Assessing the Impact of Speed-Limit Increases on Fatal Interstate Crashes - Discussion 2

Michael D. Fontaine
Tongbin Teresa Qu
Texas Transportation Institute

Karl Zimmerman
Clifford H. Spiegelman*
Texas A&M University

The Balkin/Ord paper has addressed the timely and controversial topic of whether speed-limit increases raise the frequency of fatal crashes. Earlier studies did not have sufficient data to determine the true relationship between speed-limit increases and fatal crashes. Enough time has now elapsed since the repeal of the national maximum speed limit (NMSL) in late 1995 to determine if there was a significant increase in fatal crashes. The structural model chosen by the authors certainly appears to be an improvement over models used in earlier studies.

One of the most important parts of scientific and engineering studies is the formulation of hypotheses. Studies of the safety effects of increased highway speed limits could focus on the total number of injuries, fatalities, injury crashes, fatal crashes, or many other measures. This study focuses on the number of fatal crashes. The authors fit the crash data to a structural model and do not attempt to explain the parameters estimated. Here we will try to extend the discussion begun by the Balkin/Ord paper in many important respects, such as giving alternative factors that might be modeled. We also provide a general discussion of study validity.

The study authors seem be looking for an effect independent of confounding factors and covariates. Confounding factors are common in field studies even when the study focuses on effects known to be practically important. For example, smoking is known to affect health, but there are several other factors such as diet, family health history, and exercise that should be taken into account when studying the effect of smoking. See, for example, Yano et al. (1977) as an example of a smoking-effect study that uses covariates. Including potentially important factors in an explicit manner was beyond the intended scope of the Balkin/Ord study.

It is unclear how the current study implicitly handles vehicle-miles of travel (VMT), increased availability of and different forms of airbags, or many of the other possible covariates we list in our discussion. The study authors appear to assume that changes in fatal crashes occur independently of all factors except the speed-limit increase. To some extent, they have shown that an increase in fatal crashes happening independently of other important factors may be a small, sporadic effect. This study, much like many studies of health effects, may not show as strong or convincing an effect because other important factors were not explicitly modeled.

Study Validity

The purpose of the Balkin/Ord study was to determine whether an increase in the speed limit resulted in a higher incidence of fatal crashes. The authors hypothesized that the change in speed limit results in a permanent shift in the number of fatal accidents. The general approach used was first to explore trends in the data, then identify the discontinuity of the trend at the time of speed- limit increases, and finally draw conclusions on whether the speed-limit change resulted in higher numbers of fatal crashes. Two questions need to be answered for the purpose of this study. First, can a trend interruption be observed at the times of speed-limit increases? Second, was the interruption caused by the increases in speed limits? The authors attempted to answer the first question by applying their structural model. No attempt was made to determine if the increase in speed limit was solely responsible for any change in fatal crash frequency. The authors simply indicate whether the speed-limit increase resulted in a discontinuity. Their conclusions were made without considering possible effects from external factors such as weather, traffic, road user demographics, composition of the vehicle fleet and so on.

This study can be best described as a time-series quasi-experiment study. Compared to a true experiment, a quasi-experiment lacks full control over the events and subjects being studied, in terms of random assignment of treatments to subjects (Cook and Campbell 1979). In this study, the researchers could not control the population group, location, timing, or manner in which the speed limit was increased. The monthly data from January 1975 to December 1998 on fatal crashes both before and after the speed-limit increase forms the time-series quasi-experiment problem.

The concepts of internal and external validity are essential to obtaining meaningful results from any experimental design. "Internal validity is the basic minimum without which any experiment is uninterpretable," while "external validity asks the question of generalizability" (Campbell and Stanley 1966). In other words, any experimental design must be internally valid to yield reliable results and be externally valid to provide useful predictions about the effect of that treatment (in our case a speed-limit increase) to other populations and times.

The time-series design is generally internally valid with only one major limitation, namely, rival events (called "potential interventions" by the authors). Rival events occurring at the same times as speed-limit increases are the most serious threat to the internal validity of the authors' findings. These rival events could be responsible for any observed change in crash frequency or for masking changes in the fatal crash data. Rival events also provide potential alternative explanations for these findings. This problem can be overcome when the likelihood of rival events can be discounted. The authors did acknowledge the existence of potential interventions besides the speed-limit increase. The authors, however, did not give any explanation why potential interventions were not the causes for the observed effect or did not mask an effect that might have occurred.

In fact, rival events could plausibly cause the shift in fatal accident counts. For example, in the case of rural Arizona where increases in fatal crashes were found to be significant at the first speed-limit change, several issues can be raised: 1) Was there also an unusually high increase in VMT, which might be the cause of the increase in crashes? 2) Were there any severe weather events possibly causing bad road conditions, in turn causing more crashes? Winter weather could have played a role in short-term increases in the number of fatal crashes following the speed-limit increase in 1995 since raising speed limits was permitted as early as December. To ensure internal validity, these rival factors and combinations thereof must be ruled out as the causes for the significant increases in fatal crashes. The list of rival factors could be different for different states. However, such lists could possibly be extensive for all states. Considerable information about local conditions for each state is required to isolate the effect of the speed-limit increase from other rival factors.

The strength of the time-series approach is that fatal crash data before and after the speed-limit increases provide the possibility of exploring the existing trends and patterns in the data so that a discontinuity of the existing trend can be detected. As the authors pointed out, a simple before/after study would not be appropriate in this case. Simply comparing the count of fatal accidents immediately before to the count of accidents immediately after and then attributing the difference to the speed-limit increase would be misleading.

The external validity of the time-series design has serious problems. It is clear that the effect of the speed-limit increase is specific to the individual states. As shown in this study, some states have significant increases in fatal crashes, while some states have insignificant increases, and some essentially do not change. The legitimacy of the authors' conclusions generalized across states in this study is therefore uncertain.

The time-series approach is appropriate for this study. However, more study is needed to isolate the effect of speed-limit increase from the effects of other potential interventions. The authors' analysis does not sufficiently isolate the impact of the speed-limit increase from rival explanations.

Data Limitations and Examples of a Few Confounding Factors

Fatal crashes represent a serious safety concern and are an important measure to examine. However, fatal crashes are relatively rare events and their counts may show quite a bit of instability from year to year and from month to month. For example, figure 1 in the paper shows that between 0 and 20 fatal crashes occurred each month on Arizona rural interstates. There is quite a bit of fluctuation from month to month in this figure, and it may be difficult to determine a significant trend based on fatal crashes alone. An examination of injury crashes would probably provide a more stable data set for this analysis. This paper provides a valuable indication of the possible impact of speed-limit changes on fatal crashes. However, there are some areas where this paper is unclear about the data used to perform this analysis. There are also potential opportunities to take this analysis in new directions that could provide, in our opinion, a more accurate examination of the impact of the speed-limit changes.

First, it is not clear from the paper whether the authors assumed that all states changed their speed limits in April 1987 and then again in December 1995. An assumption of uniform intervention dates across all states creates issues with their analysis. While many states did change their speed limits as soon as they were legally able, many other states did not enact a higher speed limit until much later. For example, Virginia did not choose to raise its speed limit to 65 miles per hour (mph) on rural interstates until July 1988 (Jernigan et al. 1994). Louisiana did not increase its interstate speed limit to 70 mph until August 1997 (USDOT NHTSA 1998). If these time periods were not correctly categorized in the analysis, the results could be inaccurate. It is not clear whether the authors changed the intervention dates on a state-by-state basis or used a uniform intervention date for all states.

In 1987, states were permitted to increase speed limits on rural interstates to 65 mph. This created a uniform speed-limit change in those states that chose to increase speed limits. In 1995, the NMSL was repealed, allowing states to set their own speed limits. Unlike the 1987 speed-limit change, this resulted in some variation in the interstate speed limits established across the nation. Some states raised speed limits to 70 mph, while others raised the limit to 75 mph. Some states, such as Texas, enacted differential speed limits for cars and trucks. Studies have shown that both the absolute speed of vehicles and large differences in speeds among vehicles in the traffic stream can be significant causal factors of crashes (Cirillo 1968; Beatty 1973). Given these studies, it appears that the impact of the both magnitude and type (differential or uniform) of speed-limit change should be considered when assessing the impact of the repeal of the NMSL. This could explain some of the differences in results observed by the authors.

In addition to differences in the magnitude of the speed-limit change, drivers also reacted differently to the speed-limit increases from state to state. Some states were experiencing a very high degree of motorist noncompliance with speed limits prior to the repeal of the NMSL. In these cases, actual speeds may not have changed very much following the repeal of the NMSL. Studies have shown that drivers in different states reacted very differently to the same speed-limit increases. For example, studies performed in Michigan and California showed relatively small increases in mean speed of only 1 and 2 mph, respectively, after the speed limit was increased 5 mph to 70 mph (Retting and Green 1997; Nolf et al. 1998). In Texas, mean speeds were observed to increase by 5 mph when the speed limit was increased 5 mph to 70 mph (IIHS 1996). If all changes in crash frequency could be attributed to increased travel speed, it would be expected that states that experienced smaller increases in travel speed would exhibit smaller increases in crash frequency. The relationship between the magnitude of actual observed travel speeds and crash frequency bears further investigation.

Analysis of urban crashes also presents a number of additional concerns. Speed-limit changes were not always uniform in urban areas. It is a reasonable assumption that rural interstates would be posted at the maximum speed allowable by law. However, in urban areas road geometry, safety considerations, congestion, and high volumes of traffic may preclude posting the speed limit at the legal maximum. In many urban areas, a 55-mph speed limit was retained on some roads even though a higher speed limit was legally possible. Given that speed limits were not always increased on urban interstates, it may be difficult to determine if an increase in the speed limit was responsible for any observed increase in crash frequency in urban areas. In fact, roads where the speed limit was increased may actually represent a minority of the roads, which may dilute potential impacts of the increased speed limit in this paper's analysis. Factors such as increasing congestion and greater prevalence of work zones should be examined as possible alternative explanations for any observed crash increases in urban areas.

Additional Covariates

Crashes occur for a wide variety of reasons, including driver error, vehicle breakdown or failure, poor roadway conditions, poor operating conditions, and all combinations of these factors.

For the sake of example, consider rollover crashes, one of the most severe types of crashes. The frequency of fatal rollover crashes is affected by any or all of the following:

• driver characteristics (age, gender, personality, experience, alcohol and drug use, fatigue)
• vehicle characteristics (type, loading, maintenance level)
• roadway characteristics (functional classification/design standard, curvature, delineation, illumination)
• environmental characteristics (time of day, visibility, precipitation, traffic volume)

The above list is not all-inclusive. Some of these factors may not be very important and some difficult to quantify, but all of them can play a role in fatal crashes.

A few possible covariates are of particular concern because of their obvious effect on several of the factors shown above. These may include:

• effects of winter precipitation
• percentage of trucks on a particular roadway
• differences in the amount of speed-limit increase from state to state
• "spillover effects" in states that did not increase speed limits
• uneven changes within a state
• the general population's learning curve in adjusting to higher speed limits

The effects of winter precipitation, particularly sleet or snow remaining on the roadway for an extended period, may be very important. In Texas, there were three months with unusually high numbers for injuries and fatal crashes after the last speed-limit increase. These were February 1996, January 1997, and December 1998 (see figure 1). Each of these occurrences corresponded to a major winter storm, which tends to be a rare event in Texas (see figure 2). Two of these events early in the "after" period could skew the results and may have in at least one analysis (Griffin et al. 1998). However, this effect will vary by location within the United States. A winter storm considered severe in Texas may be fairly normal winter weather in Minnesota, for instance.

Another environmental consideration is the percentage of trucks in the traffic stream. Not all interstate routes are equal in terms of truck traffic, with trucks composing over 50% of traffic on some routes in Texas and Nebraska. This has an effect on other traffic and means that trucks are more likely to be involved in a collision. Because trucks have a much larger mass than passenger cars, the risk to the occupants of the passenger vehicle is very high. Also, trucks are tall with high centers of gravity and are less stable under virtually all conditions than a passenger vehicle is. In Texas, the number of crashes involving a truck generally followed the total number of crashes, but this may not necessarily be true elsewhere in the country.

Another effect might be the spillover speed effect caused when one state changes its speed limits and another one retains the old ones. An example of this is Nebraska, with interstate speed limits increased from 65/55 to 75/65, and Iowa, with the older 65/55 speed limits retained. It is possible that crashes in Iowa, for instance, may be affected more by the changes in neighboring states because of greater variations in speed. The spillover effect could be a source of some significant results in states that did not increase their speed limits in 1996, such as Maryland, Pennsylvania, and Tennessee. The idea of a learning curve deserves mention. In one section of the paper, the authors claim that the effects of such a change in driver behavior would be relatively short-term in nature and could safely be ignored. Later, the authors use it to explain the decrease in fatal crashes in Arizona after the initial increase in 1996. The same type of reduction occurs in Texas (rural), Oklahoma (urban), and Nevada (urban). The reduction might indeed be due to drivers becoming more accustomed to higher speeds. It could also be due to different weather patterns, changes in law enforcement (speed and otherwise), road construction, or any one or more other possible factors. Also, the effect is a year or two after the speed limit change, not a few months as the authors earlier claimed. If the learning curve is indeed short-term, then the later effects must be something else entirely.

Summary

We thank Balkin and Ord for providing a means of discussing the impact of the 1995-1996 speed-limit increase. Their study represents an improvement in the series of studies of the effect of speed-limit increases. The study, however, is far from the final word on the impact of the speed-limit increase. In our opinion, their study did not pay enough attention to its conclusions' validity. We feel that a more comprehensive study that takes into account additional explanatory factors needs to be done if the public is to know the true effects of the speed-limit increase.

References

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Cirillo, J.A. 1968. Interstate System Accident Research-Study II-Interim Report II. Public Roads 35, no. 3.

Cook, T.D. and D.T. Campbell. 1979. Quasi-Experimentation, Design and Analysis Issues for Field Settings. Boston: Houghton Mifflin Company.

Griffin, L.I., O. Pendelton, and D.E. Morris. 1998. An Evaluation of the Safety Consequences of Raising the Speed Limit on Texas Highways to 70 Miles Per Hour. Texas Transportation Institute, Texas A&M University.

Insurance Institute for Highway Safety (IIHS). 1996. Urban Freeway Speeds Jump in First States to Raise Speed Limits. Status Report, 31, no. 5.

Jernigan, J.D., S.E. Strong, and C.W. Lynn. 1994. Impact of the 65 Mile Per Hour Speed Limit on Virginia's Rural Interstate Highways: 1989-1992 Final Report. Virginia Transportation Research Council, Charlottesville, VA.

Nolf, S.A., T.L. Maleck, W.C. Taylor, and T.S. Czewski. 1998. An Evaluation of the Michigan 70 MPH Speed Limit, in 77th Annual Meeting Preprint CD-ROM, Transportation Research Board. National Research Council, Washington, DC.

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U.S. Department of Transportation (USDOT), National Highway Traffic Safety Administration (NHTSA). 1998. The Effect of Increased Speed Limits in the Post-NMSL Era. Federal Highway Administration, Washington, DC.

Yano, K., G.G. Rhoads, and A. Kagan. 1977. Coffee, Alcohol, and the Risk of Coronary Heart Disease among Japanese Men Living in Hawaii. The New England Journal of Medicine, 297.

Address for Correspondence

Clifford H. Spiegelman, Department of Statistics, Room A447 Blocker Bldg., Texas A&M University, College Station, TX 77843-3143. Email: cliff@stat.tamu.edu.