliminated the threat to withhold highway funds, and several states subsequently eliminated inspection requirements.(2) Table 1 summarizes the changes in state inspection regimes during the period covered by our investigation. The number of annual inspection programs declined from 30 in 1980 to 23 in 1993. States made 20 shifts of inspection regime during the period; 15 different states experienced some form of regime shift. The variation in inspection regimes over time provided the basis for our econometric tests, described below.

Previous studies of the effectiveness of safety inspections have produced conflicting results. In fact, sorting these studies into categories corresponding to the use of time-series, cross-sectional, or pooled data shows that conflicting results exist within each category. Using cross-sectional data on the 50 states, Loeb (1985, 1988) found inspections effective while Crain (1980) did not. Keeler (1994) used county-level data and found inspections effective in 1970 but not in 1980. Loeb and Gilad (1984) found evidence that inspections were effective using time-series data for New Jersey. In national-level time series, Garbacz and Kelly (1987), Garbacz (1990), and Fowles and Loeb (1995) reported that inspections did not lower the fatality rate, whereas Loeb (1990) found inspections effective. Using pooled data, Leigh (1994) generated evidence against the effectiveness of inspections; Saffer and Grossman (1987) concluded that inspections reduced the fatality rate among young drivers.

Table 1. State Auto Inspection Programs, 1980-1993

Inspections States

Continuous Annual Inspection Arkansas, Delaware, Hawaii,
 Louisiana, Maine, Massachusetts,
 Mississippi, Missouri, New
 Hampshire, New Jersey, New York,
 North Carolina, Oklahoma,
 Pennsylvania, Rhode Island, South
 Carolina, Texas, Utah, Vermont,
 Virginia, and West Virginia

Continuous Spot Inspection Alaska, Iowa, Michigan, Minnesota,
 North Dakota, Oregon, and
 Wisconsin

No Inspections Performed Arizona, Idaho, Illinois,
 Kentucky, Montana, New Mexico, and
 Wyoming

States Altering Inspection Regime Alabama: add spot (1982);
 California: drop spot (1981);
 Colorado: drop annual (1982);
 Connecticut: add annual (1982);
 Florida: drop annual (1982);
 Georgia: drop annual (1982);
 Indiana: drop annual (1981), add
 annual (1982), drop annual (1984);
 Kansas: drop annual (1982), add
 spot (1984); Maryland: drop annual
 (1982); Nebraska: drop annual
 (1982); Nevada: add annual (1981),
 drop annual (1982); Ohio; drop
 spot (1989); South Dakota: drop
 annual (1981); Tennessee: add spot
 (1981), drop spot (1982);
 Washington: drop spot (1987)

Our empirical model takes the form

[f.sub.it] = [[Alpha].sub.i] + [Beta][prime][multiplied by][x.sub.it] + [[Epsilon].sub.it], (1)

where [f.sub.it] is the log of a casualty total in state i during year t and [[Epsilon].sub.it] is a white noise disturbance. The regressor matrix X consists of variables described below that may affect the accident rate. Our approach featured several advantages relative to prior studies of safety inspections. Most importantly, the panel enabled us to use dummy variables to estimate state-specific shifts in the fatalities intercept, [[Alpha].sub.i]. We wanted to allow for state-specific effects because the explanatory variables in X might not have captured all the factors influencing casualties across states. Many factors such as geography or policing effort can vary across states in a nonquantifiable manner. Tests using national-level time-series or cross-sectional data cannot allow for such state-specific effects.(3) To obtain consistent estimates, these studies require state-specific effects to be zero or at least to be uncorrelated with the explanatory variables. Our estimates indicate that the state-specific effects are significantly nonzero, and Hausman tests imply that they are not uncorrelated with the explanatory variables. Under these circumstances, a fixed-effects model is appropriate.(4) The fixed-effects model uses the variation in inspection regimes over time to separate the effects of inspection from those of factors varying only across states. None of the existing studies on the effectiveness of safety inspections have estimated a fixed-effects model.

Our empirical specifications also feature a wider set of explanatory variables, and our data cover more years and more recent years than previous studies modeling fatalities with pooled data (e.g., Snyder 1989; Michener and Tighe 1992). Furthermore, we estimated models of the rate of nonfatal injuries; previous research considered only fatalities.(5) A policy variable such as inspection could conceivably have differing effects on fatalities and injuries, especially if particular causal factors play a relatively greater role in certain types of accidents. For instance, inspected features such as horn and turn signals may reduce injuries by preventing low-speed accidents on local roads but have little effect on deadly high-speed accidents caused by factors such as reckless driving or environmental conditions.

We defined dummy variables, SPOT and ANNUAL, equaling I if a state had the particular type of inspection program and 0 otherwise. These variables permit the empirical model to attribute differing effects to the two types of inspection.(6) In contrast, some researchers impose the assumption that the different regimes have equivalent effects by representing both types with a single dummy variable, and many studies ignore spot inspection altogether.

Our tests also provide new estimates of the effects of several other policy variables.(7) Seat belt use reduces the probability of a fatal or serious injury conditional on an accident of given severity, but it can elevate accident likelihood and severity by increasing driving intensity (Peltzman 1975). Following Michener and Tighe (1992), we distinguished between two types of seat belt law: a primary law that empowers officers to stop a vehicle for failure to wear seat belts and a secondary law that requires additional justification for stopping a motorist. Dummy variables PRIBELT and SECBELT indicate the presence of primary or secondary seat belt laws. We also used variables representing the legal speed limit on rural interstate highways (LIMIT) and average vehicle speed (SPEED). The variable LIQUOR equals a state's legal age for purchasing hard liquor.

The specification also includes real per capita income (INCOME) and the percentage of new cars among registered autos (%NEWCARS). Income increases the demand for both maintenance and driving intensity, which exert opposing influences on fatalities. The percentage of new cars can similarly reflect both demand for safety (new cars have more safety features and experience fewer mechanical failures) and demand for driving intensity. Peltzman (1975) found that the intensity effect dominated (fatalities increased with income) in time-series regressions but that the safety effect dominated in cross-sectional regressions. Our panel data provided the opportunity for a new test of Peltzman's hypothesis.

Several control variables complete the model. The variable VSPEED measures the variance of speed; Lave (1985) found that this variable affected the probability of an accident. The percentage of vehicle miles traveled in urban areas (%URBAN) proxies for traffic density. Our reported models used total vehicle miles (VMILES) as a measure of scale; we also estimated models using state population as the scale variable. To control for road quality, we used the level of highway maintenance expenditures (MAINT) and also included a lagged value of this variable since road projects require time to build and probably have persistent effects on road quality. The population percentages of young and old (%YOUNG, %OLD) and the percentage of males among registered drivers (%MALE) proxy for driver skill and possible variation in preferences toward risk or driving intensity.

We also performed tests that focused on changes in fatalities and injuries at the time of changes in the law. We did this by estimating the models in first differences, regressing changes in log fatalities or log injuries on fixed-effect dummy variables, changes in the inspection law, and changes in the other explanatory variables. The differenced model may yield inferences more reliable than those of the levels model if the fatality or injury time series contains a significant unit root component. Moreover, estimating the model in first differences can provide a check against the problem of omitted variables. If an omitted variable changes over time, the fixed-effects model may suffer from bias in the levels but not in first differences. As a pure hypothetical situation, consider a variable measuring the public's knowledge of safe driving techniques. Suppose that the average growth rate of the public's knowledge differs across states and that, all else equal, states with high growth rates are relatively more likely to terminate inspections or relatively less likely to adopt inspections. Then, in the levels specification, knowledge correlates over time with the status of the inspection regime, resulting in omitted variable bias. The fixed effects in levels cannot model the effect of knowledge because its level is not fixed. We can, however, model variation in the average growth rate of knowledge across states as a fixed effect in first differences. The differenced specification can yield consistent estimates since states need not experience extraordinary knowledge growth during the specific years they happen to change inspection regime.

3. Techniques and Results

The pooled nature of our data creates the potential for problems of both heteroscedasticity and serial correlation. To help account for time dependency that might exist in the data and hence reduce serial correlation, we included a lagged dependent variable in all the models displayed in Tables 2 and 3. We also included a time trend since engineering improvements in roads and vehicles may create a downward trend in accidents. To obtain asymptotically valid inferences, we employed a Newey-West serial correlation and heteroscedasticity-consistent covariance matrix. Table 2 presents estimates of four econometric models of fatalities, in double log form, and Table 3 presents analagous results for nonfatal injuries. In both tables, columns a-c report ordinary least squares (OLS) coefficient estimates and Newey-West (1987) standard errors.(8)

Column d of Tables 2 and 3 presents maximum likelihood (ML) estimates of models that explicitly account for heteroscedasticity as a function of state size. The heteroscedastic models permitted us to pursue asymptotically efficient estimates rather than merely rely on consistency. Since efficiency requires specifying a correct functional form for the heteroscedasticity, the approach best suits a case where heteroscedasticity takes a simple form; hence, we assume a scedastic function of a single variable, with state size an obvious candidate. Indeed, Goldfeld-Quandt tests strongly attest to the presence of heteroscedasticity as an inverse function of state size. Given a dependent variable in log form, the result implies that casualty totals for smaller [TABULAR DATA FOR TABLE 2 OMITTED] [TABULAR DATA FOR TABLE 3 OMITTED] states experience larger random disturbances in percentage terms. Further examination of the OLS residuals suggests multiplicative heteroscedasticity of the form

[[[Sigma].sub.it].sup.2] = [[Sigma].sup.2][[n.sub.it].sup.[Gamma]], (2)

where [n.sub.it] corresponds to total vehicle miles in our reported models and state population in other models.(9) We used the ML technique to simultaneously estimate the scedastic parameter [Gamma] and the slope coefficients of the mean equation. Before discussing the results, we stipulate no relative preference for the ML or OLS results since the efficiency of ML holds only asymptotically and is subject to correct specification of the heteroscedasticity Equation 2. In any event, for our purposes, the two methods yielded similar inferences, as shown below.

To illustrate the role of fixed effects, we omit them from the estimated model in column a of Tables 2 and 3. Estimates of the full fixed-effects specification appear in column b. The fatality results underscore the importance of modeling state-specific effects.(10) Estimation of the model without fixed effects indicates that annual inspection reduces the fatality rate by about 2%, a figure differing significantly from zero at the 0.05 level. In the fixed-effect specification, however, the estimated effects of annual and spot inspections prove neither negative nor significant. The estimated coefficients for ANNUAL and SPOT are quite small and are insignificantly different from zero in the injury models, with or without fixed effects. The statistical insignificance of inspections remains robust across additional fixed-effect specifications, not reported, including those using state population as the scale variable.

Estimating fixed effects also reverses inferences on some of the other variables. Including fixed effects switches the income coefficient from significantly negative to positive and significant at the 0.01 level in the fatalities model and not quite at the 0.05 level in the injuries model. Omitting fixed effects suggests that raising the drinking age significantly increases fatalities, contrary to intuition. In the fixed-effect model, this result disappears as the coefficient proves smaller and statistically insignificant. The time trend, current maintenance expenditures, and %URBAN significantly affect fatalities only in the fixed-effects model, and the coefficients all have the intuitive sign.(11) The injuries models yield the reverse pattern for %URBAN: significant without, but insignificant with, fixed effects. The coefficient for %OLD proves significantly negative only in the fatalities model without fixed effects.

Several other control variables have significant estimated coefficients. The coefficient for lagged maintenance expenditures is significantly positive in the fatalities models; this counter-intuitive result may reflect the influence of some omitted variable or merely indicate that the rate of change, not just the level, of maintenance expenditures affects road quality. Lagged expenditures are not significant in the injuries models. The coefficient for new cars proves significantly positive in all fatalities and injuries specifications; these results, as well as the positive coefficients for income, concur with Peltzman's driving intensity hypothesis. The coefficient of the log of vehicle miles is significantly positive in the injuries models but not in the fixed-effects fatalities model. A lagged dependent variable proves very significant across models, indicating that fatalities and injuries exhibit considerable persistence over time.

Column c omits SPOT in order to focus on the role of systematic annual inspections. If spot inspections have no effect on casualty rates, then omitting SPOT can increase the efficiency of the estimate of the ANNUAL coefficient by eliminating the collinearity between ANNUAL and SPOT (every state with spot inspections has no systematic inspections). The model in column c also employs the legal speed limit (LIMIT) as an alternative measure of the effect of vehicle speed. The LIMIT variable is a positive and significant determinant of fatalities but not injuries. Otherwise, the results in column c remain essentially unchanged.

The ML estimates of the heteroscedastic models in column d reaffirm our inferences on the effectiveness of inspection. The estimates of the coefficients of ANNUAL and SPOT are insignificant for both fatalities and injuries. The remaining results concur with the OLS estimates, except that log of vehicle miles and INCOME attain significance at the 0.05 level in both models. These inferences remain robust across alternative specifications, including those using state population as the scale variable influencing the heteroscedasticity.

Our results cast doubt on the effectiveness of seat belt laws. In no regression presented here do the seat belt variables attain significance; they do, however, achieve significance in some models not reported here.(12)

The fixed-effect terms exhibit considerable joint significance, as implied by the Wald test statistics displayed in Tables 2 and 3. We could alternatively specify these state-specific effects as random, rather than fixed, effects. The random-effects model treats the state-specific effect, [[Alpha].sub.i], as a random component of a composite error term [[Alpha].sub.i] + [[Epsilon].sub.it]. If the assumptions of the random-effects model hold, the fixed-effects model yields consistent, but inefficient, estimates. Consistent estimation of the random-effects model, however, requires the state-specific effect, [[Alpha].sub.i], to be uncorrelated with the other regressors, a condition contradicted by our evidence. For instance, feasible generated least squares estimation of the random-effects model for the full fatalities specification breaks down by producing a negative estimated variance of [[Alpha].sub.i], a symptom of insufficient variation in [[Alpha].sub.i] independent of the regressors.(13) Further, the assumptions of the random-effects model imply consistency of the pooled estimates in a; the dramatic change in the estimates caused by adding fixed effects to the model belies this notion. Hence, the data reject the random-effects model in favor of the fixed-effects model.

To check that the models exhibit valid statistical properties, we applied a Ramsey (1969) RESET test. The null hypothesis states that E[[[Epsilon].sub.it][where][x.sub.it]] = 0, that is, that the model does not suffer from bias due to omitted variables or misspecified functional form.(14) At the 0.05 level, the RESET test rejects both the fatality and injury models that omit fixed effects but fails to reject these same models when the specification includes fixed effects. Thus, the RESET tests highlight the importance of modeling fixed effects to avert specification error.

Table 4 displays least squares estimates of models with variables in first differences. Columns [TABULAR DATA FOR TABLE 4 OMITTED] a and b present estimates using first differences of the log of fatalities as the dependent variable; the estimates in columns c and d use the differenced log of injuries as the dependent variable. The table presents estimates of fixed-effects models in b and d and estimates without fixed effects in a and c. The results again indicate no significant negative effect of spot or annual inspections on fatalities or injuries. The positive and significant estimated coefficients for income, new cars, and the speed limit concur with the estimates in Tables 2 and 3. The positive and significant estimated coefficients for drinking age and annual inspection in the fatalities models are perhaps difficult to rationalize. The results may reflect a driving intensity effect or may arise from simultaneity between fatalities and the inspection and drinking age policies. Hence, we must exercise caution when interpreting the results of the differenced models. The failure of the drinking age to significantly improve safety, a result consistently affirmed by our estimates, does agree with recent work by Asch and Levy (1990) and Michener and Tighe (1992).

The Wald and adjusted [R.sup.2] criteria reject the fixed-effects terms in the differenced fatalities model, implying that the levels specification does not suffer from omitted state-specific trends in fatalities. Wald and RESET tests, however, suggest that the injuries model in levels may suffer from omitted state-specific trends. In any event, the fixed-effects terms in the differenced models do not have a dramatic effect on the inferences.

4. Conclusions

Several things may account for the failure of safety inspections to reduce accidents. First, inspections may induce an offsetting increase in driving intensity. Second, drivers have a strong incentive to perform maintenance to provide for their own safety: If replacement of a $5 light-bulb yields $6 worth of benefit to the automobile owner, any external benefit conferred to other drivers becomes irrelevant. Third, inspections can at best prevent only a small fraction of accidents since most accidents do not involve mechanical failure: Crain (1980) reports that failures of vehicle lights (headlights, brake lights, and turn signals) cause less than 1% of accidents. Finally, annual inspection may fail to eliminate even the small fraction of accidents caused by mechanical failure. Annual inspection ensures only that tested parts function on the date of inspection; if owners wait less than a year to replace worn-out parts, then annual inspection detects only a portion of the faulty parts. Additionally, inspectors can fail, intentionally or unintentionally, to report defects. A Pennsylvania study found that no type of inspection station (car dealership, service station, or chain repair shop) managed to find more than 50% of defects in a sample of vehicles (Crain 1980). Inspectors may fail to report defects to minimize customer hassle and increase the number of inspections performed; Hemenway (1989) found evidence that motorists tend to patronize repair shops with a low failure rate on inspections.

If inspections are ineffective, their cost represents a social loss. The cost includes fuel and vehicle costs of traveling to the inspection site, drivers' time, resources used to perform the inspection, and repairs made to comply with the law. These costs vary across states according to the density of inspection sites and the set of safety features subject to inspection. Garbacz and Kelly (1987) estimated nationwide time and travel costs of $887 million for 1982. This calculation used averages from New Jersey data of 1.17 hours and 20 travel miles per inspection. Compared to most states, New Jersey authorizes only a small number of facilities to perform inspections, so using New Jersey averages likely overestimates national averages. Thus, we computed updated estimates of the time and travel costs using conservative assumptions of 0.50 hours and a 10-mile trip. With 54 million automobiles subject to annual inspection and average hourly earnings of $11.44, the total time cost of annual inspections equaled $309 million in 1995. Using the Internal Revenue Service (IRS) business deduction of 31.5 cents per mile for fuel and vehicle wear yields an annual travel cost of $170 million; hence, estimated time and travel costs of inspection amounted to $479 million for 1995.(15)

We used inspection fees to estimate the costs of performing inspections and administering the programs. Although fees are not market determined and so do not necessarily reflect resource costs, they provide the best readily available estimate.(16) The total annual resource cost estimated in this manner is $553 million. The total annual cost of inspections nationally is thus $1.032 billion, plus the cost of additional repairs. As a basis for comparison, this sum amounts to about half of total annual road and highway maintenance expenditures in California and exceeds total maintenance expenditures summed across 11 small states. Our results suggest that these resources could be more efficiently invested elsewhere.

Our findings parallel recent studies of the effectiveness of automobile emission inspections. Emissions are more likely than vehicle maintenance to be a relevant externality since they externalize a relatively greater portion of their cost. Tests of emissions systems, however, present many of the same difficulties as safety inspections. For instance, the relatively small portion of internalized benefits enhances the incentive for evasion of the law. In fact, recent studies have found that emissions inspections are ineffective (Glazer, Klein, and Lave 1995; Hubbard 1997). The emerging pattern of research suggests that periodic auto inspection is a poor instrument for achieving policy goals.

Appendix

FATALS. Log of motor vehicle fatalities. Source: Highway Statistics.

INJURIES. Log of nonfatal motor vehicle injuries. Source: Highway Statistics.

%OLD. Population age 65 and older as a percentage of total state population. Source: Statistical Abstract of the United States.

%YOUNG. Population ages 18-24 as a percentage of total state population. Source: Statistical Abstract.

SPEED. Mean speed in miles per hour. Source: Highway Statistics.

VSPEED. The speed at or below which 85% of vehicles are traveling minus the mean speed. Source: Highway Statistics.

LIMIT. Legal speed limit on rural interstate highways. Source: Digest of Motor Laws.

MAINT. Total highway maintenance expenditures in a state. Source: Highway Statistics.

INCOME. Real per capita income. Source: Statistical Abstract.

%NEWCARS. New vehicles registered divided by the total number of registered vehicles. Source: Ward's Automotive Yearbook.

SECBELT. Dummy variable equaling 1 if state has a secondary seat belt law for at least six months of a given year and 0 otherwise. Sources: Traffic Safety Facts and Digest of Motor Laws.

PRIBELT. Dummy variable equaling 1 if state has a primary seat belt law for at least six months of a given year and 0 otherwise. Sources: Traffic Safety Facts and Digest of Motor Laws.

%MALE. Number of licensed male drivers as percentage of total licensed drivers. Source: Highway Statistics.

VMILES. Miles traveled per capita in automobiles, buses, and trucks but not motorcycles. Source: Highway Statistics.

%URBAN. Vehicle miles driven in urban areas divided by total vehicle miles. Source: Highway Statistics.

LIQUOR. Legal age for purchasing hard liquor. Source: Digest of Motor Laws.

ANNUAL. Dummy variable equaling 1 if a state requires annual vehicle safety inspections and 0 otherwise. Source: Digest of Motor Laws.

SPOT. Dummy variable equaling 1 if a state conducts spot inspections and 0 otherwise. Source: Digest of Motor Laws.

We thank Tyler Cowen, Harvey Palmer, participants at the 1996 Public Choice Society meetings, and two referees for helpful comments on an earlier draft of the paper. The conclusions herein do not necessarily represent the views of the US Bureau of the Census.

1 Note that safety inspections are separate from auto emissions tests.

2 See Crain (1980) for a detailed legislative history of safety inspections.

3 Time-series studies evaluate the relationship between fatalities and the nationwide percentage of cars subject to inspection. The empirical model implicitly assumes that inspection regime changes in different states have equivalent effects on fatality rates. But if inspection has a fixed percentage effect on the fatality rate (i.e., the relationship is log-linear), then the absolute effect depends on the state's current fatality rate, which in turn depends on a number of state-level variables. These time-series studies, however, account for neither state-specific nor time-varying state-level variables.

4 See also Snyder (1989) and Michener and Tighe (1992) on the importance of accounting for state-specific effects in an empirical model of highway fatalities.

5 Loeb (1985) is an exception.

6 We need not allow for interaction effects between the two types of inspection programs since no state simultaneously employed both types.

7 See the Appendix for details on the variables and data sources.

8 Using conventional OLS standard errors does not substantively alter our inferences.

9 We chose the functional form in Equation 2 by estimating a simple linear regression of log [[[Epsilon].sub.it].sup.2] on [z.sub.it], where [[[Epsilon].sub.it].sup.2] is the squared residual from an OLS estimate of Equation 1, and [z.sub.it] measures the scale of state i at time t as a function of either population or total vehicle miles (depending on the specification of Eqn. 1). We find this regression to have relatively more explanatory power with the scale measure [z.sub.it] equal to the log, rather than the level, of either vehicle miles or population; the result implies the functional form in Equation 2.

10 The data source for injuries contains a number of missing observations; the estimates in Table 3 use 553 available observations on the 50 states for 1981-1993. Note also that, to conserve space, none of the tables report fixed-effect coefficients.

11 We also estimated models that allowed a more general time effect by replacing the linear trend with year-specific dummy variables. These results did not substantively differ from our reported results.

12 In particular, the seat belt variables tend to attain joint significance in models with injuries measured in per capita terms.

13 Omitting lagged fatalities, which correlate particularly closely with the state-specific effect, permits FGLS estimation of the random-effects model to proceed. But in this case, a Hausman test rejects uncorrelatedness of the remaining regressors and state-specific effects; the resulting chi-square (17) equals 207.4, with a 1% critical value of 33.4.

14 We performed a version of the RESET test that uses squares, cubes, and fourth powers of the fitted values (Ramsey 1969); the resulting test statistic distributes asymptotically as a chi-square with three degrees of freedom.

15 We thank a referee for suggesting use of the IRS figure.

16 Delaware permits no fee for inspections, and New Hampshire, Pennsylvania, and Vermont allow stations to set their own fee. For these states, we used the average fee in the other states ($9.89). Mark Bertus kindly supplied data on inspection fees.

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