Policy ineffectiveness or offsetting behavior? An analysis of vehicle safety inspections.

Sutter, Daniel

1. Introduction

Over 60 million registered motor vehicles in 20 states are subject to mandatory periodic safety inspection. Safety inspections typically require safety features, such as brakes, headlights, turn signals, and horn, to be in working order. (1) The economic argument for mandatory inspection relies on the idea that vehicle maintenance reduces the accident rate and therefore provides external benefits. Drivers cannot capture the full benefit of their maintenance expenditures, so they might voluntarily provide less than the efficient level of maintenance. Periodic inspection addresses the inefficiency by compelling drivers to purchase a higher level of maintenance.

Numerous studies have tested the effectiveness of safety inspections by estimating their impact on roadway fatalities and injuries. These studies have produced mixed results. For instance, Loeb and Gilad (1984) and Saffer and Grossman (1987) find inspections effective, but Fowles and Loeb (1995) and Merrell, Poitras, and Sutter (1999) do not. Keeler (1994) finds inspections effective in 1970 but not in 1980.

A number of factors can potentially cause inspection to fail to save lives and prevent injuries. First, if vehicle maintenance provides sufficient internal benefits, drivers might voluntarily provide maintenance close to or exceeding the level mandated by the inspection regulation; that is, the maintenance externality could be inframarginal. Furthermore, state authorities may insufficiently monitor the performance of inspections by private repair shops, allowing approval of vehicles that do not meet the requirements. Repair shops can ignore mechanical defects to minimize customer hassle or to pocket more inspection fees by increasing the number of inspections performed. This type of corruption is difficult for the authorities to prevent because it benefits both repair shops and drivers. Hemenway (1989) in fact presents evidence that drivers actively seek out repair shops that perform pro forma or fraudulent inspections, a so-called Gresham's law of garages. Finally, even if inspections do successfully increas e vehicle maintenance, they can nonetheless yield no reduction in roadway casualties if they also induce drivers to use less caution. As was first demonstrated by Peltzman (1975) and more recently by Chirinko and Harper (1993), safety regulations can lead to offsetting behavioral adjustments. In the absence of inspection requirements, drivers of mechanically inferior vehicles might compensate by driving more cautiously.

Safety inspections can thus fail to reduce roadway casualties in two fundamental ways; they can fail to significantly improve the mechanical condition of vehicles, or they can induce offsetting changes in driver behavior. Consequently, testing the effect of inspection on casualties involves a joint hypothesis about maintenance and driver behavior. Some studies find inspection ineffective with respect to casualties, but these studies cannot distinguish between the effects of maintenance and those of offsetting behavior. Hence, existing studies can shed no light on the source of inspection failure.

We provide a unique test of the effectiveness of inspections by estimating their impact on the number of old vehicles in use. If inspection effectively increases the minimum level of maintenance, the operating costs of older vehicles rise relative to those of newer vehicles. Older vehicles generally require more repairs to meet a given mechanical standard, and these expenditures represent a larger fraction of annual depreciation. An increase in the relative cost of old vehicles should lead some motorists to substitute newer vehicles for older vehicles or to choose alternative forms of transportation. The costs of inspection can cause older vehicles to be prematurely scrapped or to migrate from inspecting states to noninspecting states. As a result, in inspecting states the number of old vehicles falls. If old vehicles decline but casualties do not, this would be evidence of Peltzman-type offsetting behavior. On the other hand, if the quantity of old cars does not fall, this suggests that periodic inspection d oes not enhance maintenance. Hence, unlike tests that focus on casualties, our tests allow us to isolate the maintenance effect from the Peltzman effect.

Economic theory implies that safety inspection can correct a significant external cost or possibly induce offsetting behavior only by imposing on motorists significant replacement or repair costs. To see this, assume the contrary: that the costs of compliance are trivial. If inspection is to correct a significant external cost, in other words, provide a significant external benefit, inspection must also provide a substantial internal benefit. A considerable proportion of the benefit from additional maintenance must be internal. After all, an accident caused by your car's mechanical failure will almost certainly involve your own car. Hence, the internal and external benefits must be of a similar order of magnitude. But if the internal benefit is large and the maintenance cost small, a rational motorist voluntarily purchases the maintenance even in the absence of inspection. Inspection policy becomes irrelevant because the externality is inframarginal. To be effective, therefore, inspection must impose substant ial costs. We generate additional evidence on the cost of inspection by estimating the impact of inspection on the revenues of the repair industry. Our revenue estimates complement our analysis of the effect of inspection costs on old vehicles.

The paper is organized as follows. The next section describes the data and presents our econometric model of old cars. Section 3 presents the results. We find that inspection does not significantly reduce the number of old cars on the road, which suggests that inspection policy is an ineffective means of addressing the externality in vehicle maintenance. Section 4 presents our econometric model of repair industry revenue and discusses the results. The results indicate no significant effect of inspection on repair industry revenue. These results concur with our inference from the old-cars model: Inspection does not increase repairs. Finally, section 5 offers concluding remarks.

2. The Econometric Model

We examine the effect of inspection on registrations of old vehicles using a panel of annual observations on the 48 contiguous states and the District of Columbia. The dependent variable is the registered number of passenger cars that are 12 years of age or older. We placed the cutoff age for an old car at 12 because we judged the resulting subset of vehicles to be neither so slim as to be vulnerable to noise or measurement error nor so broad as to include too many vehicles insufficiently old for inspection to affect. In our sample, about 10.2% of all cars on the road qualify as old.

Our panel data consist of 733 observations for the years 1953-1967. (2) The time period was dictated by the fact that our data source, Automotive Industries, stopped publishing data on the model years of registered vehicles in 1968. This sample period, however, is relatively well suited to examining the effects of inspection policy for two reasons. First, the 1953-1967 period saw several states enact new inspection requirements, and a few states terminate their inspection programs. For instance, in 1953 only 15 states required inspection, whereas 22 did in 1967; overall, 13 states made a total of 15 changes of inspection regime during the period. In fact, the 1960s featured more changes of inspection regime than did any other decade. This variation in the incidence of inspection regimes forms the basis of our empirical tests by allowing us to estimate a fixed-effects model. The fixed-effects model estimates the effect of inspection by exploiting the fact that inspection regimes vary not just across states but also across years. More time variation in inspection regimes is desirable because it increases the expected precision of the estimates and the statistical power of the tests.

Another advantage of our sample period is that it pre-dates the era of vehicle emissions inspection. In recent years, many communities have sought to comply with environmental regulations by requiring mandatory periodic inspection of vehicle emissions. Emissions inspection is a process distinct from safety inspection, but like safety inspection, emissions inspection imposes a disproportionate cost on older vehicles. Since emissions inspection did not exist during our sample period, our sample enables us to isolate the effect of safety inspection from that of emissions inspection.

Numerous factors besides inspection can conceivably influence the number of old cars in use, and many of these factors can be difficult to identify or to quantify. The fixed-effects specification can control for any unspecified determinants of old cars by modeling them as either time specific (constant across states) or state specific (constant across time). State- and time-specific factors do in fact account for a considerable fraction of variation in old registrations. For instance, an important state-specific influence on old registrations is climate. Winter weather and road salt significantly lower expected vehicle life, so that in our sample old vehicles comprise 12.1% of total registrations in California but only 7.1% in the New England states.

As for time-specific effects, a major one in our data set is the long-term impact of World War II. The war effort diverted resources toward armament production, which brought the manufacture of passenger cars to a virtual halt during 1942-1945. By the late 1950s, the lost wartime production caused the nationwide number of old vehicles to drop dramatically. Specifically, old cars accounted for 24% of nationwide registrations in 1953 but merely 4.1% in 1958; renewed postwar production boosted the figure to 8.9% by 1963. These considerations underscore the importance of applying a fixed-effects model. By controlling for state- and time-specific factors, the fixed-effects model helps avert an omitted variables problem and to secure consistent estimates of the effect of inspection. (3)

Our models also include control variables for some fairly standard factors that vary over both time and states, namely, income and demographics. For state i at time t, the variable [INC.sub.i,t] represents the log of real per capita income and [POP.sub.i,t] stands for the log of total adult population. In addition, we hypothesize that demand for old cars increases with the proportion of young drivers in the population. (4) The variable %[YOUNG.sub.i,t] equals the percentage of the adult population aged 18 to 21. To indicate the presence of an inspection program, we specify a dummy variable, [INSPECT.sub.i,t] that equals one if state i requires safety inspection at time t; otherwise, [INSPECT.sub.i,t] equals zero. (5)

We can now specify the following structural equations for the quantity demanded ([Q.sup.D.sub.i,t]) and quantity supplied ([Q.sup.S.sub.i,t]) of old cars:

log([Q.sup.D.sub.i,t]) = [f.sub.i] + [f.sub.t] + [[alpha].sub.1]log([Q.sub.i,t-1]) + [[alpha].sub.2][P.sub.i,t] + [[alpha].sub.3][INSPECT.sub.i,t] + [[alpha].sub.4][INSPECT.sub.i,t][INC.sub.i,t] + [[alpha].sub.5][INSPECT.sub.i,t]%[YOUNG.sub.i,t] + [[alpha].sub.6]%[YOUNG.sub.i,t] + [[alpha].sub.7][POP.sub.i,t] + [[alpha].sub.8][INC.sub.i,t] + [[alpha].sub.9][INC.sup.2.sub.i,t] + [v.sub.i,t]; (1)

log([Q.sup.S.sub.i,t]) = [g.sub.i] + [g.sub.t] + [[beta].sub.1]1og([Q.sub.i,t-1]) + [[beta].sub.2][P.sub.i,t] + [[beta].sub.3][TOTAL.sub.i,t-12] + [[eta].sub.i,t]. (2)

Here, [f.sub.i] and [g.sub.i] denote state-specific fixed effects, while [f.sub.t] and [g.sub.t] stand for year-specific fixed effects; [v.sub.i,t] and [[eta].sub.i,t] are white-noise disturbances, and the parameters are [[alpha].sub.1], . . . , [[alpha].sub.9], [[beta].sub.1], [[beta].sub.2] and [[beta].sub.3]. In the demand equation, we interact the inspection dummy variable with [INC.sub.i,t] and %[YOUNG.sub.i,t] to allow the marginal effect of inspection to vary with these variables. (6) The equations also include a lagged dependent variable to allow for persistence in the quantity of old cars; in other words, we specify a partial adjustment model. Drivers might adjust their demand for old cars only slowly over time because changing vehicles requires significant transaction and search costs. Similarly, transaction costs can cause interstate transfers of old vehicles to change only slowly in response to cross-state differences in the cost of old vehicles.

Ignoring for the moment interstate transfers of registrations, a state's current number of old registrations must equal total registrations of all model years that prevailed 12 years previously minus those vehicles subsequently scrapped or otherwise removed from use. Hence, the number of registered vehicles that existed 12 years in the past is another source of persistence in old cars. Consequently, our supply equation includes the explanatory variable [TOTALS.sub.i,t-12], which represents the log of total auto registrations, new and old, in state i at time t - 12 (7)

The term [P.sub.i,t] denotes the price of an old car, perhaps in terms of expected annual depreciation. Since price data are not available, we use substitution to eliminate the price variable and thereby obtain the reduced-form equation for the short-run equilibrium quantity:

log([Q.sub.i,t]) = [h.sub.i] + [h.sub.t] + [gamma] log([Q.sub.i,t-1]) + [[pi].sub.3][INSPECT.sub.i,t] + [[pi].sub.4][INSPECT.sub.i,t][INC.sub.i,t] + [[pi].sub.5][INSPECT.sub.i,t]%[YOUNG.sub.i,t] + [[pi].sub.6]%[YOUNG.sub.i,t] + [[pi].sub.7][POP.sub.i,t] + [[pi].sub.8][INC.sub.i,t] + [[pi].sub.9][INC.sup.2.sub.i,t] + [[PHI].sub.1][TOTAL.sub.i,t-12] + [[PHI].sub.2][[eta].sub.i,t] + [lambda][v.sub.i,t]. (3)

The fixed effects are now denoted [h.sub.i] and [h.sub.t]. The parameters [lambda], [gamma], [[PHI].sub.1], [[PHI].sub.2], and [[pi].sub.3],..., [[pi].sub.9] are defined such that [lambda] = [[beta].sub.2]/([[beta].sub.2] - [[alpha].sub.2]); [[pi].sub.i] = [lambda][[alpha].sub.i] for i = 1, 2,...,9; [gamma] = [[pi].sub.1] - [[pi].sub.2][[beta].sub.1]/[[beta].sub.2], [[PHI].sub.1] = -[[alpha].sub.2][[beta].sub.3][[lambda].sup.2]/[[beta].sub.2]; and [[PHI].sub.2] = [[PHI].sub.1]/[[beta].sub.3]. Equation 3 is our estimating equation, and the main parameters of interest are [[pi].sub.3], [[pi].sub.4], and [[pi].sub.5], the coefficients of the inspection dummy variable and the interaction variables. For [[pi].sub.3], [[pi].sub.4], or [[pi].sub.5] to be nonzero, and for [[PHI].sub.1], [[PHI].sub.2] and [gamma] to exist, we must assume that [[beta].sub.2], the price elasticity of supply, is nonzero. Since our test seeks to detect the effect of inspection through the influence of cost on quantity, we obviously cannot have quantity determined independently of cost (a perfectly inelastic supply curve). We thus assume [[beta].sub.2] > 0, and this implies that the inspection variables should enter the reduced form with the same sign they obtain in the structural demand equation. Hence, if inspection imposes sufficient cost, we expect the estimates of [[pi].sub.3], [[pi].sub.4], and [[pi].sub.5] to imply a negative impact on quantity. We describe our results in the next section.

3. Inspections and Old Cars

The dual time-series and cross-sectional nature of our data creates the potential for problems of both heteroscedasticity and serial correlation. We find that our estimated models do not suffer from serial correlation, and we can attribute this to the apparent ability of the lagged dependent and lagged registration variables to account successfully for the persistence in the data. Breusch-Pagan tests, however, do find considerable evidence of heteroscedasticity. (8) Consequently, we use a heteroscedasticity-consistent covariance matrix recommended by MacKinnon and White (1985) to compute the standard errors of our coefficient estimates. (9)

Table 1 presents least squares estimates of fixed-effects models of the determinants of old cars in use. The specification in column A uses a dummy variable to model the impact of inspection as a fixed effect, while the specification in column B also includes interaction terms, as in Equation 3. The specification in column C addresses a particular econometric issue that we discuss in the following. We first discuss the results in columns A and B. As column A shows, the MacKinnon--White asymptotic t-statistic for the fixed effect of inspection is only about 176/202, or 0.87. We therefore cannot reject the null hypothesis that inspection has no fixed effect on the quantity of old cars. Similarly, the full model presented in column B shows that the fixed effect and the inspection interaction terms all fail to achieve individual significance at conventional levels. Furthermore, the inspection variables also have a joint effect that does not differ significantly from zero. We test joint effects by using the MacKin non--White covariance matrix to compute Wald test statistics and present the results in Table 2. The Wald chi-square statistic for the joint significance of the inspection variables in the full model is only 4.18, which for three degrees of freedom is not significant at conventional levels. Hence, we cannot reject the null hypothesis that inspection has no effect on the quantity of old cars. (10)

The statistically significant determinants of old cars include lagged old registrations ([Q.sub.i,t-1]), the 12th lag of total registrations ([TOTAL.sub.i,t-12]), the adult population ([POP.sub.i,t]), and per capita income ([INC.sub.i,t]). The estimated coefficients of these variables have the expected sign, except perhaps the population coefficient, which is negative. This coefficient, however, is significant at the 10 level only marginally, and it may be picking up the influence of unspecified factors that correlate with population growth, such as increasing wealth or urbanization. Turning to the other control variables, we note that per capita income and its square have estimated coefficients of opposite sign, so that near the sample median level of income the marginal effect switches sign from positive to negative. This result concurs with the idea that at low levels of income old cars are a normal good but at high levels of income are an inferior good. The estimates also suggest that old cars in use do n ot depend on the proportion of young drivers. Finally, the Wald chi-square statistics in Table 2 indicate that both the state- and the time-specific fixed effects differ very significantly from zero.

The fixed-effects models, however, give rise to an econometric issue regarding estimation of the coefficient of the lagged dependent variable, [gamma]. The estimate of this coefficient converges to the true value only as the number of time periods becomes large, T [right arrow] [infinity], not as the number of cross-sectional units becomes large, N [right arrow] [infinity]. Since our T = 15 is relatively modest, we can expect our estimate of [gamma] to exhibit the well-known downward bias of an autoregressive coefficient (Hurwicz 1950). Since the lagged dependent variable is highly correlated with the state-specific effects, underestimating the coefficient of the lagged dependent variable generally leads to overestimation of the state-specific effects (Nerlove 1971). In theory, this bias could also contaminate the estimates of time-varying factors, such as our inspection variables, although this is less likely. To be sure, we need to verify that our inferences on the effect of inspection are not sensitive to the estimate of [gamma].

Following Anderson and Hsiao (1982) and Arellano (1989), we estimate Equation 3 in first differences (to eliminate the state-specific effects) and use the second lag of the dependent variable, log([Q.sub.i,t-2]), as an instrument for the first difference of the lagged dependent variable, log([Q.sub.i,t-1]) - log([Q.sub.i,t-2]). This procedure yields an estimate of the coefficient of the lagged dependent variable that is consistent on both T and N, not just T. We obtain the following estimates:

[DELTA]log([Q.sub.i,t]) = [DELTA][h.sub.t] + .90[DELTA]/ log([Q.sub.i.t-1]) + .29[DELTA][INC.sub.i,t] + .46[DELTA][INSPECT.sub.i,t]

(.87) (2.39) (.56)

-.15[DELTA]([INSPECT.sub.i,t][INC.sub.i.t]) + ln 1.9[DELTA]([INSPECT.sub.i,t]%[YOUNG.sub.i,t])

(.13) (1.6)

- .58[DELTA]%[YOUNG.sub.i,t] - .24[DELTA][POP.sub.i,t] - .031[DELTA][INC.sub.i,t.sup.2] + .026[DELTA][TOTAL.sub.i,t-12]

(1.69) (.60) (.286) (.120)

[R.sup.2] = .75 N = 683. (4)

Parentheses contain two-stage least squares (2SLS) standard errors, and [DELTA][h.sub.t] denotes the estimated effect of the (differenced) time-specific dummy variables in period t.

Like the models in levels, the estimates of the differenced model indicate that inspection has no significant impact on old cars. The estimated coefficients for the three inspection variables differ insignificantly from zero, both individually and jointly. Specifically, the Wald chi-square statistic for the joint significance of the three inspection variables is only 4.05, which falls short of the .10 critical value of 6.25.

While the differenced model yields estimates that are consistent, the process of differencing the inspection variables potentially discards a great deal of information that is contained in the levels. We therefore prefer to base our inferences on the models in levels, that is, on the fixed-effects models. One way to address the issue of possible underestimation of [gamma] in the fixed-effects models is to explore the robustness of the inferences with respect to different values of [gamma]. The estimate of [gamma] from the fixed-effects models is about .78; the differenced model yields .90, which concurs with the expected downward bias of the fixed-effects estimates, although the computed standard error is quite large. Nonetheless, the consistent estimate from the differenced model provides a convenient alternative estimate that reflects less downward bias. We proceed by treating this estimate of [gamma] as a priori information, and we reestimate the fixed-effects Equation 3 in the levels with [gamma] restrict ed to the fixed value, .90. The restricted least squares estimates, presented in column C of Table 1, concur with our previous inferences regarding the effect of inspection on old cars. As shown in Table 2, the Wald chi-square statistic for the joint effect of the inspection variables is only 2.50, which is not significant at conventional levels.

4. Inspections and Repair Shop Revenue

Since inspection does not significantly affect the quantity of old cars, we cannot reject the hypothesis that inspection does not improve mechanical condition. This hypothesis further implies that inspection must generate no additional maintenance expenditures at repair shops and hence no increase in repair shop revenue. To explore this issue, we estimate an econometric model of the determinants of total repair industry revenue. Our available data consist of a cross section of the 50 states for 1992. The model takes the following form:

[REVENUE.sub.i] = [[alpha].sub.0] + [[alpha].sub.1][INSPECT.sub.i] + [[alpha].sub.2][FEE.sub.i] + [[alpha].sub.3][INC.sub.i] + [[alpha].sub.4][MILES.sub.i] + [[alpha].sub.5][URBAN.sub.i] + [[epsilon].sub.i]. (5)

For state i, the dependent variable [REVENUE.sub.i] represents total repair industry revenue per registered vehicle. (11) The dummy indicator [INSPECT.sub.i] models the fixed effect of inspection on revenue. We also allow the revenue effect of inspection to vary with the fee charged by private repair shops. The variable [FEE.sub.i] represents the per vehicle inspection fee, which typically is fixed by state law. The fee variable can model the direct impact of fee collection on revenue and might also pick up the influence of additional repairs if the rigor of the inspection procedure happens to correlate with the size of the fee. (12)

Higher income can increase maintenance expenditure by stimulating demand for maintenance or by elevating maintenance labor costs. Hence, our model includes per capita income, [INC.sub.i], as a control variable. Two additional control variables proxy for the wear and tear imposed by vehicle use. [MILES.sub.i] stands for miles driven per vehicle, and [URBAN.sub.i], reflects the proportion of miles driven in urban areas. We predict these control variables to have positive coefficients. (13) The final term in Equation 5, [[member of].sub.i], denotes a white-noise disturbance.

Our main parameters of interest are [[alpha].sub.1] and [[alpha].sub.2], which together define the overall revenue effect of inspection. One hypothesis consistent with our inferences from old cars states that inspection generates no revenue from additional repairs but that fee collection increases revenue dollar for dollar. In this case, the null hypothesis takes the form [H.sub.0]: [[alpha].sub.1] = 0, [[alpha].sub.2] = 1. Fees, however, need not increase revenue dollar for dollar. Fees could crowd out revenue from sales of other services, perhaps through price discounts for regular customers. If repair shops operate in a competitive environment, inspection's cost to drivers falls to its resource cost, which for pro forma inspection would approach zero. We can thus express the null hypothesis more accurately as [H.sub.0]: [[alpha].sub.1] = 0, [[alpha].sub.2] [less than or equal to] 1, but to simplify our analysis and to increase the statistical power of our tests, we formulate a stronger version of this hypot hesis:

[H.sub.0]: [[alpha].sub.1] = 0, [[alpha].sub.2] = 0. (6)

By stipulating [[alpha].sub.2] = 0, the null hypothesis also rules out a revenue effect from additional repairs that correlate with the size of the fee.

We obtain least squares estimates of Equation 5 and present the results in Table 3, column A. The resulting estimates of [[alpha].sub.2] and [[alpha].sub.1] have opposite sign, and their joint effect does not differ significantly from zero. Testing the joint hypothesis in Equation 6 yields an [F.sub.2,44] statistic equal to 1.54, which is not significant at conventional levels. Testing the coefficients individually, we find that the estimated [[alpha].sub.1] does not differ significantly from zero, but the estimate of [[alpha].sub.2] is significantly positive, though only marginally. Since [[alpha].sub.1] proves insignificant and the inspection dummy is highly correlated with the fee variable, we can pursue a sharper estimate of [[alpha].sub.2] by omitting the inspection dummy. Column B displays these estimates. As expected, the estimate of [[alpha].sub.2] now has a lower standard error, but the estimate itself falls by an even greater proportion, so that it no longer differs significantly from zero. Hence, w e can conclude that the inspection variables have a joint effect that does not differ significantly from zero, and neither variable can individually survive data-based reduction of the model.

The overall model has considerable explanatory power. The adjusted [R.sup.2] exceeds 0.6, which is quite high for a cross section. As predicted, the control variables have estimated coefficients that are positive, and each is statistically significant. To check the validity of our inferences, we perform a battery of diagnostic tests. As the test statistics in Table 3 indicate, Breusch--Pagan tests find no evidence of heteroscedasticity, and Ramsey RESET tests detect no sign of model misspecification. (14) A cause for concern in a cross section of modest size is the presence of influential outliers. Using a criterion described by Welsch (1980), however, we find no evidence of influential outliers in our sample. (15)

Our revenue estimates suggest that we cannot attribute inspection's lack of impact on old cars to price inelasticity of the supply of old cars. In a state mandating inspection, registered old cars can conceivably have no profitable alternative uses, such as reregistration in a noninspection state or scrapping for parts. If so, inspection has no effect on the quantity of old registrations, even if inspection requires additional repairs. But performing more repairs on the same number of old cars would imply higher repair industry revenue, which is contradicted by our revenue regressions. The revenue regressions thus reinforce the conclusion that inspection does not increase maintenance and mechanical soundness.

5. Conclusions

Roadway casualties are determined by the physical aspects of the driving environment and by the behavior of drivers. Traffic safety policies that improve the safety of the physical environment can unintentionally induce drivers to take more risks: so-called Peltzman effects. If a policy fails to reduce casualties, policymakers must try to infer whether the failure arises from policy impotence or Peltzman effects. We provide some unique tests that distinguish policy impotence from offsetting behavior by analyzing mandatory auto safety inspections. We formulate our tests by observing that improving the mechanical condition of vehicles involves costs. These costs should decrease the number of old vehicles in use, elevate repair industry revenue, or both. Our tests indicate that inspection has no significant impact on either old cars or repair industry revenue, which implies that inspection does not improve the mechanical condition of vehicles. Consequently, our results lend support to existing studies that find inspection ineffective in reducing roadway casualties. Furthermore, our results imply that inspection's ineffectiveness arises from policy impotence rather than Peltzman effects.

Two possibilities remain. First, drivers might voluntarily provide the efficient level of maintenance when considering only private benefits; that is, the maintenance externality might be inframarginal. Second, periodic inspection might be a poorly enforced or unenforceable policy. Drivers and garages can mutually benefit from conducting pro forma inspections, giving rise to Hemenway's (1989) Gresham's law of garages. In fact, there exists considerable evidence of weak enforcement and evasion of inspection requirements. Massachusetts officials claim that monitoring the inspection performance of licensed garages is prohibitively expensive simply because submitting an undercover test car for inspection requires letting the garage keep the $15 inspection fee. A Washington Post investigation (Eggen 1999) found that in a recent year, about 600 out of 4300 inspection stations in Virginia issued no rejection stickers at all. Approval stickers can be readily obtained on the black market for as little as $40 (Campbell 1994). (16) Hence, the available evidence casts doubt on the wisdom of preserving the existing state inspection programs. If mandatory inspection does not improve mechanical condition, it corrects no externality; if the external benefits are inframarginal, there is no market failure for inspection to correct.

Critics of inspection policy frequently allege that inspection stations fraudulently fail vehicles in order to charge motorists for unnecessary repairs (Crain 1980). Our results, however, suggest that inspection policy's costs do not include significant additional repairs, necessary or unnecessary. But while unnecessary repairs do not appear to be a widespread problem, any remaining costs of inspection would represent pure social cost. This cost includes fuel and vehicle costs of traveling to the inspection site, drivers' time, and resources used to conduct the inspections. Merrell, Poitras, and Sutter (1999) estimate that these costs can exceed $1 billion annually.

In many communities, licensed repair shops conduct another version of periodic inspection that focuses on vehicle emissions. Recent studies by Glazer, Klein, and Lave (1995) and Hubbard (1997, 1998) find emissions inspection to be an unsuccessful policy. Together with this study, these results suggest that periodic vehicle inspection is a poor instrument for achieving policy goals.

Table 1.

Fixed-Effects Models of the Determinants of Old Cars in Use: Least
Squares Estimates of Coefficients for Time-and-State- Varying
Explanatory Variables. 733 Annual Observations on the 48 Contiguous
States and the District of Columbia. 1953-1967 (a)

Explanatory Variables Model (A) Model (B)

Old cars lagged .786 (***) .775 (***)
 (.045) (.048)
Real per capita income 1.63 (**) 1.63 (**)
 (.82) (.83)
Real per capita income squared -.195 (*) -1.91 (*)
 (.107) (.108)
Total registration, 12th lag .211 (***) .215 (***)
 (.074) (.075)
Log of adult population -.164 (*) -.165 (*)
 (.091) (.091)
Percentage of population age 18-21 -.436 -.670
 (1.04) (1.06)
Inspection X percentage age 18-21 -- .681
 (1.01)
Inspection X income -- -.0968
 (.0655)
Inspection .0176 .381
 (.0202) (.238)

Explanatory Variables Model (C)

Old cars lagged .900
 --
Real per capita income .921
 (.707)
Real per capita income squared -.112
 (.092)
Total registration, 12th lag .172 (**)
 (.070)
Log of adult population -.220 (**)
 (.089)
Percentage of population age 18-21 -.172
 (1.06)
Inspection X percentage age 18-21 .269
 (.949)
Inspection X income -.0137
 (.0507)
Inspection .063
 (.181)

(a)All strictly positive variables are in log form or percentage form.
Parentheses contain asymptotic standard errors. The standard errors are
computed using the heteroscedasticity-consistent matrix recommended by
MacKinnon and White (1985).

(*)Significant at the 10% level.

(**)Significant at the 5% level.

(***)Significant at the 1% level.
Table 2

Wald Tests (a)



 Degrees
Null Hypotheses of Freedom

Inspection has zero effect 1 (A), 3 (B, C)

Time-specific effects equal zero 14

State-specific effects equal zero 48

Income has zero effect 2


 Chi-Square Statistics
 (p-values)


Null Hypotheses Model (A)

Inspection has zero effect 0.76
 (.383)
Time-specific effects equal zero 1640
 (<[10.sup.-6])
State-specific effects equal zero 113
 (<[10.sup.-6])
Income has zero effect 5.88
 (.053)

 Chi-Square Statistics (p-values)


Null Hypotheses Model (B) Model (C)

Inspection has zero effect 4.18 2.50
 (.243) (.475)
Time-specific effects equal zero 1600 1830
 (<[10.sup.-6]) (<[10.sup.-6])
State-specific effects equal zero 108 312
 (2 X [10.sup.-6]) (<[10.sup.-6])
Income has zero effect 6.31 2.06
 (.043) (.357)

(a)The Wald test statistics are computed using the
heteroscedasticity-consistent covariance matrix recommended by MacKinnon
and White (1985).
Table 3

Ordinary Least Squares Estimates of the Determinants of Repair
Industry Revenue. Dependent Variable: Total Statewide Revenue per
Registered Vehicle. Observations on the 50 States for 1992

Explanatory Variables Model (A) Model (B)

Per capita income .00825 (***) .00779 (***)
 (.00192) (.00192)
Miles driven per vehicle 6.75 (**) 4.78 (*)
 (3.19) (2.91)
Proportion of miles driven in
 urban areas 73.3 (**) 81.1 (**)
 (30.6) (30.4)
Inspection -19.6 --
 (13.7)
Inspection fee 2.04 (*) .705
 (1.16) (.697)
Intercept -79.8 -55.0
 (55.1) (52.9)
 Test Statistics (p-Values)

Hypothesis Tests Model (A)

Null hypotheses:
 Inspection has zero effect [F.sub.2,44] = 1.54
 (.226)
 Model has no explanatory power [F.sub.5,44] = 16.5
 (<[10.sup.-6])
 Homoscedasticity [chi square](5) = 6.10
 (.297)
 No specification error (RESET) [F.sub.3,41] = .468
 (.706)

 Test Statistics
 (p-Values)

Hypothesis Tests Model (B)

Null hypotheses:
 Inspection has zero effect [F.sub.1,45] = 1.02
 (.317)
 Model has no explanatory power [F.sub.4,45] = 19.6
 (<[10.sup.-6])
 Homoscedasticity [chi square](4) = 4.34
 (.362)
 No specification error (RESET) [F.sub.3,42] = .878
 (.460)

(*)Significant at the 10% level.

(**)Significant at the 5% level.

(***)Significant at the 1% level.

Received December 2000; accepted August 2001.

(1.) The exact requirements vary from state to state. Note also that safety inspections are separate from auto emissions tests mandated for some metropolitan areas.

(2.) We are missing one observation (and one lagged observation) because we could not obtain reliable data for the number of old cars in Delaware in 1962.

(3.) Failure to model fixed effects can lead to inconsistent estimates if the state- and time-specific factors happen to correlate with the incidence of inspection. For example, inspection policy might play the role of a treatment; that is, the likelihood of policy enactment might increase with the severity of the problem to be addressed. In this case, the likelihood of inspection would increase with the number of old or inferior vehicles, implying statistical correlation between the fixed effects and the inspection variable.

(4.) Since young people are newer entrants to the labor force and have lower wealth and income, they might have greater demand for old cars. Young drivers also have relatively greater accident risk, and in this respect low-priced old cars offer young drivers the advantage of putting less wealth at risk of accident.

(5.) To the best of our knowledge, safety inspection requirements cover all old registered vehicles without exception. In a few states, vehicles might be exempt if they are less than a year old.

(6.) In other words, we allow for the possibility that imposing an inspection requirement causes a shift in the elasticity of demand for old cars with respect to income and young persons. For instance, the cost of inspection might make drivers more willing to substitute into newer cars as their income increases.

(7.) We obtain our data from the following sources: old and total registrations, Automotive Industries; population, Current Population Report P-25 series; income, Statistical Abstract of the United States; and inspection, The Book of the States and Cram (1980).

(8.) Applying a Breusch-Pagan test to the model in Equation 3 yields a chi-square statistic of 1035; the .01 critical value for rejecting the null hypothesis of homoscedasticity is 102.

(9.) The estimator of the covariance matrix takes the form [(X'X).sup.-1]X'[OMEGA]X[(X'X).sup.-1]. Here, [OMEGA] is an n X n diagonal matrix with ith element equal to [u.sup.2.sub.i]/[(1 - [h.sub.i]).sup.2], where [u.sub.i], is the ordinary least squares residual and [h.sub.i] is the ith diagonal element of the so-called hat matrix, X[(X'X).sup.-1]X'. MacKinnon and White (1985) conducted a Monte Carlo analysis of the finite sample properties of this estimator and several alternative heteroscedasticity-consistent covariance estimators and found that this estimator performed best.

(10.) We also obtain estimates that model the heteroscedasticity explicitly by specifying a scedastic function of the form [[sigma].sup.2.sub.i,t] = [[sigma].sup.2][POP.sub.l,t.sup.[delta]]. In this function, the adult population provides a measure of scale that happens to correlate significantly with the dispersion of the ordinary least squares residuals. We use the method of maximum likelihood to simultaneously estimate the scedastic parameter [delta] and the coefficients of the model. The resulting estimates yield inferences equivalent to those we report in this paper.

(11.) Our source for revenue is the 1992 Census of Service Industries. We measure revenue in per vehicle terms in order to facilitate interpretation of our fee variable. This approach involves the implicit assumption that revenue is unit elastic with respect so the number of registered vehicles. The assumption does not alter our results and is closely supported by the data. To verify this, we estimated a simple regression of the log of revenue on the log of vehicles. The resulting 95% confidence interval for the elasticity was 0.98 to 1.11.

(12.) In 1992, inspection fees ranged from $3.50 in Arkansas to $20 in Pennsylvania, with the average around $10. Our fee variable equals zero for noninspecting states and states conducting inspections at state-operated facilities instead of privately operated repair shops. As of 1992, only Delaware and New Jersey conducted inspections at state-operated facilities.

(13.) Since the repair industry might earn additional revenues by inspecting emissions, we also intend [URBAN.sub.i] to proxy state i's rate of emissions inspection. Localities under federal mandate to conduct emissions inspection typically are large urban areas (so-called Air Quality Control Areas). Heavily urbanized states can therefore be expected to have a relatively greater percentage of vehicles subject to emissions inspection.

(14.) We employ the version of the RESET test that involves square, cube, and fourth power of the fitted values, as recommended by Ramsey (1969). The resulting test statistic distributes asymptotically as a chi-square with three degrees of freedom.

(15.) The Welsch (1980) criterion involves computing [DFFITS.sub.i], a standardized measure of the change in the fitted value due to deletion of observation i. By definition, we have [DFFITS.sub.i] = [e.sub.i][{[h.sub.i]/(1 - [h.sub.i])}.sup.1/2], where [e.sub.i] is the ith studentized residual and [h.sub.i] is the ith diagonal element of the hat matrix, X[(X'X).sup.-1]X'. In our sample, an observation would qualify as an influential outlier if [DFFITS.sub.i] exceeds 0.86, but none of our observations had [DFFITS.sub.i] greater than 0.81.

(16.) Conceivably, some motorists might also evade inspection by illegally operating old vehicles without registering them. But this method of evasion is not supported by our results since we find no significant decline in old registrations in inspecting states. For this point, we thank an anonymous referee.

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Marc Poitras (*)

Daniel Sutter (+)

(+.) Department of Economics, University of Oklahoma, Norman, OK 73019-2103, USA.

(*.) Department of Economics, University of Dayton, Dayton, OH 45469-2251, USA; corresponding author.