Better to see Chapter 11 Occupant protection ,
Chapter 13 Measures to improve traffic safety and
Words only (no formatting, figures, tables, or photographs) from 1991 book
Chapter 10. RESTRAINT-USE LAWS, USE RATES, AND FIELD EFFECTIVENESS (From 1991 book Traffic Safety and the Driver)
While equipping a vehicle with a passive occupant protection device, such as an airbag, is expected to automatically reduces risk, the same is not true for active devices such as safety belts. Adding safety belts reduces risk only if they are worn. It is only in the limit of 100% wearing rates that the field effectiveness, or actual reduction in fatalities in a population of drivers in vehicles equipped with belts, will equal the when-used effectiveness values in Table 9-6. For passive devices (assuming that they are not disabled) there is no distinction between when-used and field effectiveness.
Notwithstanding the safety benefits provided by belts, voluntary wearing rates have generally been low. Many efforts have been made to increase such rates by motivational and informational campaigns [Robertson et al. 1974; Geller 1984; Nagayama 1990]. While some such measures have generated increases in use rates, these have been small compared to use increases from mandatory belt-wearing laws.
Influence of mandatory belt-wearing laws on use rates
The first mandatory belt-wearing law in a jurisdiction with a substantial car population came into effect on 22 December 1970 in Victoria, one of the states in Australia [Trinca 1984]. (Malawi and the Ivory Coast appear to have had earlier laws [Grimm 1988]). The Victoria law required drivers and front passengers in seats equipped with safety belts to fasten them. In 1971 about 75% of driver seats in cars in Victoria were equipped with belts, over 90% of these being lap and shoulder belts. As all new cars were required to have belts, the rate soon approached 100%. In the first year of the law about 75% of drivers in cars equipped with belts wore them. Andreassend  estimates that as a consequence of the law, deaths to drivers and left-front passengers declined by about 12% in 1971 when the overall use rate was about 50%. By January 1972, the compulsory wearing of safety belts, if fitted, for occupants over 8 years of age applied throughout all Australian states [Trinca 1984].
By mid 1990, 40 countries had mandatory wearing laws, as did all 10 Canadian provinces and 34 US states (plus DC) [Grimm 1988; 1990]. Even though four US states (Massachusetts, Nebraska, North Dakota and Oregon) have repealed laws by referendum, 84% of the US population lives in states with laws [Campbell, Stewart, and Campbell 1988]. While belt-wearing rates in excess of 90% have been often observed in some Australian states, the UK, Japan, Finland, and West Germany, much lower rates, often under 40%, occur in other jurisdictions [Grimm 1988; 1990].
In the US from the early 1970's to the mid 1980's, before there were any mandatory wearing laws, belt-wearing rates were relatively stable at close to 14%. The first mandatory wearing law in the US became effective in New York State in December 1984, well after such laws had become widespread in the rest of the world. US wearing rates, based on daytime samples in 19 cities [National Highway Traffic Safety Administration 1989], now average 46%. The rate for cities without wearing laws is 33%, and for those with laws is 50%.
It is not as simple as it might appear to obtain an accurate estimate of belt-wearing rates. A common technique is to place observers on the sidewalk near traffic lights, so that belt use of occupants in stationery vehicles can be noted. When traffic is moving, reliable observation becomes more difficult, although in some cases rural use is estimated. Although fatality crash risks peak at night (Figs 4-12 and 7-5), it is not generally possible to obtain nighttime wearing rates. Apart from the obvious difficulty of observing in the dark, there are questions of danger to observers and low traffic volumes which lead to substantially higher costs per observation. So, estimates of wearing rates for jurisdictions are necessarily extrapolations of data from a few specific sites at restricted times.
While the influence of wearing laws on use rates is different in detail for each jurisdiction, there are some recurrent general patterns. Fig. 10-1 shows data from the UK, where belt wearing became compulsory on 31 January 1983. The law is associated with a steep increase in belt wearing from 40% to over 90%.
Fig. 10-1 about here
More modest increases in belt wearing occurred with the passage of various mandatory wearing laws in the US. Fig. 10-2 shows fairly typical data for two states, both of whose laws came into effect in July 1985 (month 0 in the graph). The increases prior to the laws apparent for Michigan, and also in Fig. 10-1, are fairly typical, and arise because of media discussion and possible confusion about when belt-wearing is mandatory as distinct from when the legislation is passed. Also typical is an immediate increase in wearing rates just after the passage of the law, followed by a decline to a lower level, but one still substantially above the pre-law level.
Fig. 10-2 about here
The use rate levels in Fig. 10-2 were in response to secondary enforcement, meaning that police officers were not empowered to stop vehicles solely because they observed occupants not wearing belts. Citations for non wearing could be issued only after vehicles were stopped for some other reason, such as speeding or defective equipment. In efforts to increase wearing rates, a number of jurisdictions have changed from secondary to primary enforcement, which does allow police to stop vehicles and issue citations based solely on wearing-law violations. The effect of increasing enforcement in a state with a primary law, North Carolina, is shown in Fig. 10-3.
Fig. 10-3 about here
Campbell  finds considerable evidence (Fig 10-4) that increasing the level of enforcement leads to increased belt-use rates.
Fig. 10-4 about here
CALCULATING CASUALTY CHANGES FROM BELT-USE CHANGES
While changes in belt-wearing rates attributable to passing wearing laws can be measured readily, it is much more difficult to determine directly with much precision any consequent changes in casualties, as is discussed in later sections. In order to anticipate better the magnitude of effects to be expected, we first derive an equation estimating changes in driver fatalities when belt-use rates change from some initial value to a new value. (For expository convenience, the derivation is described in terms of fatalities, though the ideas and equations are applicable to all injury levels). If belt wearers had crash rates that were the same as those for non-wearers, then estimating changes in driver fatalities associated with changes in belt-wearing rates would be relatively simple. However, copious evidence (cited in Chapter 9) shows that belt wearers are less risky drivers than belt non-wearers. Therefore, if additional drivers are recruited to belt wearing (when belt-wearing rates are low), these drivers are likely to be of below average risk. Hence the reduction in fatalities would be less than if the same number of average drivers became wearers. The process by which it is the safer-than-average drivers who switch from non-wearing to wearing has been labelled "selective recruitment" [Evans 1985].
Simple calculation ignoring selective recruitment
To clarify the discussion of expected casualty changes from changes in belt-use rates we first develop a "simple calculation" based on the (incorrect) assumption that, apart from their decision on belt use, belted and unbelted drivers behave similarly. We introduce the following notation:
ui = initial, or old, belt-use rate Eqn 10-1
uf = final, or new, belt-use rate Eqn 10-2
Du = uf - fi = change in belt-use rate Eqn 10-3
F = fractional reduction in fatalities Eqn 10-4
E = when-used belt effectiveness Eqn 10-5
Assuming that all drivers have identical crash rates, it can readily be shown [Evans 1987a; Hedlund 1986] that
F = E Du/(1 - E ui) Eqn 10-6
If an initial use rate of zero increases to 100%, Eqn 10-6 reproduces the definition of E. The simple calculation, Eqn 10-6, has the characteristic that, starting from the same initial use rate, fractional reductions in fatalities increase linearly with increases in belt-use rate. In order to obtain an estimate of F that reflects the important differences between crash rates of wearers and non-wearers that are ignored in Eqn 10-6, quantitative estimates of such differences are required.
Belted compared to unbelted driver crash rates
The ratio R, defined as
involvement rate for unbelted drivers
R = ───────────────────────────────────── , Eqn 10-7
involvement rate for belted drivers
is estimated in Evans [1987b] for involvements in various types of crashes, and also for traffic violations. Seven essentially independent estimates of R are obtained (Table 10-1); three use FARS data, and four use data from the State of Michigan giving crash and traffic violation records of drivers whose belt use was determined from photographs of them driving in traffic.
Table 10-1 about here
The first estimate is based on comparing belted and unbelted daytime driver fatalities to the number expected, based on the 14% use rate in Michigan at the time, and the when-used effectiveness of safety belts. The second (and third) estimates compare the numbers of pedestrians (motorcyclists) killed in daytime crashes with cars driven by belted drivers to the number killed in crashes with unbelted drivers.
The remaining four cases in Table 10-1 are based on studies in which approaching cars were photographed on Michigan roads [von Buseck et al. 1980; Evans and Wasielewski 1983; Wasielewski 1984]. Driver safety belt use was noted from the photograph, as was the car license-plate number, which, through the cooperation of the Michigan Department of State, yielded information on the car's registered owner, including his or her driver license number. Cases in which the driver photographed appeared different in age or sex from the one described in the driving record were excluded; if not so excluded, it was assumed that the observed driver was the one whose record was provided, and that the observed safety belt use could be associated with that driver. From the driver license file, the driver's record, including crashes and traffic violations (there was then no law requiring belt wearing) were obtained. All the observational data also included a measure of driver risk taking, either following headway or travel speed; in Table 10-1 this is used only for identification purposes.
For all seven cases studied, unbelted driver involvement rates are 28% to 86% higher than those for belted drivers. A feature not noted in the original paper [Evans 1987b] is that the seven values divide rather cleanly into the three lowest (from R = 1.28 to 1.37) and the four highest (from R = 1.57 to R = 1.86). The three lowest values all refer to essentially two-vehicle crashes (the great majority of police-reported crashes involve two vehicles), whereas four highest refer more to single-vehicle incidents. This therefore presents another example of the distinction between, on the one hand, involvement, and on the other hand, responsible involvement, which is discussed in Chapter 7. Many of the safer belted drivers were crash-involved because of the actions of the drivers of other vehicles, which reduces the proportional difference between involvement rates of the safer and the less safe.
The average of the seven values in Table 10-1 is 1.53, meaning that unbelted drivers are 53% more likely to be involved in crashes than belted drivers. An essentially similar value is obtained by Hunter et al.  using a survey method. We therefore use R = 1.53 to capture quantitatively the selective recruitment phenomena in a calculation of how fatality reductions are expected to depend on changes in belt use.
Calculation including selective recruitment
The central concept behind the calculation is that differences in risk taking between belted and unbelted drivers observed consistently in so many studies reflect an underlying continuous relationship between propensity to wear a belt and crash rate. Consider all the drivers in a population rank ordered from the most willing to the least willing to wear a belt. Conceptually, one can imagine any level of belt use occurring for such a population of drivers, depending on external motivation. Presumably, if wearing were heavily taxed, wearing rates would approach zero, whereas if non-wearing were severely punished, rates would approach 100%. As the motivational level is increased, more and more unwilling drivers, with ever higher and higher crash rates, become users. The only observational data is that the average crash risk for the 86% of non-users observed in Michigan is 1.53 times the average rate for 14% of users. From this information, a fairly robust relationship between fatality changes and belt-use changes is derived in Evans [1987a], which can be expressed as
E Du [1 + k (u + u u + u ) ]
i i f f
F = ──────────────────────────────── , Eqn 10-8
1 + k - E u (1 + k u )
where the parameter k captures the selective recruitment effects and is given by
k = (R - 1)/(1 + b + b2 - R b2 ) = 0.4692, Eqn 10-9
where b is the use rate, namely 0.14, for the studies from which the unbelted to belted risk ratio R = 1.53 is derived.
While Eqn 10-8 might appear somewhat complicated, it is based on fairly simple assumptions. Because the fatality reductions depend on both final and initial belt-use rates, it is not possible to display Eqn 10-8 in simple graphical form. The quantitative results are relatively unchanged for different choices of plausible assumptions provided belt non-users have crash rates 53% higher than users. If R = 1, meaning that there is no selective recruitment, then k = 0 and Eqn 10-8 reduces to the simple case, Eqn 10-6.
Fatality changes compared to zero belt use
One case of particular interest is determining the total casualty reductions from belt use; that is, comparing the reduction in fatalities for some belt-use rate compared to zero belt use. If ui = 0, and u = uf = Du, then Eqn 10-8 gives
F = E u (1 + k u2)/(1 + k) . Eqn 10-10
Fig. 10-5 shows F plotted versus u. Also shown as a straight line is the simple model calculation.
Fig. 10-5 about here
The data points plotted are estimates of fatality reductions reported by Partyka and Womble  (the numerical values appear later in Table 10-2). These are estimated using data on fatally-injured driver and right-front passengers coded in FARS as using a restraint system. These fatality data, together with the known effectiveness of the belts, are used to estimate the number of belted occupants who, but for the belt, would also have been killed, from which the percent reduction in driver and right-front passenger fatalities is estimated.
It is clear that the curve (Eqn 10-10) provides a much superior fit to the data than the straight line (Eqn 10-6). The data are systematically lower than the curve, but by fairly small amounts. Partyka and Womble  show that these same data fitted well a quadratic function of u. It should be stressed that the curve in Fig. 10-2 is not a fit to the data -- the equation was published prior to the availability of the data.
While the agreement between the data and Eqn 10-10 is good, one must keep in mind that the data are not directly-observed fatality reductions, but inferences from fatalities. If there were 100% belt use, then the calculated data are constrained to agree identically with the curve (ignoring differences that arise because Partyka uses a 45% effectiveness whereas the equation uses 41%). Thus there is sufficient overlap in the computations required for the data and for the curve that each does not provide an entirely independent check on the other. However, the closer agreement with the curve than with the straight line does reflect real agreement which increases confidence that the more general form, Eqn 10-8, may also be reasonably accurate.
OBSERVED CASUALTY CHANGES FROM CHANGES IN BELT USE
The ideal evaluation of a public-health measures would be a clearly observed change in the harm that the measure was enacted to reduce. It is rarely possible to provide such evaluations, which are generally not even contemplated. For example, a new heart operation, no matter how successful, cannot be expected to generate observable changes in the total number of deaths from heart disease, because that total number is far too large, and therefore subject to large random variation. The only feasible (even if flawed) evaluation of such an intervention is the standard one of comparing recovery rates of patients undergoing and not undergoing the procedure. Such an evaluation cannot address the possibility that improved heart surgery might encourage increased smoking, and thereby generate a net increase in heart and other disease. However, it would be unreasonable to interpret the lack of a measured decline in hear-disease deaths as indicating that this did indeed happen. Such data would argue that the intervention was ineffective only if they did not show a decline larger than that calculated in terms of the likely efficacy of the operation, when applied, and the number of operations.
The tradition of expecting directly observable casualty reductions from passing safety-belt wearing laws became established because unrealistically large, readily observable, casualty reductions were promised. Such promises were based on assuming unrealistic when-used effectiveness, assuming unrealistically large and sudden increases in belt use, and, more understandably, ignoring selective recruitment effects. If a halving of fatalities is promised, then a change should be readily apparent. However, laws have typically increased use rates from about 20% to about 40%, which Eqn 10-8 calculates will reduce fatalities by 6.7% for those covered, who typically constitute well under half of all road users. It is exceedingly unlikely that such a difference can be measured using data from a typical jurisdiction with a few hundred relevant fatalities per year; it is even more improbable that a 3% reduction in total fatalities can be detected. Early promises of large reductions, followed by no discernible decrease, gave rise to many explanations, including that compulsory belt-wearing laws induce collective increases in driver risk-taking that reduce the benefits to the belted occupants while at the same time placing other road-users at increased risk [Adams 1985].
Directly observing casualty changes -- difficulties and methods
From the point of view of ease of evaluation, one would like use rates to increase overnight from 0% to 100%, nothing else to change, and to have as large a population as possible affected by the law. These conditions cannot be attained even approximately. Even before wearing laws are discussed, use rates are well above zero; laws are introduced only after much debate and media coverage, which usually generates increases in use rates prior to the passage of the law (Figs 10-1 to 10-3). Thus, increases in belt use occur in the pre-law period. After wearing is required, rates may increase only modestly more (Fig. 10-3) until another law increasing penalties is enacted. Thus, instead of a steep step-function increase in use rates, a more gradual increase generally occurs which makes evaluation difficult. In federal nations like Australia, Canada, and the US, laws are introduced one state or province at a time, so that sample sizes are generally inadequate relative to the size of effects.
Even without changes in laws, casualties change for a variety of reasons. Note particularly the seasonal effects in Figs 4-8 to 4-10; US traffic fatalities in July and August are typically 50% higher than in January and February. In the face of such large monthly variation, a 7% effect from a belt-wearing law is going to be exceedingly difficult to observe. Taking periods of whole years before and after enactment will remove effects due to monthly variation, but introduces variation from other sources, such as economic changes (Fig. 11-3), or a general change in time (Figs 13-1 to 13-4). In addition to variation from sources that can be to some extent explained, there is of course additional unexplained random variation.
There is no entirely satisfactory solution to these formidable difficulties. We can identify five approaches to estimate the casualty changes from wearing laws.
1. Interrupted time-series analyses. Apply statistical time series analyses to the pre-law casualties, and generate equations which predict what post-law casualties would have been if the pre-law trends had continued. A comparison with the observed post-law data gives an estimate of the effect of the intervention. Among the difficulties here is that the method usually relies on monthly data, which, for fatalities, provide relatively small sample sizes. Another difficulty is the inherent complexity of the models. It is difficult for anyone other than the researchers actually doing the work to get a feel for the source of the estimates.
2. Control jurisdiction. Compare the ratio of post- to pre-law casualties to a corresponding ratio for the same periods in a control jurisdiction which had no law change. The aim here is that all effects due to seasonal, economic, etc. factors will be taken account of by the control jurisdiction, so that any remaining difference can be attributed to the law. This approach has been applied to US and Australian states, and to Canadian provinces; it has little possibility of application to the majority of countries, which have nation-wide traffic laws. The negative features of this approach are that the choice of the control jurisdiction is arbitrary, and control jurisdiction sample sizes place additional constraints on precision.
3. Control occupant. Compare the ratio of casualties to affected road users (say car drivers) to those for non-affected, or control, road users. There are various choices for control road users, such as truck drivers (if not affected by the legislation). Pedestrian and motorcyclist fatalities can be used only if it is assumed that the wearing laws do not influence casualties to these road users. Other occupants in the same car as the driver cannot be used to estimate the effect of the mandatory wearing law on total driver fatalities, but instead can be used to estimate the effectiveness of the belts in crashes (Chapter 9).
4. Simple before versus after count. This has the advantage of transparency and simplicity. While estimates for one specific jurisdiction might have substantial errors, there is no reason to presume that the average value obtained for many jurisdictions would not tend towards an unbiased estimate of the true effect.
5. Count and examine crash victims admitted to hospital. This approach has been more successful at identifying changes in character and types of injuries when belt laws are passed than in evaluating overall field effectiveness.
The UK's mandatory belt-wearing law
Of the over 70 mandatory belt-wearing laws passed, the one that came into effect on 31 January 1983 in the UK has three factors favoring effective evaluation which are not available for any other jurisdiction. First, belt use was closely monitored before and after the law came into effect at 55 Department of Transport traffic census sites, generally from 8:30 a.m. to 4:30 p.m. Second, a large increase in belt use occurred quickly, from about 40% to 90% (Fig. 10-1). Third, the UK, with over 16 million cars in 1983, provides about the largest population of occupants affected by a single law. While France and West Germany have somewhat more cars, their laws did not lead to such sharp increases in belt use. In France, use was required on rural roads only in 1973, and on all roads in 1979. When belt wearing was made compulsory in West Germany in 1976, use rates rose only modestly, from 32% to 50%. In 1985 the instigation of more severe penalties led to an increase from 58% to 92%. While Japan has had a law since December 1971, with a increase in penalty for non-compliance in September 1985, eventually generating compliance of over 90%, I am not aware of any estimate of its effect on fatalities.
Despite uniquely favorable conditions, evaluating the UK's law has not been without difficulties or controversy, especially regarding possible driver behavior changes induced by the law [Adams 1985]. The simplest evaluation, a count of casualties in an 11-month period before the law to an 11-month period after the law [Mackay 1985] is shown in Fig. 10-6; January is excluded because of the rising belt use in the month of introduction. The somewhat higher reductions in serious injuries compared to fatalities (26% compared to 23%) is consistent with the discussion in Chapter 9 suggesting that when-used belt effectiveness is likely higher for levels of injury lower than fatality. Adams  argues that changes in other factors could have produced the declines, a view he supports by fitting a multivariate function to a time series for all UK fatalities without invoking any influence from the law. However, annual changes as large as 23% are simply not vulnerable to being explained away by other factors; only major inputs, like the energy changes after the Arab oil embargo, generate effects of such magnitude.
Fig. 10-6 about here
A somewhat more complex time-series analysis was applied to the UK data by Scott and Willis . They conclude that there was an approximately 20% reduction in fatal and serious casualties to car drivers and van occupants; for front-seat car passengers they find a larger 30% reduction. More recently, Broughton , in examining long term trends in total British fatalities per unit distance of travel, finds a 6.2% decrease (90% confidence limits from 1.9% to 10.3%) associated with law; as affected occupants were 37% of all road users, this result implies a 17% reduction.
Despite the relative agreement between the inference from the simple numbers and the Scott and Willis  time-series analysis, various questions continued to be raised, especially about possible effects on pedestrians and pedalcyclists. Accordingly, two distinguished statisticians without prior involvement with the Department of Transport, the body responsible for both implementing and evaluating the intervention, were invited to examine the monthly time series of casualties to various road users. Their paper, which is at the cutting edge of statistical theory, and accordingly understandable only to a few, was presented to the Royal Statistical Society [Harvey and Durbin 1986]. The discussion (printed after their paper) is uninhibited by the politeness that often does such disservice to the search for truth in North America.
For the large samples of those seriously injured (including fatally injured), Harvey and Durbin  find a reduction of 23% for car drivers and a 30% reduction for front-seat passengers, showing large reductions for those directly affected by the law. For those not affected, they find a 3% increase for rear-seat passengers, a 0.5% decrease for pedestrians and a 5% increase for pedal cyclists, all these values being not statistically significant. The uncertainties surrounding injury definitions (Chapter 1) are not likely to cause a major problem for a study of this type unless important changes in data-collection procedures coincide with the introduction of the wearing law.
For fatalities they find reductions of 18% for drivers and 25% for front-seat passengers. For those not directly affected by the law, they find increases of 27% for rear-seat passengers, 8% for pedestrians and 13% for cyclists. The value for rear-seat passengers is highly statistically significant and the other two values are on the borderline of significance. Harvey and Durbin  conclude that there was an increase in fatalities to those not directly affected, but write that they cannot explain its origin. They specifically state their reluctance to accept changes in driving behavior as an explanation because of, among other reasons, the inconsistency of the fatality and injury findings.
As a possible explanation for part of the increase in rear-seat fatalities, Jones  provides data suggesting possible migration of passengers unwilling to wear belts from front to rear seats, which were not covered by the legislation. I find this convincing for three reasons. First, I know with certainty of one specific case of its occurring. As it is hard to imagine anyone moving to the front seat because belt wearing was required in it, the direction, if not magnitude, of the effect is established. Second, interpreting the 27% increase as an identical increase in severe crash involvement by belted drivers in the face of an 18% reduction in driver deaths implies a when-used belt effectiveness that is unrealistically high. The third reason is the consistent finding of higher fatality reductions for passengers than drivers for essentially similar use rates, implying substantially higher when-used effectiveness for passengers, in contrast to a small difference in the opposite direction in Table 9-1; some of the reduction in front-passenger deaths may have occurred because of fewer front passengers.
The Harvey and Durbin  estimates of reductions of 18% for drivers and 25% for front passengers give a weighted average of 20% as the estimated reduction in fatalities to affected occupants. This is quite close to the simple fatality count calculation of 23% in Fig. 10-6. Substituting ui = 40% and uf = 90% into Eqn 10-8 generates an estimate of 26%, which is in reasonable agreement with the observed value.
The medical effects of the UK's law were determined by Rutherford et al.  by examining crashed-car occupants requiring hospital treatment. Patients arriving at 15 hospitals (eight in England, four in Northern Ireland, two in Scotland, and one in Wales) the year before and the year after the law were compared. The hospitals were chosen because of their high standards of data collection. The study finds a 15% reduction in patients brought to hospital, a 25% reduction in those requiring admission to wards, and a similar fall in bed-occupancy. Larger reductions are found for front-seat passengers than for drivers.
Are there cases in which the use of a safety belt increases injury?
I cannot conceive of any medical or other safety intervention which, in some cases, may not increase rather than decrease harm. Let us illustrate with an example from traffic. Every year a number of pedestrians walking on the sidewalk are killed by out of control vehicles. The existence of specific instances in which walking on the sidewalk led to death, while walking in the center of the fastest traffic lane would have been safer (well, certainly not less safe), while undoubtedly true, hardly has any bearing on whether one should walk on the sidewalk or the center of the fast lane. We choose the sidewalk not because it is always, under all circumstances, safer, but because it is, on average, safer. The same reasoning applies to all safety interventions, including use of safety belts.
Some types of injuries may increase with safety-belt use. Rutherford et al.  concluded that fractures of the sternum and sprained necks appeared to have increased. Salmi et al.  report increases in tharaco-lumbar spine injuries and serious cervical spine injuries following the French mandatory belt-wearing law. However, the decrease in injuries in general was much greater than these specific increases. Indeed, the injuries that increased in frequency might be substitutes for more serious injuries if no belt had been worn.
Casualty changes in other jurisdictions
Wagenaar, Maybee, and Sullivan  list 101 estimates of fatality reductions associated with introducing mandatory belt wearing in 27 jurisdictions, thus providing an average of over three estimates per jurisdiction. However, unlike the three estimates for the UK discussed above, these different estimates often vary widely. For example, for France from 21% to 50%; for New York State from 5% to 27%; for North Carolina from -7% (an increase of 7%) to 5%. Because the methods used to obtain some of the estimates (usually the high ones) are not technically defensible (six of them exceed the when-used effectiveness of 41%!) one cannot simply take the average as the best estimate. Accordingly, with present knowledge, there is no effective way to compare what actually happened in most jurisdictions with the values calculated using Eqn 10-6.
The main reason we do not have reliable estimates for fatality changes after wearing laws are introduced is because of the difficulty of measuring small effects in insufficiently large samples of data that are additionally changing for various other reasons. While estimates for individual US states are uncertain, a number of authors have estimated the effects for all states combined. The results obtained are: 7% by Partyka ; 7% by Campbell, Stewart, and Campbell ; 6% by Hoxie and Skinner ; and 9% by Wagenaar, Maybee, and Sullivan . These estimates use several of the techniques mentioned earlier. The relatively good agreement between the overall national estimates, even though estimates for different states varied by large amounts, shows the advantage of combining states. Collectively, the studies show no change in the risk to non-affected road users. Use rate typically changed from about 16% to 45% when laws were passed [Wagenaar, Maybee, and Sullivan 1988]. Substituting these values into Eqn 10-8 calculates a reduction of 9.7%, similar to, but higher than, the reductions estimated directly from data.
In addition to estimating reductions for individual US states, and for all states, Wagenaar, Maybee, and Sullivan  also estimated reductions for two groups of states, those using secondary and those using primary enforcement, by applying an interrupted time-series analysis which included the use of adjacent states for control of other sources of variability. They find a 6.8% reduction for secondary enforcement states and a 9.9% reduction for primary enforcement states. Assuming a use rate increase from 16% to 40% for the secondary and from 16% to 55% for the primary states gives calculated fatality reductions of 7.8% and 13.6%, respectively, values reasonably close to, but larger than, those observed.
Switzerland provides a particularly interesting case, because the law that became applicable in January 1976 was repealed because of voter petition in July 1977 and subsequent court action, leading to wearing being no longer required after October 1977 [Grimm 1988; Huguenin 1988]. However, a new law became effective on November 1980, providing a unique natural experiment in which the independent variable (the law) changed from off to on, from on to off, and from off to on again. The results in Fig. 10-7 show clear effects at every law change.
Fig. 10-7 about here
COMPARISON BETWEEN OBSERVED AND ESTIMATED FATALITY REDUCTIONS
The fatality reductions estimated quantitatively are compared to the values calculated using Eqn 10-8 in Table 10-2 (Let us use "observed" to refer to estimates from field data, even though such estimates involve analyses and assumptions). The first point to note is the extent of agreement; selective recruitment goes a long way to explain the actual changes in fatalities from changes in belt use, a point previously made [Evans 1988a] in comparing estimates for four US states [Williams and Lund 1988] with Eqn 10-8. Any additional factors, such as behavioral change, cannot be all that large, insofar as the observed effects are reasonably well explained without invoking them.
Table 10-2 about here
Beyond the relatively good agreement between the observed and estimated reductions, the next most striking feature of Table 10-2 is that all observed values, except one, are lower than estimated; for the exception, the values are identical. The most likely reason for this is that actual belt-use rates are systematically lower than those shown in Table 10-2, which are based on daytime observations. Mackay  indicates that observational data suggest lower rates when pubs are closing. The data in Evans [1987b] show that belt use in fatal crashes is consistently lower at night than in the day. For example, FARS 1975-1983 data show 5.59% of fatally-injured drivers in crashes from 6:00 a.m. to 6:00 p.m. coded as belt users. The corresponding rate for 6:00 p.m. to 6:00 a.m. is 3.41%. Thus, for these pre-law data, the nighttime driver is only 60% as likely as the daytime driver to be wearing the belt. Other data in Evans [1987b] show similarly large effects. If one assumes, as an approximation, that half the fatalities are at night, and that use rates at night are 60% what they are during the day, then all use rates in Table 10-2 should be set to 80% of their observed daytime values (this means that for the UK the change is from 32% to 72% instead of from 40% to 90%). After such a use rate adjustment, 12 of the 14 estimated fatality reductions become lower than observed. The pre-law results in Evans [1987b] may overestimate differences when use rates increase. If one instead assumes that nighttime wearing rates are 80% of daytime rates, so that all wearing rates should be 90% of the values in Table 10-2, then agreement between the observations and calculations is remarkably close. No deviation is as large as 2 percentage points, and most are substantially less.
Thus, modestly lower wearing rates during nighttime hours account for the systematic differences between the observed and estimated reductions. There is no need to invoke other explanations, such as crash rates increasing more steeply with unwillingness to use belts than in Eqn 10-8 (or Fig. 10-4), or changed user risk taking.
REPEAL OF MANDATORY MOTORCYCLE HELMET-WEARING LAWS
Following the Highway Safety Act of 1966, the US Federal Government made passage of mandatory helmet-wearing laws for motorcycle drivers and passengers a precondition for the states to receive highway-construction funds. All but three states passed such laws. In 1976, in response to pressures from many states, the US Congress revoked the financial penalties for non-enactment of helmet-wearing laws. In the next few years, just over half of the states repealed their laws; half repealing and half not provides the optimum "natural experiment" to compare repeal and non-repeal states.
The results of such a comparison are shown in Fig. 10-8, computed from the data in Chenier and Evans . The numbers along the horizontal axis give the states ordered by date of repeal, from 21 May 1976 for Rhode Island to 1 January 1982 for Louisiana. There are 27 data points for 26 states in Fig. 10-5; Louisiana appears twice as a result of repealing its law, passing another, and subsequently repealing this also. All the states may be identified from Table 2 of Chenier and Evans , which presents them in the order plotted. The fatality change for each state is estimated by dividing the ratio of the number of fatalities in a period after the law to the number in a period before the law by the corresponding ratio for all the fatalities in the non-repeal states. Thus each estimate, and its corresponding error, is computed from four fatality frequencies in a manner similar to in Eqns 7-2 and 7-4. A minor difference is that the log transformation (Eqns 6 and 7 of Evans [1988b]) is used, as is required for large errors, because, logically, changes cannot be less than -100%, but can have any positive value. The pre-law period is from 1 January 1975 (the beginning of FARS) to three months before repeal; the post-law period is from three months after repeal to 31 December 1982. As the laws were repealed at haphazard times, and the repeal states show no obvious geographic groupings, taking the average over all the jurisdictions should eliminate spurious effects and provide a reliable estimate for the fatality change associated with repeal.
Fig. 10-8 about here
Nominally, 24 of the points indicate fatalities increased after repeal, compared to 3 indicating a decrease, so the data provide extremely strong evidence that repeal led to a substantial increase in fatalities. The weighted average of all 27 values, indicated by the horizontal line in Fig 10-8, is (25 + 4)%. The error limits for 17 values (or 63% of the 27 values) cross this value. As the error limits are one standard error, 68% of them are expected to include the true value, thus perhaps indicating weekly that a few data may depart more from the average than would be expected by chance.
There have been a number of other estimates of the effect of repeal on fatalities. Watson, Zador, and Wilks  report a 40% increase using methodology criticized by Adams , who claims that the data can also support a value close to zero. De Wolf  reports an effect in the range of 4% to 10%, which might reasonably be interpreted as a point estimate of 7%. Fatality increases of 14% and 22% are reported by Graham and Lee  after controlling for changes in registrations; the two values reflect different calculation assumptions. A 24% increase is reported by Hartunian et al. .
Helmet use rates
An attempt to calculate increases in fatalities expected from repealing mandatory wearing requires estimating helmet-wearing rates in law and no-law states. Helmet use is observed as part of the 19 city survey sponsored by the National Highway Traffic Safety Administration. Over 18 000 observations in 1984 gave the following estimates:
Helmet wearing rates
Daytime city use in law states 99.7% 98.4%
Daytime city use in no-law states 51.3% 34.8%
Consulting FARS data indicates lower wearing rates in crashes; for example, in law states, one in three motorcyclists killed was unhelmeted. By using the 28% when-used effectiveness of the helmet (Chapter 9), one can estimate (as previously done by Partyka  and Evans [1987b] for safety belts) the number of helmeted motorcyclists involved in crashes of sufficient severity to kill unhelmeted motorcyclists, and thereby infer the wearing rates in crashes of the same severity. The results are:
Helmet wearing rates
Severe crash involvement in law states 76% 61%
Severe crash involvement in no-law states 32% 12%
The use rates inferred from the fatality data are in all cases substantially lower than those directly observed in cities in daylight, although there is qualitative correspondence between all differences. The use rates inferred from FARS do not represent use rates averaged over the times and places that fatal crashes occur, because, as in the case of safety belts, there is every reason to expect that the non-users have higher crash rates than the users. However, such effects cannot come close to explaining the magnitude of the discrepancy, especially given the near 100% observed helmet use in the law states. With present knowledge there is no satisfactory resolution of these differences. Let us therefore take the simple average of both estimates, thereby obtaining:
Helmet wearing rates
Best estimate for law states 88% 80%
Best estimate for no-law states 42% 23%
Comparison of estimated with observed increases
Although there is no quantitative information available for selective recruitment in motorcycle helmet wearing, we use Eqn 10-8 in the absence of anything more specific for helmets. Substituting the best estimates gives fatality increases of 18% for drivers and 19% for passengers, for a weighted average of 18% (compared to 17% and 21%, for a weighted average of 18% from the simple calculation, Eqn 10-6).
The estimated reduction is in reasonable agreement with, but somewhat less than, the (25 + 4)% value from Chenier and Evans . It is also in reasonable agreement with three of the other estimates discussed earlier which are 14%, 22% and 24% (the other three estimates, 40%, 7% and 0% appear to be outside the general pattern).
MANDATORY USE LAWS AND BEHAVIOR CHANGES
In many cases road users react to safety changes in ways that lead to safety changes quite different from those intended (Chapter 11). It is therefore not surprising that such an explanation arose when large promised reductions in casualties from belt laws were not apparent in data. Adams  claims that safety-belt laws induced increased driver risk taking that greatly diminished the safety benefits to those wearing the belts while increasing the risks to other road users. Adams  also claims that the repeal of motorcycle helmet-wearing laws induced increased caution, so that the repeal did not affect motorcyclist fatalities.
When one takes into account selective recruitment, and the clear evidence that observed daytime use rates are higher than those during the nighttime high crash-risk hours, then estimated fatality reductions from increases in belt wearing are in satisfactory agreement with those few observed values based on sufficiently large populations to be estimated reliably. While the comparison provides no evidence of a behavioral change in response to the introduction of mandatory belt wearing, the weak nominal indication is that an increase in caution is more likely than a decrease. While there are suggestions of increases in deaths, but not injuries, of pedestrians and pedalcyclists following the UK's mandatory wearing law, no such effects are found in other jurisdictions [Wagenaar, Maybee, and Sullivan 1988; Huguenin 1988].
The observed increase in motorcyclist fatalities after repeal of helmet-wearing laws is in agreement with increases estimated assuming realistic changes in helmet wearing rates. Again, the weak nominal indication is that repealing the laws is more likely to have increased than decreased recklessness. Another possibility is that repeal made motorcycling more appealing, thereby increasing the exposure to risk.
If compelling drivers to wear belts did indeed increase their risk taking, this ought to lead to observable consequences. Evans, Wasielewski, and von Buseck  examined driver risk taking, as indicated by close following, for belt wearers and non wearers in two jurisdictions. One was Michigan in 1978, with no belt law and a use rate observed in the study at 14%. The other was Ontario, Canada in 1980, with a mandatory wearing law and a use rate observed in the study of 51%, compared to a pre-law rate of 14%. Thus, 37% of the Ontario users were compelled users. In both jurisdictions, belt non-wearers were found to take higher driving risks. Making the assumption that behavior in Ontario before the law could be estimated by observed behavior in Michigan generated no evidence of any increase in risk taking in response to the law; indeed, the weak nominal indication was of a reduction in risk taking.
Lund and Zador  and O'Neill et al.  compared a number of driver behaviors in Newfoundland, Canada before and after that province acquired a mandatory law to the same behaviors in Nova Scotia, which did not have a law during the observation period. The behaviors examined were travel speeds, following headways, turning headways, and responses to yellow signals. None showed any indication of increased risk taking after the law. O'Neill et al. also report that drivers in England travelled significantly slower around sharp curves eight to nine months after the law than a year earlier, whereas other measures showed no evidence of change. They conclude that the evidence does not support any increase in driver risk taking.
Ideally, one would prefer to compare behavior in the same driver belted and unbelted than to look for differences between populations of belted and unbelted drivers. Streff and Geller  attempted to do this by having the same subjects drive a five-horsepower go-cart around an oval test track. Four groups of subjects drove in two phases, each consisting of 15 circuits of the track. One group drove phase one unbelted and phase two belted, another the opposite, while a third group drove all trials unbelted and a fourth all belted. The behavioral measure was the average time to drive around the track (the reciprocal of the speed, which was typically about 20 km/h). The paper includes a graph showing this measure for each of the group's 30 circuits, plus two initial warm-up circuits.
Streff and Geller's  plotted data show two dominant effects. First, a systematic learning effect (the time to complete the 30th lap is typically 10% less than the time to complete the first lap). Second, the group that changed from unbelted to belted contained a consistently slower group of drivers (with a shallower learning curve) than the other three groups. While the nominal indication from the graph is that those who switched from using belts to not using belts increased their speed more than those who did not change their belt-wearing status (that is, they are more cautious using the belts), the effect is small compared to the two dominant effects mentioned, and the authors conclude it is not statistically significant. However, they claim a statistically significant increase in speed (compared to the other groups) for those who changed from not wearing to wearing, an effect which seems to flow mainly from speed increases that occurred some number of trials after the subjects first fastened the belts, rather than as a result of the belts. Their claim of a statistically significant effect due to the belts seems to me as unconvincing as their claim of no statistically significant difference between the speed of this same group and the others, notwithstanding that this group was the slowest of the four in 32 trials out of 32. I think that the only important conclusion from these interesting data is that they exclude the possibility that switching from belt use to non use (or vice versa) changed the speed at which the go-cart was driven by more than about two percent in either direction. A more general question than whether the results support that belt wearing influenced go-cart speed is whether the results of such a laboratory test have realistic transferal to the overlearned task of normal driving.
Based on reason alone, it is essentially certain that users change behavior in some ways in response to an intervention as clearly visible as wearing a belt or helmet. The empirical evidence collectively establishes that any such reaction is of small magnitude, and of unknown sign. The evidence suggests very weakly that behavioral changes in the direction of driving more carefully after belt laws are introduced is more likely than one in the opposite direction.
While the evidence cannot determine the sign of the behavioral response, it can dismiss beyond reasonable doubt any suggestions that users react in such a way to as to negate, or almost negate, expected changes. There is no scenario of biases or changes that could plausibly suggest that the data in Fig. 10-8 are compatible with zero effect, or that the evidence on belt laws is so flawed that the effects are zero, or near zero. Following the point of Farber , if former belt non-wearers are to retain their fatality risk unchanged after becoming wearers, they would have to increase their severe crash involvement rate by 1/(1-E), where E is when-used belt effectiveness, assumed to be 42% (Chapter 9) ; that is, a 72% increase in crash rate would be required. Any increase approaching this would be observed readily, by, for example, insurance companies when jurisdictions experience large increases in belt use. An effect even 20% this size would long since have been observed reliably, and the consequent approximate 15% increase in insurance insurance premiums would have generated considerable public debate.
DIFFERENCES BETWEEN JURISDICTIONS
While over 80 mandatory belt-wearing laws are in effect, daytime use rates vary widely from over 90% in Australia, Finland, Japan, the UK and West Germany to under 40% in some US states. Many jurisdictions, including 16 US states, have no laws and wearing rates of 20% or less are not uncommon. These differences have invited all sorts of interesting explanations in terms of differing national characteristics. I have often heard (fortunately less frequently in recent years) citizens from nations with no laws or low use rates invoking national or cultural characteristics as explanations. Examples are that the citizens are too independent thinking and individualistic to allow the government to tell them what to do (the explanation favored by those inclined towards chauvinistic jingoism) or too lawless and stupid to know what is good for them (favored by those inclined "to praise every century but this and every country but his own. " [W.S. Gilbert, 1885])
Rather than being due to differences in national temperaments, it seems to me that the variations between jurisdictions flow from legislative decisions responding to pressures from specific institutions, or in many cases, just one or two individuals. Victoria, Australia, had the first important mandatory wearing law largely because a few individuals, mainly physicians, vigorously sought it. Because of the esteem of those advocating mandatory belt wearing, and the favorable media coverage, wearing rates were high. After passage, there was widespread agreement of substantial reductions in casualties (some estimates now seem to have been clearly too high). With such positive experience it is not surprising that other Australian states soon passed similar laws.
I see no indications that the US has any greater or lesser intrinsic tendency to mandatory laws than Australia, or anywhere else. The first child restraint law in the US came into effect in Tennessee in January 1978 at a time when there were only a few comparable laws in effect in the world. The driving force was two Tennessee pediatricians. By June 1985, child restraint laws were in force throughout the entire US, whereas many of the countries which had passed adult belt-wearing legislation had no laws covering children and infants. No prediction based on stereotypical views of the role of government or political attitudes in different US states would have identified Tennessee as the most likely state to have the nation's first car-occupant restraint law. A similar comment applies to mandatory safety belt laws. In 1985 the US state with the highest belt-wearing rate was Texas; Massachusetts does not have a mandatory wearing law.
Wearing rates seem largely determined by the way laws are introduced and media coverage, in addition to enforcement policies. Ireland required mandatory wearing in February 1979, yet wearing rates remained below 50% [Hearne 1981]. However, in adjacent Northern Ireland, rates reached the same high levels of over 90% observed in the rest of the UK after the mandatory wearing law came into effect in January 1983 [Rutherford et al 1985, Table 18]. The high UK rates seem more related to positive media coverage and public acceptance than to enforcement, which is modest and non-obtrusive. A publicity campaign in Elmira, New York raised wearing rates from 49% to 77% [Williams et al. 1987]; there are other examples of public information increasing compliance with traffic laws [Shinar and McKnight 1985].
Campbell and Campbell [1988 p. 24-25] explain why mandatory belt-wearing was introduced into the US so much later than in other countries as follows:
One reason for the delay in passing seat belt legislation in the United States may have been a lack of early advocacy on the part of traffic safety leadership groups. In the absence of vigorous support by leadership groups, there was little movement toward seat belt laws during the 1960s and 70s. Illustrative is the fact that in the late 1960's, the newly created National Highway Safety Bureau (NHSB) of the US Department of Transportation (DOT) promulgated 17 different state standards touching almost every area of highway safety, none of which had anything to do with seat belt use. It was not until 1984 that, for the first time, DOT publicly endorsed seat belt laws.
According to Campbell and Campbell [1986; 1988], a factor that almost certainly delayed consideration of wearing laws was the debate centered on choosing between automatic passive restraint systems, such as airbags, and belt laws. This point is also made by Trinca [1984, p. 4], representing the Royal Australasian College of Surgeons, which played a pivotal role in Victoria making belt wearing mandatory, who writes (before the US had any mandatory laws):
The arguments for passive restraint, for air bags as an alternative to seat belts, for exemption against seat belt wearing produce a smoke screen that has successfully delayed in many countries and in the U.S.A. actually prevented, the introduction of mandatory seat restraint laws.
Eventually all cars in the US were required to to be equipped with passive devices for the driver and right-front-passenger seats. Graham  gives a fascinating account of the over two decades of squabbling that culminated in
this decision. In reviewing Graham's  book, Campbell  writes
Another irony: the sight of people long associated with highway safety and the need for occupant restraint standing in opposition to seat belt laws. I am still dumbfounded that both [former NHTSA Administrators] Claybrook and Haddon presented barriers to belt laws.
Almost totally absent from the airbag versus safety belt debate [Graham 1989] was any focus on the relative effectiveness of these different approaches to occupant protection. It seems that the technical question of which approach would save more lives was not an important ingredient of the debate, because, many of the key participants had neither the interest nor the competence to address it. Yet one early well-designed study [Wilson and Savage 1973] showed the fatality-reducing effectiveness of airbags to be about half that of lap/shoulder belts (Table 9-7), devices then already being fitted to all new cars. It is therefore not surprising that airbags are now offered not as complete restraint systems, but as supplements to the primary restraint system, the lap/shoulder belt. There is even a product liability case pending in New York in which an automobile manufacturer is being sued in the death of an unbelted occupant, the claim being that the installed airbag discouraged the deceased from wearing the belt that it is claimed would have prevented her death. In many more cases manufacturers are sued for non-installation of airbags, and it is entirely within the rules of the game for the same manufacturer to lose one case of each type on the same day. The degree to which product-liability litigation in the US bears no resemblance to that anywhere else in the world is effectively documented by Babcock , who compares how the same injury in the same crash would be handled in a number of US states, compared to in eight other Western democracies.
The different handling of occupant protection legislation in the US compared to in all other countries also is probably related to the uniquely powerful role of the legal industry in the US, and its dominance over technical and other considerations. As Lamm  points out, the US has 5% of the world's population, but almost 70% of its lawyers (there are 700 000 lawyers in the US); the US has 25 times as many lawyers per capita as Japan. Even just one portion of the burden the legal industry imposes on US society, what Huber  calls the "tort liability tax", he estimates costs the nation $300 billion per year -- more than the cost of defense, and four times the total cost of traffic crashes (Chapter 1). Comparing the US with other nations, none of which does anything remotely comparable, shows no discernible benefit from such staggering expenditures. Essentially everything that happens in the US leads to wealth on a grand scale being transferred to the legal industry. The situation does not seem susceptible to remedial measures because the benefactors define and administer the rules.
If the energies and resources of the airbags versus belts debate had been focused on passing mandatory belt-wearing laws, and on increasing use rates, there can be no doubt that large numbers of lives would have been saved. Partyka  estimates that in 1984, 1985, 1986, 1987, and 1988 US belt-wearing laws prevented 239, 850, 2016, 2551, and 2956 occupant deaths, respectively (assuming a 40% effectiveness, her lower-bound estimate). The increasing numbers reflect the increasing numbers of states with laws, and increasing use rates in these states as well as increases induced in the no-law states by increases in the law states. If, rather than starting in 1984, this sequence had started in 1978 (Canada's two most populous provinces, Ontario and Quebec, had compulsory wearing since 1976), then by 1984 over 8000 lives would already have been saved. This is of course based on the relatively low US wearing rates. The US having national wearing rates comparable to those in Australia or the UK, rather than pre-law rates, would save 8300 deaths per year. Whatever plausible scenario one considers leads to the inescapable conclusion that the delay in introducing mandatory wearing laws in the US compared to most other nations, and the uncertainty raised regarding their value, has led to the deaths of tens of thousands of occupants. It seems improbable that such losses will be balanced by future reductions from the passive approach adopted after so much debate, effort and litigation [Graham 1989] by the US, an approach that has found no adherents in any other nation in the world.
Over 80 jurisdictions have laws compelling drivers and some passengers to wear safety belts. Wearing rates vary widely, from over 90% in Australia, the UK, and West Germany to under 40% in some jurisdictions. Among the factors influencing wearing rates is publicity and level of enforcement. The highest precision evaluation is for the UK's law, where belt use rose rapidly from 40% to 90% in a large population of affected occupants. The law reduced fatalities to drivers and front-seat passengers by 20%. For smaller use rate increases, and for smaller populations (that is, in nearly all other cases), it is not possible to directly measure fatality changes. They can be reliably estimated using an equation based on the known when-used effectiveness of the belts together with a quantification of "selective recruitment" effects -- the tendency of those changing from non-use to use to be safer than average drivers. The equation fits well the few data points that are reliably known. The repeal of mandatory helmet-wearing laws in the US increased motorcyclist fatalities by about 25%. If realistic assumptions are made about nighttime use rates for belts and helmets, the agreement between predicted and observed changes is sufficiently close to preclude any possibility that mandatory use laws induce substantial changes in driver behavior; the weak nominal indication is that such laws more likely decrease than increase driver risk taking.
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Harvey, A.C.; Durbin, J. The effects of seat belt legislation on British road casualties: a case study in structural time series modeling. Journal of the Royal Statistical Society A149:187-227; 1986.
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Huguenin, R.D. Personal communication; 1990.
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Jones, D.H. Comment on the paper by Harvey and Durbin. Journal of the Royal Statistical Society A149:219-219; 1986.
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Table 10-1. Estimates of the involvement rate of unbelted drivers to the rate for belted drivers in various traffic incidents.
TYPE OF EVENT ─────────────
Driver fatalities 1.57
Crashes in which pedestrians were killed 1.57
Crashes in which motorcyclists were killed 1.37
Police reported crashes (headway study) 1.32
Police reported crashes (speed study) 1.28
Traffic violations (headway study) 1.86
Traffic violations (speed study) 1.73
Table 10-2. Comparisons of fatality reductions estimated using field data to the reductions calculated using Eqn 10-8.
Belt-use Fatality reductions
Study Population ───────────────────
change From data Eqn 10-8
Wagenaar, US states 16% to 45% 8.7% 9.7%
Maybee, and US states (secondary) 16% to 40% 6.8% 7.8%
Sullivan  US states (primary) 16% to 55% 9.9% 13.6%
UK 40% to 90% 20% 25.8%
1983 - all US states 0%*to 14.0% 2.7% 3.9%
1984 - no-law states 0% to 14.4% 3.7% 4.1%
1985 - no-law states 0% to 19.8% 5.4% 5.6%
1986 - no-law states 0% to 23.3% 6.7% 6.7%
Partyka and 1987 - no-law states 0% to 29.7% 7.8% 8.6%
Womble  1988 - no-law states 0% to 34.0% 9.4% 10.0%
1985 - law states 0% to 40.9% 11.4% 12.3%
1986 - law states 0% to 47.1% 13.1% 14.5%
1987 - law states 0% to 49.8% 13.8% 15.5%
1988 - law states 0% to 50.0% 13.8% 15.6%
* Fatalities at observed belt-use rate compared to estimate for zero belt use