The Impact of Periodic Passenger Vehicle Safety Inspection Programs on Roadway Fatalities: Evidence from US States Using Panel Data

To ensure that vehicles continue to meet safety standards over their lifetimes, jurisdictions may establish vehicle safety inspection and maintenance (I/M) programs. The aim of these programs is to mitigate motor accidents or roadway fatalities that can be attributed to vehicles operating unsafely due to wear and tear or insufficient and improper maintenance. I/M programs exist across the world and are typically administered by national or (as in the case of the United States), state departments of transportation (DOTs). Typically, these programs require that vehicles be periodically brought to an inspection station, where a road-worthiness certificate is issued only to LDVs meeting all standards and requirements. For example, in Pennsylvania, annual “safety inspections for passenger cars and light-duty trucks require that the following items be checked: suspension components, steering, braking systems, tires and wheels, lighting and electrical systems, glazing (glass), mirrors, windshield washer, defroster, wipers, fuel systems, the speedometer, the odometer, the exhaust systems, horns and warning devices, the body, and the chassis” (PennDOT 2017). Vehicles are only certified upon the completion of required maintenance.

I/M programs were among the earliest strategies implemented to regulate vehicle safety in the United States. The first programs were voluntary (i.e., states recommended periodic inspections but did not mandate them). Massachusetts’ voluntary program, founded in 1926, was followed in quick succession by similar offerings in states across the eastern seaboard. The first mandatory safety I/M program was established in 1929 in Pennsylvania; this program continues to be active and is the nation’s longest running safety I/M program. After a 1968 hearing in the US Senate found that vehicle owners were incurring high costs for unsatisfactory vehicle repairs, the Motor Vehicle Information and Cost Savings Act was passed, giving the US DOT (through state agencies, if needed) the power to establish inspection stations and conduct vehicle safety inspections (Schroer and Peyton 1979). As a result, in 1973, NHTSA issued vehicle-in-use (VIU) standards, with the intention of requiring every US state to institute a safety I/M program. This rule received almost immediate pushback from the states, compelling NHTSA to weaken the VIU standards in 1976, no longer requiring mandatory inspections (Thompson 1985). As a result, while over a dozen US states established programs in the 1960s and 1970s, several of them were repealed soon after. Though not mandating I/M programs, NHTSA continues to promote safety inspections in recommendations and guidance, such as routinely published Proactive Safety Principles. Yet of the 32 active I/M programs in 1976, 18 have since been repealed, and no new programs have been established (GAO 2015). As shown in Fig. 1, only 14 US states continue to have mandatory periodic vehicle safety inspection programs in 2020.

The decline in legislative and popular support for these programs since the mid-1970s, which has led to this string of repeals, was primarily motivated by “waning public concern with highway safety” and the perception “that mechanical defects cause a small portion of” accidents (Thompson 1985, p. 696). Although there may be a perception that I/M programs are ineffective since newer vehicles rarely fail safety inspections, Peck et al. (2015) noted that this perception hinges on a significant underestimation of the number of LDVs failing safety inspections. Additionally, they argued that since inspection failure rates do not tend to zero, they are still an important means of identifying the need for, and enforcing, critical vehicle maintenance. Stakeholders across the United States continue to advocate for the elimination of I/M programs, arguing that they are expensive to consumers and cause no significant changes in rates of road accidents or fatalities. A large strand of literature contains studies that have attempted to quantify these changes. However, most of the earlier studies (discussed in what follows) have been narrowly defined—either focusing only on one region or limiting their analyses to a short time frame. Several others also used data that may now be considered outdated. The 1970s and 1980s saw the implementation of FMVSS as well as laws lowering speed limits and mandating seat-belt use, making vehicles and roads safer and noncomparable with data or analyses from earlier decades. We believe that outdated studies based on small subsets of data from many years ago are not sufficient to support current considerations of the effectiveness of I/M programs.

A large number of studies in the literature examined the relationship between safety inspection programs and road accident or fatality rates, but this question has rarely been explored with a panel-data approach.

Jurisdictions continue to debate the need for, and effectiveness of, I/M programs while relying on outdated or narrowly focused evidence in the literature. To better inform future legislation and policy development, this study aimed to develop a reproducible and data-driven analysis that applied nationally representative data over the longest possible period, to quantify the mitigating effect—if any—of safety I/M programs on motor accidents and roadway fatalities. Applying a panel of fatal accident data representing all 50 states (and the District of Columbia) over a 44-year period, we developed a FE regression to control for the potential state and time effects in order to improve the robustness of our estimates. Our specification regressed the presence of state I/M programs against adjusted roadway fatality rates while controlling for several related factors. The results obtained from the FE regression were supported by several supplementary regressions, including an instrument variable regression that relaxed the assumption that the implementation of the I/M program (i.e., the treatment) was random across states.

Given the variation in fleet and driving characteristics between countries and regions, it is unclear whether, and to what extent, the findings of these international studies will hold true in the United States. Unlike in Europe, where I/M programs are typically administered at the national level, passenger vehicle safety inspections in the United States are based on a patchwork of state-level regulations, whereas accident and fatality rates also continue to depend on nationwide trends and federal laws. The results presented in what follows were developed from US accident and demographic data of uniform resolution (rather than sampled surveys) in all 50 states and the District of Columbia, allowing stakeholders to access relevant, national-level results instead of interpolating from regional or international studies. Rather than assessing only one state or region, the results presented in what follows indicate an average treatment effect (ATE) of I/M programs on roadway fatalities across the United States. Given the variation in demographics, fleet characteristics, and state governments, we admit it is likely that a state-by-state model would reveal heterogeneity in treatment effects between states and that exogenous variables may not fully account for these state-to-state differences. However, to facilitate comparison of effects across states, we believe it necessary to calculate an ATE. To ensure that our estimate of the ATE is unbiased (e.g., free from the influence of state-specific unobservable or omitted biases), we adjust for differences between states that are relevant for program establishment/repeal and for the outcomes in our regression specifications. It would not be possible to make these adjustments in a state-level analysis.

Regressions based on shorter time frames are also more likely to include bias in estimating any time-related effects. As discussed in the following section, the data used in this study represent the largest publicly available road fatality database in the United States; this database contains records of nearly every fatal accident that occurred anywhere in the country over a period of more than four decades.

Every year, states share data with NHTSA on all police-reported fatal motor accidents in their jurisdiction through the Fatality Analysis Reporting System (FARS), which was created by an act of Congress (NHTSA 2020a). “The FARS crash data files contain more than 100 coded data elements characterizing the crash, vehicles, and people involved” (NHTSA 2010). This feature-rich data set is maintained primarily to inform regulation in Congress and at the USDOT. Although reporting data to FARS is entirely voluntary and governed by cooperative agreements, most states have regulations mandating the collection and submission of data on fatal accidents. This reporting—since 1975—has led to the development of a nationwide census of fatal accidents over the last four decades. The FARS database provides a uniform and systematic format for states to record and share fatal accident data, which is why it was selected for this study. We decide to focus on road fatality rates as our primary outcome of interest since the likelihood of reduction in fatalities is a strong element in decisions surrounding the implementation, withdrawal, or maintenance of I/M programs. Another advantage of the FARS database is that, unlike the limitations of other data sources used in previous studies, the FARS database provides feature-rich, uniform, and systematically recorded data on fatal accidents in every state and over several decades. Owing to this consistency, the models presented in what follows—in line with numerous past studies—use the FARS database to assess I/M programs’ effect on fatality rates. Although the task of collecting, collating, and submitting data to the FARS database falls on first responders and on staff at state DOTs, the process is heavily controlled by NHTSA. Summary statistics and additional information regarding the FARS data are provided in the Appendixes.

The FARS database includes records of vehicle contributing factors, i.e., factors related to involved vehicles’ safety features that first responders may have taken the time to perceive to have led to an accident. The FARS data format allows for the optional recording of over a dozen so-called contributing factors, as listed in the Appendixes. These factors—such as low tire-tread depth or worn brakes—involve components that would typically be inspected and remedied during a periodic inspection. Fig. 2 shows the percentage of yearly fatal crashes in each state, for which at least one contributing factor was recorded in FARS between 1975 and 2017. Overall, between 1975 and 2017, at least one contributing factor was recorded in just over 3% of all fatal accidents. In theory, these data would be the most reliable indicator of the impact of I/M programs on preventing fatal accidents since a vast majority of these factors would likely have been identified and remedied during a safety inspection. Police officers who respond to fatal accidents are expected to include information on these factors in their reports. Analysts trained by NHTSA then format and record information from these reports for submission to the FARS database (NHTSA 2010). There may be evidence in the literature that these data may be underreported: Although they did not examine vehicle contributing factors specifically, Rolison et al. (2018, p. 22) found that other contributing factors (e.g., driver distraction and impairment, cell-phone use) are underreported, since the priority of responding officers at the scene of an accident is to ensure the safety of road users rather than to collect these data. This evidence is also supported by anecdotal accounts of numerous I/M program administrators. Given our belief that these data are underreported, the specifications developed in this study apply a dependent variable based on all fatal accidents, regardless of whether such a contributing factor was recorded. However, the proportion of accidents with a recorded contributing factor was included as a control to evaluate its correlation respectively with other exogenous variables and with the rate of fatalities. Additional discussion of vehicle contributing factors is provided in the Appendixes.

Furthermore, we chose not to focus our analyses on these contributing factors since, unlike the control studies conducted by Fosser (1992) and Christensen and Elvik (2007), data on defects or contributing factors are not publicly available in the United States for vehicles not involved in accidents.

In addition to FARS, this analysis uses numerous other data sources, all of which are free and publicly available (FHWA 2018; US Census Bureau 2016, 2020; NCEI 2020; NCSL 2020). Further discussion of these supplementary data sources, and the regressors developed from them are presented in the following section and in Appendix IV.

The availability of longitudinal data on accidents occurring at the state level enabled us to gather information and responses to a total of 51 jurisdictions over 44 years (1975–2018). Given the large temporal span and geographical coverage of the data, we built our econometric specifications on the basis of panel data models because they allowed us to control for broader time trends and state effects across observed units (Chamberlain 1984; Hsiao 2003) that should clear our estimates from external biases unrelated to the implementation of I/M programs (e.g., improved standards, seat-belt laws) that can still impact road fatality rates. Therefore, the specifications in our analysis use both time and state FE. The decision to use panel data models is in line with the recent strands of the literature, as several recent studies discussing model and regressor specifications for the prediction of accident and fatality rates concur on the use of panel data models to assess weighted fatality rates (Stipdonk et al. 2010; Siegrist 2010; Hauer 2010; Liu et al. 2018; Chen et al. 2018; Fountas et al. 2018).

We note here that by modeling average or mean values, rather than looking at each vehicle’s inspection status during an accident, our analyses may be subject to an ecological fallacy. However, we believe that by limiting our analyses to in-state passenger vehicles, we are able to reasonably assume the inspection status of each individual vehicle and of the group as a whole, based on the inspection requirements in each state at the time of analysis. Furthermore, mean accident data are calculated based on individual-vehicle level records, and resultant errors are explicitly stated in our analyses.

The FARS database includes fatal road accidents of all types, including those involving commercial vehicles (e.g., buses, trucks, other commercial equipment), which are governed by safety standards and I/M programs unrelated to the LDV I/M programs that are the focus of this study. Therefore, we exclude accidents involving only other types of vehicles and accidents involving passenger vehicles as well as other types from the present analysis. This allows for models to be developed around only those vehicles that are likely covered by the I/M programs in question.

Passenger vehicle I/M programs are administered at the state level, usually by transportation agencies, which implies that the jurisdiction of each I/M program is assumed to be limited to vehicles registered in said states. However, a considerable proportion of vehicle miles (1 km = 0.62 mi) are traveled out-of-state, and as a result, vehicles may be involved in accidents outside their home state. One previous study addressed that issue by ignoring the location of the accident and developed panels based solely on vehicles’ state of registration (Hoagland and Woolley 2018), but this strategy is limited by the fact that it does not control for state-based differences across states in first-responder procedures, which can lead to biases since data collection and reporting norms can differ significantly from one state to another. This study contributes to the literature by clearing up this potential threat to estimate quality. We restrict the analysis to accidents in which all vehicles involved were registered in the state where the accidents occurred. This approach (of restricting analyses to vehicles under the jurisdiction of specific I/M programs) does not appear in recent literature, and its application to quantifying the effectiveness of I/M programs is a unique contribution of this paper. These restrictions do not impair the size of our final sample. The analysis presented here was based on over 80% of the accidents recorded in FARS data for each year over the period 1975–2018 (for Panel I, as described in what follows) and totals over 1.33 million fatal accidents. The Appendixes provide additional details on these sampling choices.

The dependent variable selected for these models was a LDV fleet size–adjusted statewide annual road fatality rate. This allowed us to uncover any links between trends in these fatality rates and the regression variables. The rate was expressed in fatalities per 100,000 registered passenger vehicles, as shown in Eq. (1). The choice to develop these models based on a fleet size–adjusted variable was made to control for the variability in per-capita vehicle ownership (i.e., population may not be an accurate measure of the number of passenger vehicles on a state’s roadways) and to simplify the interpretation of results.

Two data panels (henceforth referred to as Panels I and II) were developed for this analysis. Each was indexed by state and year and contained the dependent variable and the treatment variable, in addition to various exogenous variables.

An inverse hyperbolic sine transformation of both the dependent and independent variables was used to improve regression performance and to facilitate easier interpretation of results. This transformation is similar to the log transform but may be used in cases where valid zeroes are present in the data. Additional discussion of this transformation may be found in Burbidge et al. (1988). When the inverse hyperbolic sine transformation is applied to both dependent and exogenous variables (Bellemare and Wichman 2020), note that regression coefficients may be interpreted as elasticities (in a similar fashion to log-log regressions).

This study implements two main FE model specifications: Model I and Model II were based on Panel I and Panel II, respectively. Both models regress the treatment variable (i.e., the presence or absence of a state I/M program) against the dependent variable. FE models were chosen based on the result of (1) a robust Hausman specification test; and (2) an F-test (Baltagi and Bresson 2012; Hui et al. 2019). The Hausman test indicates that the rejection of the null hypothesis indicates that omitted variables may be correlated with regressors which motivated the choice of an FE model over a random effects model; and the F-Test leads to the rejection of the null hypothesis indicates the presence of fixed effects. The “within” estimator controls for omitted variable bias, with regard to any effects that do not vary over time, and are specific to individuals (in this case, states). Further, these models assume the effects are correlated with one or more regression features. The “within” estimator de-means each variable, thereby cancelling out the term corresponding to these individual effects. State effects include variations between states, which are relatively time invariant but which may account for differences in the dependent variable, e.g., road conditions and funding, climate, and the relative volume of industry and related commercial or industrial traffic. For a dependent variable (i.e., fatality rate) $y_{s,t}$, as defined for a state $s$ and year $t$, real data generation may be assumed to follow a process, as shown in Eq. (2), where ${\alpha }_i$ represents the time-invariant effect associated with any omitted variables. The “within” estimator de-means this equation, thereby counteracting ${\alpha }_i$, as shown in Eq. (3):

Since the literature indicates effects both across time and states (i.e., so-called individual effect), FE Models I and II are two-way models and control for both state and time FE. By applying two-way models, we aim to control for individual and time effects. The FE models described here were developed with the plm package in R (Croissant and Millo 2008; R Core Team 2020).

We present two FE regressions. Model I was developed based on Panel I (a balanced panel for 51 jurisdictions and each year in the period 1975–2018), and Model II was developed on Panel II (which contains data for all 51 jurisdictions, but only a subset between 1975 and 2017). Panels I and II are further described in earlier sections on exogenous variables. To address any possible correlation between exogenous variables, FE Models I and II use only a subset of variables from the corresponding panels. We selected variables for each regression on the basis of variance inflation factors (VIFs), calculated for ordinary least squares (OLS) regressions for each panel, containing all exogenous variables from that panel. For Panel I, two variables—vehicle ownership per capita and proportion of driving on rural roadways—were found to have $\mathrm{VIF}\ge 5$ and were thus excluded from Model I. For Panel II, two iterations were conducted. Five variables with $\mathrm{VIF}\ge 10$ in the first regression were excluded from a second OLS regression. Only variables with a $\mathrm{VIF}<5$ in this second iteration were included in FE Model II. The VIFs calculated from the OLS model are presented in the Appendixes. By excluding variables that do not meet the VIF threshold, the FE regressions presented here are unlikely to be affected by correlation or multicollinearity between independent variables (Mansfield and Helms 1982). Although the Boolean variable Program_Ever was included in the Model I specification, it was dropped during the regression (since it was redundant in a two-way model that controlled for both time and state).

Table 3 presents estimates from Models I and II. The coefficient for the treatment variable is found to be negative and statistically significant in both models (respectively at the 90% and 95% levels), indicating that states with I/M programs have a lower fatality rate than those without. Model II showed a reduction in fatality rates of 5.5% (95% CI: 0.4% to 10.6%), and Model I—with fewer variables but over a longer time period—found a complementary result: Jurisdictions with I/M programs had 2.8% (90% confidence interval [CI]: 0% to 5.6%) fewer fatalities per 100,000 registered vehicles than those that did not.

Both models also indicate that fatality rates are negatively correlated with mean vehicle age, which corroborates findings in the literature that crashes involving older vehicles are more likely to result in fatalities. The models also indicate a negative correlation between the accident rate and the number of passenger vehicles registered per capita. Model II also found two of the additional demographic variables to be statistically significant—the statewide gross domestic product (GDP) and the political party in power at the state level. The sources and means of calculating these variables are presented in Appendix IV. Further, the results are robust to the inclusion of the party-in-power controls, which indicates that our conclusions are not impaired by nonrandomness or omitted variable bias. Neither Model I nor Model II found the proportion of accidents with a recorded vehicle contributing factor to be significant.

Several other regression variables were found to have a statistically significant correlation with the fatality rate. Models I and II found the mean age of vehicles involved in accidents to be positively correlated with the fatality rate. This finding is supported by studies in the literature showing that, given that an accident occurs, occupants of older vehicles are more likely to be fatally injured (O’Donnell and Connor 1996; Martin and Lenguerrand 2008). Both FE regressions also found the proportion of fatal accidents involving DUI to have a significant positive correlation with the dependent variable. This may be attributable to the fact that drunk drivers tend to drive more aggressively: Zador et al. (2000) found that “the relative risk of involvement in a fatal vehicle crash increased steadily” as driver blood-alcohol content increased.

Model I indicates an inverse relation between fatality rates and median driver age—supporting several similar findings in the literature (McCartt et al. 2009). Model I also assigned negative coefficients for the variable corresponding to the proportion of fatal accidents where speeding was recorded. Although the analyses presented here do not include a means to assess the reason behind this relationship, one potential explanation may come from evidence that points to the idea that speeding-related crashes tend to involve single vehicles with a single occupant, in constrast to accidents with multiple fatalities, which are more commonly attributable to other causes (Høye 2020).

Both models indicated that states with more registered passenger vehicles per capita had a lower fatality rate. This relationship has been explored extensively in the literature. Smeed (1949) first showed how increased traffic density would tend to decrease the number of roadway fatalities per vehicle (Oppe 1991; Ross 1985). Model I also indicated a significant negative effect of state population, suggesting that states with higher populations may have fewer road accidents per registered passenger vehicle. Further analyses are warranted to fully explain these correlations. However, the authors posit that this may be due to a concentration of urban centers in states with higher populations, where vehicle density is higher, in addition to fewer rural miles driven per capita.

With respect to additional demographic variables, Model II found there to be more road fatalities in states where a greater fraction of road miles were traveled on rural roads—in keeping with most similar studies in the literature (Peltzman 1975; Zlatoper 1989; Merrell et al. 1999)—and in states with a lower GDP (supporting the so-called Peltzman effect hypothesis). The positively correlated GDP (and the positively correlated median household income) aligns with findings in the literature that higher-income drivers are less likely to drive defensively and therefore more likely to be involved in accidents (Shinar et al. 2001; Males 2009). The positive coefficients may also be caused by a positive correlation between GDP and recreational travel (McMullen and Eckstein 2012). Increased travel, especially long-distance travel and driving on rural roads, would increase the number of fatal accidents. Model II also found a statistically significant relationship between the party in power in a state legislature (i.e., the Dem variable) and the adjusted roadway fatality rate. This party-in-power variable also allows us to test Leigh’s hypothesis that I/M program so-called strength may be politically endogenous (Leigh 1994). Further, as noted in several examples in the literature, the political party of state governments also impacts key economic indicators, including “pollution, spending, policies, and labor market outcomes” (Beland 2016, p. 2).

It bears noting that neither regression found the proportion of fatal accidents where a contributing factor was recorded to be a significant predictor of accident rates—further supporting the hypothesis that these data may not be complete, as discussed earlier.

The supplementary regression developed to further examine this relationship (Table 5) showed a negative correlation between the treatment variable and fatal accidents involving a vehicle contributing factor. However, the regression has a low coefficient of determination, implying that the presence or absence of I/M programs and other exogenous variables still do not explain most of the variation in the number or proportion of these accidents with a recorded contributing factor. Since I/M programs are designed to address these factors, the weak treatment effect shown in this regression may appear to contradict the main finding of the other FE specifications presented. Although this dichotomy merits further investigation, we hypothesize that it may be explained by the lack of sufficiently high-resolution data (especially when compared to the variables and data sets used for Models I and II) on vehicle contributing factors in fatal accidents. Further, we hypothesize that I/M programs affect fatal accidents where—even though no vehicle contributing factor was recorded—the effect of subpar maintenance may have been compounded by factors such as road or weather conditions.

The relationship between I/M programs and vehicle maintenance, as well as between vehicle maintenance and accident rates in the United States, needs to be further examined. Unlike the randomized trials conducted in Norway by Fosser (1992) or Christensen and Elvik (2007), this study relied on fatal accident data and so could not control for the effect of inspection and maintenance programs on those vehicles that were not involved in a fatal accident. Data on vehicle maintenance and defects are not widely available in the United States, except for vehicles appearing in the FARS database.

Our results affirm—based on data from 50 states and the District of Columbia over a 44-year period—that I/M programs have a negative and causal relationship with roadway fatalities and that these programs are effective in their stated aim of mitigating roadway fatalities. In this paper, we choose not to comment on the financial cost of I/M program administration or on the potential public cost savings from mitigated accidents and fatalities. Though acknowledging these to be important factors, we argue that legislative bodies must consider the reduction in fatalities as a statistically significant benefit resulting from inspections when debating the establishment or repeal of state safety I/M programs.

The findings of this study are limited to fatal accidents, which comprise about 0.5% of all road accidents occurring in the United States each year (NHTSA 2020c). Based solely on the analyses presented here, no inferences may be made about the impact of I/M programs on less severe motor accidents; however, Blows et al. (2003) showed that changes in the rate of all motor accidents are of the same order as changes in the rate of fatal accidents. We posit that safety inspections will only become more important as advanced driver assistance systems (ADAS) and autonomous vehicle (AV) technology become more prevalent, and although several international jurisdictions have already adapted safety inspections to include testing and calibrating ADAS systems, they have not yet been applied in the United States (Bellon 2020). Future analyses could consider the vehicle-level differences in the availability of safety features and how they may help to contribute to highway safety along with I/M programs.

Data from FARS (which has a unique record for each fatal accident and for each involved vehicle) and other sources were used to develop regression variables corresponding to each instance of the dependent variable (i.e., statewide, annual means for each of 50 states, for each year from 1975 to 2018). An inverse hyperbolic sine transformation was applied to the dependent and independent variables, allowing for easier interpretation of results.

As discussed in the “Methodology” section, only a subset of FARS data was included in these analyses. Specifically, accidents where one or more of the vehicles involved were either registered outside the state where the accident occurred or were not passenger vehicles (as recorded in FARS) were excluded. Fig. 5(c) shows that despite these restrictions, the analysis was built on over 81% of all available data in 2019. As shown in Fig. 6, over 80% of accidents from FARS data were included in the analysis for each year in the period 1975–2019, totaling over 1.33 million fatal accidents.