Discrediting defense experts in whiplash cases: to support a pre-trial motion to exclude defense expert testimony in these cases, the lawyer must expose the faulty methodologies in the biomedical and engineering literature.

A frequently disputed condition in the medical literature is the constellation of symptoms comprising acute whiplash and its chronic iteration, late whiplash (which is collectively known as whiplash syndrome). The primary reason for the dispute is that the validity of the syndrome is often a key issue in litigation involving motor vehicle crashes in which the injured party is not at fault.

The judge or jury in these cases is asked to weigh opposing medical and scientific evidence supporting the plaintiff's position that whiplash injuries are real and the defense position that the injuries are greatly exaggerated--or perhaps even that they are nonexistent. More than $29 billion a year is spent on whiplash injuries and litigation in the United States alone. (1)

It is not surprising, considering the financial stakes, that many experts have dedicated their careers to one side or the other of the controversy. These experts are increasingly relying on biomedical and engineering literature to support their views.

Defense accident reconstructionists and biomechanical engineers are using the literature in a particularly egregious way. They use studies to validate their claim that a given crash cannot result in injury. This ploy is being used increasingly in low-speed rear-end impact collision (LOSRIC) cases, which plaintiff attorneys often refer to as minor-impact soft-tissue (MIST) cases. In the authors' opinion, defense use of these studies is contributing greatly to the increase in low-or zero-award verdicts in cases where there is legitimate injury.

Despite strong epidemiologic evidence supporting LOSRIC as the cause of whiplash syndrome, numerous papers have been published in peer-reviewed journals, most since 1990, attempting to show that LOSRIC is an unlikely cause of acute or chronic symptoms. This article discusses the literature most often used by defense experts, categorized by defense claims that the papers are purported to support. In addition, the scientific flaws inherent in the papers are discussed.

Defense claim one

This argument says that studies have documented a relationship between speed and injury potential. The implication: Low-speed collisions causing little or no vehicle damage cannot cause occupant injury. The defense uses the following studies to support this claim.

McConnell and others reported the results of human volunteer rear-impact crash testing of four subjects in 1993. They determined that in whiplash injuries resulting from rear-impact collisions, the threshold of a "very mild, single event musculoskeletal cervical strain injury" is a delta V (the velocity change of the struck vehicle, as opposed to the speed of the striking vehicle at impact) of 4 to 5 miles per hour (mph). (2)

In 1995, McConnell and others, in a separate study, examined the movements and acceleration forces sustained by seven volunteers subjected to repeated rear-end collisions with delta Vs of up to 6.8 mph. They concluded that at a delta V of 5 mph, the likelihood of neck and shoulder strain may increase for the average occupant. They also concluded that any injury to the lower back is "quite unlikely as a result of a low velocity rear-end collision." (3)

West and others studied the acceleration forces sustained by six volunteers in crash testing of five different vehicles. They concluded that occupants are unlikely to be injured in collisions with an equivalent barrier speed (EBS) of less than 8 mph. (4) EBS refers to the speed at which a vehicle will sustain a specific amount of damage when colliding with a fixed barrier.

Szabo and others reported on crash testing of five volunteer subjects in vehicles that were struck in the rear at approximately 10 mph by another vehicle, resulting in an average delta V of 5 mph. The subjects were evaluated by an orthopedic surgeon and given a magnetic resonance imaging (MRI) scan before and after the crash testing.

Although four of five complained of headache directly after the crashes, none had symptoms that lingered for more than two days, and no subjects reported further symptoms the following year. The authors concluded that rear-end collisions with a delta V of 5 mph or less were within human tolerance levels and that injury was unlikely after such a collision. (5)

These papers contain the following methodological errors:

* Inadequate study size. When attempting to study a population sample, in order to make an inference that applies to a population beyond that of the study, it is essential to use inferential statistics to determine if the study results were truly a result of the variables under study or if they were due to random variation. With crash testing, the dependent variable (the variable under study) is injury status. An occupant is either injured or not injured. A confidence interval can be established that indicates the potential effect of random variation on the study results--in other words, how much of the results was due to chance.

If the study were to be repeated, the confidence interval tells us how many and how few injuries are possible in future studies, based on the results of the current study. The width of a confidence interval is indirectly related to the number of subjects in a study, because random error makes the interpretation of the study results less precise. The wider the confidence interval, the more likely the study results are due to chance.

For example, consider a typical coin toss. If a coin is tossed three times (resulting in a wide confidence interval) and heads is observed all three times, it is much less precise to state that the coin has heads on both sides, compared with 100 coin tosses (with a narrower confidence interval) resulting in heads.

Even performing crash testing using as many as 20 subjects who sustain no injury in the test, the probability of injury in a larger population is still 0.15 percent (based on the confidence interval). This means that three subjects could be injured the next time the same study is conducted with the same subjects, and those results would still be consistent with the results of the current study.

Thus, the confidence interval for crash test studies of five or six subjects is too wide to conclude that no injury is possible under similar conditions. To adequately describe the range of injury responses for the general population--given the wide variety of human susceptibility to injury, vehicle types, crash conditions, and so forth--many hundreds or even thousands of subjects would need to be studied in crash tests.

* Nonrepresentative study sample. The subjects in the crash test studies consisted of the authors of the studies, employees of the corporations financing the studies, and other associates of the authors who may have had a vested interest in their outcome. In addition, almost all the test subjects were male.

To generalize the results of any study to a larger population--in this case, the general population at risk for whiplash injuries--the study population must represent the larger population. Not only did the authors of each of the four papers listed above not pick a representative sample, they literally "stacked" the study with themselves and their colleagues. So, if there was injury among the study subjects, they were less likely to report it, since it was contrary to the study's hypothesis.

* Nonrepresentative crash conditions. Even if the number of subjects were sufficient to generalize the results to the general population, the results would only be applicable to perfectly healthy males who were prepared for a rear impact and ideally situated in the vehicle seat at the time of impact. Only a very small proportion of the crash-injured population fits this narrow description.

Defense claim two

This claim argues that specific actions or movements common to daily living or sports and recreational activities do not cause injury, yet involve forces similar to or higher than those produced in whiplash movements. The implication: Whiplash forces should not cause injury because they are comparable to other movements that do not cause injury.

Allen and others studied the acceleration forces of common movements in eight volunteers with accelerometers (devices to measure acceleration) affixed to a helmet. The authors reported that peak accelerative forces measured while subjects "plopped down into a chair" were similar to accelerative forces recorded during published accounts of volunteer crash testing. The authors concluded that the acceleration of noninjury "perturbations" was comparable to the "jostling expected in low velocity 'whiplash'-type motor vehicle accidents," neither of which is likely to result in injury. (6)

The paper contains the following methodological errors:

* Unsupported conclusions. The authors concluded that whiplash trauma and ordinary daily movements were comparable, even though none of the movements studied duplicated the direction, or vector, of force of whiplash trauma. Most of the acceleration in a rear-impact crash is in the x vector--that is, front to back. The largest single acceleration reported by Allen was 10.1 g in a diagonal vector (54.9 degrees from horizontal) during "plopping down into a chair." (One g is the accelerative force of the Earth's gravity, 32.2 feet per second squared.) The x vector component was 5.6 g.

However, the average x vector acceleration of plopping in a chair was only 3.3 g, the highest average x vector acceleration of all the movements studied. Allen reported that 10 of the 13 movements studied had average x vector accelerations of less than 2 g.

In comparison, another study reported a range of peak acceleration at the head during crash testing of six volunteers of 6 to 14.5 g at 5.6 mph equivalent barrier speed. (7) The largest published crash test study to date reported 6.7 to 12 g of peak head acceleration among 39 subjects crash tested at 5 mph delta V. (8)

Additionally, the duration of peak acceleration of the movements studied by Allen--about 1 millisecond--is not comparable to the duration of peak acceleration measured during whiplash trauma--70 milliseconds. (9) Taking into account both factors of acceleration--magnitude and duration--whiplash trauma produces more than 150 times greater accelerative force than plopping in a chair.

* Misleading illustration. In an illustration of the acceleration forces measured while plopping in a chair, the authors of Alien's study showed a human head apparently moving into extension, with an arrow traveling rearward through the head and "10.1 G" labeled at the arrowhead. However, the legend of the figure parenthetically states that "the apparent axis of rotation of the head in this schematic is not the true motion of the head. It is an expression of the acceleration forces."

In spite of the disclaimer in the legend, it seems clear that the authors are attempting to mislead the reader into believing that plopping in a chair produces the same vector and magnitude of acceleration, as well as movement of the head, as a rear-end collision.

* Inappropriate study design. Other than to purposely trivialize whiplash injuries, there is no scientific reason to compare common movements that do not usually cause injury to whiplash trauma, which results in 2.9 million injuries in the United States annually. (10) By its design, Allen's study could not yield any information about whiplash injuries, since neither these injuries nor the mechanism of these injuries was studied.

Defense claim three

This argument asserts that acute whiplash injuries do not cause or are unlikely to cause chronic pain. The implication: Those claiming chronic pain following whiplash are malingering. The defense commonly uses two studies to support this claim.

The Quebec Task Force (QTF) conducted a retrospective insurance data study and a literature search and issued a set of guidelines and recommendations based on the results. (11) Among other things, the QTF concluded that whiplash injuries were "short-lived," that they involved "temporary discomfort," that the pain was "not harmful," and that the injuries have a "favorable prognosis." The authors also concluded that 87 percent and 97 percent of their cohort "recovered" from their injuries at 6 months and 12 months after the collision, respectively.

The study contains the following methodological errors: (12)

* Nonrepresentative sample. With the QTF whiplash-associated disorder (WAD) insurance data study, the task force set out to estimate the incidence of "compensated whiplash injury" in Quebec and classify recipients of compensation by age, gender, and geographical region. The study subjects were identified from an insurance database of people with cervical sprains and strains and included only those who had received disability compensation for their injuries in 1987 in Quebec. No information was gathered about treatment rendered, symptoms, or the extent of functional impairment of those receiving compensation.

Additionally, people who had any diagnosis in addition to neck strain, such as lumbar strain, were eliminated from the analysis of injury recurrence. The resulting subpopulation that was ultimately studied made up only 35 percent of an already biased subpopulation of whiplash-injured individuals. As a result of the selection criteria for study, the QTF could not generalize its results to the majority of the population at risk for whiplash injury.

* Improper use of terminology. The results and discussion section of the study contained numerous references to the percentage of the study population "recovered" at the time compensation ended. However, the QTF did not gather data regarding the symptoms, amount or type of treatment, or functional impairment of the subjects in the study group--all factors necessary to determine the level of recovery after an injury.

The QTF chose to define "recovery" unconventionally as cessation of compensation. Not surprisingly, the task force found that 87 percent and 97 percent of its subjects were "recovered" at 6 and 12 months after the collision, respectively. To refer to these individuals as recovered misrepresented the data collected.

* Unsupported conclusions. In a table labeled "Prevalence of symptoms at follow-up," the task force enumerated the four studies on prognosis that were accepted for review, along with their findings. These were as follows:

According to QTF, Norris and Watt reported in 1983 that 66 percent of their cohort had neck pain an average of two years after injury. (The QTF reported Norris' and Wart's findings erroneously. Norris and Watt actually reported neck pain at follow-up in 44 percent, 81 percent, and 90 percent of the three groups they studied.) (13)

In 1991, Radanov reported that 27 percent of the cohort were symptomatic six months after the collision. (14) In a study two years later, Radanov reported that 27 percent of the cohort had headaches six months after the collision. (15)

In 1990, Hildingsson and Toolanen reported 43 percent of their cohort symptomatic of more than minor discomfort at an average of two years after injury. (16)

Despite these findings, the QTF concluded that:

"Patients should be reassured that most WAD [whiplash-associated disorders] are benign and self-limiting";

"All interventions ... should be accompanied by reassurance about the favorable prognosis";

"The key message to the WAD patient is that the pain is not harmful [and] is usually short-lived"; and

"[M]ost incidents of WAD are self-limited, involving temporary discomfort and rarely resulting in permanent harm."

These conclusions misrepresent the literature the task force reviewed.

Schrader and others--the second study used to support the claim that whiplash injuries do not cause chronic pain--studied 202 people in Lithuania who had been involved in motor vehicle collisions. The exposed group was matched by age and gender with a control group of 202 people, also in Lithuania, who had no history of a motor vehicle collision. The two groups were surveyed an average of 21.7 months after the crash and were found to have the same prevalence of neck pain.

The authors concluded that whiplash injuries do not cause chronic symptoms and that the reason that late whiplash exists in industrialized countries is because insurance settlements are available to those claiming chronic pain. (17)

This study's methodological error involves inadequate sample size. The study was criticized because only a very small proportion of the exposed cohort--15 percent--had been injured initially and thus exposed to the cause of late whiplash. (18)

We performed a sample-size calculation on the data in this study. Our statistical analysis showed that 94 percent of the acutely injured subjects in this study would have had to develop chronic symptoms to enable the authors to detect a statistically significant difference between the two groups, an extremely remote possibility (particularly in light of the fact that only 4.5 percent of the exposed cohort had symptoms for more than one week).

Our recalculations showed that the total study cohort needed to be at least 3,000 in order to have sufficient statistical power to discern a significant difference between the two groups. (20) Therefore, the authors' statements regarding chronic pain after whiplash are not based on valid research results.

Defense claim four

This claim contends that it is impossible or nearly impossible to injure the temporomandibular joint (TMJ) in a whiplash-type injury. The implication: Claims for TMJ injury after whiplash trauma are not believable. Three studies purportedly support this conclusion.

Howard and others, in describing their theoretical biomechanical model of TMJ forces during whiplash trauma, (21) stated in 1991 that "head accelerations produced by forces in the neck (extension-flexion motion) ... will generate forces in the temporomandibular joints that ... are of substantially lower magnitude than a force encountered routinely in normal mastication." The authors also said that the normal motion of chewing produced "greater potential to produce traumatic injury" than whiplash trauma.

The methodological error in this study involves inappropriate study design. The authors theorized that extension of the head with the mouth closed would not cause TMJ injury. While this may be true, the most widely accepted and researched model of TMJ injury during whiplash centers on the jaw opening during cervical extension, a motion that leaves the joint much more susceptible to injury than when the jaw is closed. (22)

The comparison that Howard made between the forces acting on the TMJ during whiplash trauma and the normal forces of chewing was fundamentally unsound. The closed position of the joint at the point of maximum force during chewing and the upward direction of the force cannot be meaningfully compared with the open position of the joint and the backward direction of force during whiplash trauma.

Howard and others, in a separate study, looked at the acceleration forces at the TMJ that occurred during rear-impact crash testing of four volunteers. (23) The authors used accelerometers fitted to a bite plate to measure these forces at the approximate level of the TMJ during 5 mph impacts. They concluded that the forces measured at the jaw during crash testing constitute a "small fraction" of the normal forces experienced during chewing and that low-speed whiplash trauma cannot cause TMJ injury.

This study contains four methodological errors:

* Inappropriate study design. The authors used a bite plate to measure forces at the TMJ. This required firm closure of the mouth on the plate during crash testing. Since jaw opening is integral to the mechanism of injury at the TMJ during whiplash, (24) having the subjects keep their jaws firmly elevated during the testing defeated the purpose of the study. The results are meaningless with regard to the actual forces that are sustained at the TMJ during whiplash trauma.

* Nonrepresentative sample. The subjects in this study were not randomly selected from the general population at risk for whiplash injury.

* Inadequate study size. The study was too small to assume that injuries would not occur if the crash test were performed on more subjects.

* Unsupported conclusions. The authors concluded that the harmless forces of chewing were far greater than the forces of whiplash trauma. However, they did not study acceleration forces specifically at the TMJ. They cannot compare the forces measured in their study to those of chewing, since the cranium and the jaw, the two bony components of the joint, accelerate at different rates during chewing. Because the jaw was closed in this study, it was accelerated at the same rate as the cranium, and no differential movement for the two parts of the joint was allowed. We found no support for the authors' conclusions regarding TMJ injury potential in the methods or results of this study.

Heise and others, the third study on TMJ injuries, reported on 155 patients presenting to an emergency room following a whiplash trauma. The patients were divided into two groups: 63 patients with unspecified radiographic evidence of cervical musculoskeletal injury and 92 patients without this evidence. The two groups were examined and interviewed for TMJ symptoms at the time of initial presentation, then followed up by phone interview one month and one year later. (25)

The follow-up rate at one year was 70 percent of the group with positive radiographic findings and 65 percent of the group with negative findings. None of the patients contacted at one year had continued symptoms of TMJ dysfunction. The authors concluded that the incidence of TMJ injury after whiplash trauma was "low."

Two methodological errors flaw this study:

* Inappropriate study design. The authors do not state their rationale for stratifying their cohort into two groups on the basis of unspecified "positive radiographic findings" of whiplash. We were unable to find any reference in the literature to a correlation between TMJ injury and radiographic findings of whiplash injury that would justify the study design employed here.

* Inadequate sample size. Using a literature-based estimate that 4 percent of the whiplash-injured population will sustain a TMJ injury, (26) we performed a sample-size calculation on Heise's data. Assuming double the frequency of TMJ injury in the exposed group, the authors would have needed more than 2,500 subjects for their study. Assuming a highly unlikely eight times greater frequency of TMJ injury between the two groups studied, the authors still would have needed more than 650 subjects, four times greater than the number in the study.

Defense myths

The methodology used by researchers attempting to refute the validity of whiplash syndrome is generally flawed. More specifically, we have concluded that there is no epidemiologic or scientific basis for the following statements, which are often made by defendants:

* Acute whiplash injuries do not lead to chronic pain.

* These injuries are unlikely to result in chronic pain in countries in which there is no compensation for injury.

* Rear-impact collisions that do not result in vehicle damage are unlikely to cause injury.

* Whiplash trauma is biomechanically comparable to common movements of daily living.

* There is insufficient force generated at the TMJ during whiplash trauma to cause injury.

* TMJ injuries are not associated with whiplash trauma.

As the body of literature increases, studies with findings that support one side or the other of the legal debate over the validity of whiplash syndrome are increasingly likely to be used in litigation.

We hope this article will assist plaintiff lawyers in identifying when scientific literature is used in an unscientific manner in these cases.

Notes

(1.) Michael D. Freeman, A Study of Chronic Neck Pain Following Whiplash Injury (UMI Dissertation Services, Ann Arbor, 1998).

(2.) WARD E. MCCONNELL ET AL., SOCIETY OF AUTOMOTIVE ENGINEERS, SAE 930889, ANALYSIS OF HUMAN TEST SUBJECT KINEMATIC RESPONSES TO LOW VELOCITY REAR-END IMPACTS 21-31 (1993).

(3.) Ward E. McConnell et al., SAE 952724, Human Head and Neck Kinematic After Low Velocity Rear-End Impacts: Understanding Whiplash, 39TH STAPP CAR CRASH CONE PROC., SOCIETY OF AUTOMOTIVE ENGINEERS 215-38 (1995).

(4.) D.H. West et al., Low Speed Collision Testing Using Human Subjects, 5 ACCIDENT RECONSTRUCTION 1.22 (1993).

(5.) THOMAS J. SZABO ET AL., SOCIETY OF AUTOMOTIVE ENGINEERS, SAE 940532, HUMAN OCCUPANT KINEMATIC RESPONSE TO LOW SPEED REAR- END IMPACTS 23-35 (1994).

(6.) Murray E. Allen et al., Acceleration Perturbations of Daily Living." A Comparison to "Whiplash," 19 SPINE 1285 (1994).

(7.) West et al., supra note 4.

(8.) GUNTER P. SIEGMUND ET AL., SOCIETY OF AUTOMOTIVE ENGINEERS, SAE 973341, HEAD/ NECK KINEMATIC RESPONSE OF HUMAN SUBJECTS IN LOW-SPEED REAR-END COLLISIONS 357-85 (1997).

(9.) Id.

(10.) Freeman, supra note 1.

(11.) Walter O. Spitzer et al., Scientific Monograph of the Quebec Task Force on Whiplash-Associated Disorders: Redefining "Whiplash "and Its Management, 20 (Supp.) SPINE 18 (1995).

(12.) See generally Michael D. Freeman & Arthur C. Croft, The Controversy over Late Whiplash: Are Chronic Symptoms After Whiplash Real? in WHIPLASH INJURIES 161, 163-64 (Robert Gunburg & Mark Szpalski eds., 1998).

(13.) S.H. Norris & I. Watt, The Prognosis of Neck Injuries Resulting from Rear-End Vehicle Collisions, 65 J. BONE & JOINT SURGERY (BRIT.) 608 (1983).

(14.) Bogdan P. Radanov et al., Role of Psychosocial Stress in Recovery from Common Whiplash, 338 LANCET 712 (1991).

(15.) Bogdan P. Radanov et al., Factors Influencing Recovery from Headache After Common Whiplash, 307 BRIT. MED. J. 652 (1993).

(16.) Chirster Hildingsson & Goran Toolanen, Outcome After Soft-Tissue Injury of the Cervical Spine: A Prospective Study of 93 Car-Accident Victims, 61 ACTA ORTHOPAEDICA SCANDINAVICA 357 (1990).

(17.) Harald Schrader et al., Natural Evolution of Late Whiplash Syndrome Outside the Medicolegal Context, 347 LANCET 1207 (1996).

(18.) Michael D. Freeman &Arthur C. Croft, Late Whiplash Syndrome (3d reply), 348 LANCET 125 (1996).

(19.) Freeman, supra note 1.

(20.) Michael D. Freeman, The Epidemiology of Late Whiplash, LYONS-DAVIDSON INT'L WHIPLASH CONE (Sept. 3, 1997).

(21.) Richard P. Howard et al., Assessing Neck Extension-Flexion as a Basis for Temporomandibular Joint Dysfunction, 49 J. ORAL & MAXILLOFACIAL SURGERY 1210, 1213 (1991).

(22.) K. Schneider et al., Modeling of Jaw-Head-Neck Dynamics During Whiplash, 68 J. DENTAL RES. 1360 (1989).

(23.) Richard P. Howard et al., Temporomandibular Joint Injury Potential Imposed by the Low-Velocity Extension-Flexion Maneuver, 53 J. ORAL & MAXILLOFACIAL SURGERY 256 (1995).

(24.) Schneider et al., supra note 22.

(25.) Andrew P. Heise et al., Incidence of Temporomandibular Joint Symptoms Following Whiplash Injury, 50 J. ORAL & MAXILLOFACIAL SURGERY 825 (1992).

(26.) INSURANCE RESEARCH COUNCIL, PAYING FOR AUTO INJURIES: A CONSUMER PANEL SURVEY OF AUTO ACCIDENT VICTIMS (1994).

Michael D. Freeman is a trauma epidemiologist and a clinical assistant professor in the Department of Public Health and Preventive Medicine at Oregon Health Sciences University School of Medicine in Portland. Arthur C. Croft is director of the Spine Research Institute of San Diego. Mark Reiser is a professor in the Department of Economics at Arizona State University in Tempe, Arizona. For a longer version of this article, see "A Review and Methodologic Critique of the Literature Refuting Whiplash Syndrome, "24 Spine 86 (1999).