Don't know much about epidemiology? Gain a strategic advantage in pharmaceutical litigation by boning up on epidemiology. Here's what you need to know to understand the strengths and shortcomings of research studies.

Epidemiology plays an important but complicated role in pharmaceutical and toxic tort litigation. Courts and scientists place greater value on epidemiologic evidence than on animal studies or human case reports and view epidemiological studies as the preferred evidence for determining the cause of disease in humans.

Epidemiology applies the scientific method to the study and comparison of groups of people, using the principles of medicine, public health, and biostatistics. Simply put, epidemiology can illuminate whether drugs cause, or are associated with, injuries.

For instance, some diseases, such as mesothelioma, occur only with exposure to a harmful agent (in that case, asbestos). More often, however, the disease or injury is not uniquely linked to the exposure. People not exposed to cigarettes still can get lung cancer, and not all cigarette smokers get lung cancer--yet we know that lung cancer is caused by cigarette smoking from multiple lines of evidence (animal studies, human case reports, experimental studies, toxicology data). Epidemiologic studies constitute the best evidence, providing a valid statistical association between exposure to cigarettes and lung cancer.

In pretrial Daubert proceedings, epidemiological studies often come under intense scrutiny, and if the results are negative (that is, not finding a valid association between exposure to the agent under study and an increased risk of the disease) or deemed unreliable, they can lead to case dismissal. (1) Even when epidemiological studies provide strong evidence in support of causation, defense lawyers and their retained experts will point out the studies' limitations--and all studies have limitations.

Jurors tend to find these studies confusing because of their complexity, and defense experts can make them more so. Many judges also misunderstand them. For these reasons, a civil jury trial is a challenging forum for presenting this type of evidence. (2)

General and specific causation

The ultimate issue in pharmaceutical litigation is causation, and a single epidemiological study does not establish causation. A study can, however, answer whether exposure to a drug is associated with an increased risk of the disease or condition under study.

Scientists recognize that causation is a judgment about the totality of experimental or epidemiological data. (3) As an amicus brief in the Daubert case noted, "By its nature, scientific evidence is cumulative: the more supporting, albeit inconclusive, evidence available, the more likely the accuracy of the conclusion." (4) Only through the accumulation of scientific evidence may a scientist infer causation. (5)

Proving causation in pharmaceutical cases requires showing that the drug is capable of causing the alleged injury (general causation) and that it was a substantial contributing cause of the plaintiff's injury (specific causation). Epidemiology is primarily used for addressing general causation but can also provide useful evidence in support of specific causation. (6)

Other evidence can help prove general causation. Case reports of the injury occurring after drug exposure provide good foundation evidence and, depending on their quality and content, can be persuasive.

Defendants downplay the value of case reports, claiming that they are merely anecdotal because there is no control group. However, if the injury has no other plausible explanation, if the timing of the injury in relation to drug exposure is striking, if the report concludes that the exposure was a likely cause of the injury based on differential diagnosis, or if the case report includes a challenge/rechallenge (where one takes a drug; watches for reactions; stops the drug; and then resumes taking it, watching for the same reactions as before), these facts can provide persuasive general causation evidence.

Other evidence that contributes to proving general causation includes animal studies and human pharmacology and toxicology experimental evidence, which provide insight into the mechanism of action (how a drug causes an injury) and biological plausibility (a causal connection that is consistent with medical knowledge). Proving the mechanism of action, although certainly helpful, is not required, and this mechanism is often, at best, only partially understood. Indeed, the manufacturers of many drugs admit they do not know how the drugs work. (7)

In 1965, scientist Austin Bradford Hill suggested various factors scientists could consider when determining whether to infer causation. (8) Each element of the so-called Hill guidelines does not have to be established to distinguish causal from noncausal associations; causation can be inferred even if some of the criteria are not met. (9)

The Hill guidelines are strength (of the association); consistency (that is, a repeated observation in different populations); specificity; temporality; biological gradient (that is, dose response); biologic plausibility; coherence (that is, the findings are consistent with other knowledge); experiment (that is, supporting animal and clinical evidence); and analogy (to similar drugs and disease).

Study types

Epidemiological studies generally fall into one of several categories, depending on the methods used to study the groups.

Cohort studies. Cohort studies are observational studies used when a large population exposed to a substance can be followed over time and compared with a large, unexposed population. Cohort studies can be used to measure the effects of environmental and toxic chemical exposures as well as the occurrence of adverse health effects in people who have used particular pharmaceutical products.

The largest cohort study ever conducted, the Million Women Study in the United Kingdom, showed a doubling of breast cancer risk among current users of combined hormone replacement therapy and increasing risk with increased duration of exposure. (10)

Case-control studies. These are a type of observational epidemiological study often used to evaluate the association between exposure to a drug and a rare or unexpected outcome of that exposure (such as hemorrhagic stroke or primary pulmonary hypertension). Case-control studies assess the effect of a drug by comparing users who have a disease or injury of interest (the "cases") to users without that disease or injury (the "controls").

By contrast, cohort studies start with a group of people exposed to a particular drug or agent and compare them with a group of people who were not exposed. Case-control studies usually are smaller (that is, fewer subjects are required), their duration is shorter, and costs are lower.

A case-control study starts with ascertaining a case group that has the disease or injury of interest, and a matched control group. Controls are matched to the case group on the basis of specified criteria, such as age, gender, race, and various socioeconomic characteristics.

Members of these two groups are then questioned extensively concerning lifestyle and health issues, medication use, and education level. If the question under investigation is whether Drug X causes Disease A, all cases and controls are asked to provide details about their exposure to Drug X. Preferably, the study should be "blind" to minimize bias--that is, study participants should be unaware of the study's hypothesis (that Drug X does (or does not) cause Disease A).

After statistical adjustments are made to account for differences between the groups with respect to known Disease A risk factors, a statistician can calculate whether there is a statistically meaningful difference of outcome between the cases and the controls, measure the magnitude of that difference, and calculate the degree to which the perceived difference could be due to chance.

Generally speaking, if the rate of exposure in the case group is greater than that in the control group (after adjustments for confounding factors), an association exists between the exposure and an increased risk of the disease. That association can be quantified, and the result is expressed as an odds ratio with a "Pvalue" and/or a confidence interval. [See box on page 34 for definitions of common epidemiology terms.] Exposure data can be collected to allow for assessments of dose, duration of exposure, how recent the exposure was, and other variables.

Randomized controlled trials (RCTs). These are interventional clinical trials that test the efficacy of a drug or procedure. The random assignment of the drug exposure in RCTs by the scientists conducting the study distributes potentially confounding factors equally among comparison groups. One group includes users of the drug under study; the other includes users of an alternative drug for treatment of the same medical condition or users of a placebo. (11)

RCTs are considered the strongest type of epidemiologic study for evaluating drugs: They have confirmed and quantified the cardiac risks from Vioxx and the breast cancer risks from hormone replacement therapy. (12)

The Women's Health Initiative was a 15-year RCT involving 161,808 postmenopausal women designed primarily to determine if hormone replacement therapy conferred a cardioprotective effect. It also tracked, as part of an observational cohort study, fractures and the incidence of breast and colon cancer. A total of 16,608 women were involved in the Prempro arm of this study, which was halted because it detected increased numbers of adverse health events, including invasive breast cancer, among women who took the drug. (13)

In the Vioxx litigation, RCTs have provided strong evidence of causation. The VIGOR study was designed to show that Vioxx caused less gastrointestinal toxicity than traditional nonsteroidal anti-inflammatory drugs (in this case, naproxen).

ADVANTAGE was an even larger study of 5,557 patients with osteoarthritis who were randomly assigned either Vioxx or naproxen. The APPROVe study (which resulted in the eventual withdrawal of Vioxx from the market) was designed to test whether Vioxx slowed the progression of colonic polyps.

All three RCTs provided evidence that Vioxx increases the risk of heart attacks, and APPROVe revealed a doubling of risk of heart attack or stroke even in a healthy population.

Size matters--and other concerns

Underpowered studies may miss an association, so effective studies must have adequate sample size to detect a difference between exposed and unexposed groups--if a difference really exists. Detection of rare events can require substantial numbers of study subjects.

Considerations such as time and cost may influence decisions about sample size and power. As a general rule, the greater the power, the more likely a study result will have a low P value and meet the conventional definition of statistical significance. When designing the study, the researcher will use statistics to calculate the minimum size of the study that will be needed to ensure that it answers specified questions within a specified range of confidence that the results will be valid, based on certain assumptions about exposure prevalence.

Often, a defendant will point out that although a study may associate a drug with a disease, it does not answer many necessary questions: For example, is the drug associated with the disease in subpopulations that were not studied, or at low doses, or after short-term use? A Study usually will not generate enough data to answer these detailed questions, allowing defendants to argue that the plaintiff cannot meet his or her burden.

However, in cases where the defendant sponsored the study, the plaintiff can argue that the defendant chose to keep the study small enough to avoid answering those questions. (14) In addition, when pharmaceutical companies sponsor case-control studies to investigate whether their drug causes a disease or injury, they often do so under pressure from the FDA and usually design the studies to be marginal on power.

By doing this, they save money and, more important, are more likely to miss detecting a result associating their drug with the disease (that is, the study more likely will have a false negative result, called a "Type II" error). Moreover, in a study that does not have a lot of power, if there is a result that associates a drug with a disease, defendants will be able to argue that the results are not statistically significant or that the numbers are small or "fragile."

When there is a clear association of a drug with a disease, but the study results do not meet the conventional definition of statistical significance (with a P value less than .05, meaning there is less than a 5 percent probability that the association is due to chance), defendants often point out that the finding should be disregarded--even if the odds ratio is high, indicating some association between the drug and the condition. They treat a P value of .05 as a bright line.

This approach has been criticized by epidemiologists:

   The notion that only when data demonstrate "statistical
   significance" do epidemiologists draw inferences about observed
   associations between suspected risk factors and medical conditions
   is mistaken.... Indeed, the term "statistical significance" could
   be expunged from the lexicon of the epidemiologist with no loss;
   accordingly it should not be allowed to assume an importance or
   role in law beyond its use as an epidemiological tool. (15)

In civil litigation, the burden of proof does not require a .05 P value as a standard for admissible evidence. Several noted epidemiologists have cautioned against using a P value greater than .05 to reject a study's results, noting that this practice transforms information about an association into a simple dichotomy of "significant" versus "not significant," which can be misleading. (16)

Observational studies, particularly case-control studies, are subject to a number of biases. The design and analysis of good case-control studies minimize biases to the greatest extent possible. Strict diagnostic criteria should be developed to ensure accurate identification of cases in the target population.

For instance, to minimize misclassification bias, investigators can confirm the disease by reviewing the medical records of suspected cases, without knowledge of their exposure status. Where timing of ingestion in relation to onset of symptoms is critical, extra care must be taken to ensure accurate data about when each person took the drug.

Inclusion and exclusion criteria should be clearly defined for both cases and controls before they are enrolled in the study. Exposure should be clearly defined, and an exposure window should be identified. Interviewers should be randomly assigned to cases or controls, and questions should be asked about multiple medications--this blinds subjects to the exact exposure under study. If possible, the interviews should be structured and scripted to protect against interviewer bias.

Working with experts

That an exposure may be associated with a disease does not mean that the exposure is the cause of the disease. At deposition, most epidemiologists will agree that there are only four possible explanations for a finding that A is associated with B: causation, chance, bias, and confounding factors. The researchers must therefore consider whether chance, bias, or confounding factors are likely explanations for the finding by reviewing the study critically.

In the end, researchers must make a judgment about whether an association indicates that a drug causes a condition. Chance, bias, and confounding factors cannot be eliminated completely, but they can be minimized. Experts should be questioned so that the opinion that causation is the most likely explanation for the results of the study can be critically explored. And all experts can be questioned on the roles of chance, bias, and confounding.

It is important not to get bogged down in a minitrial of the study itself. An expert, on direct examination, should be able to fully describe a study in about 30 minutes, explaining that all studies have limitations and biases and that, while chance can never be eliminated, it can be reduced to an acceptable level.

The use of visual aids at trial can be very helpful. For example, when the tables that appear in a published study are projected on a screen in the courtroom, jurors can see the data as the expert interprets it.

A case study

The litigation surrounding the drug phenylpropanolamine (PPA)--an ingredient in decongestants and appetite suppressants--and its role in causing hemorrhagic stroke in users featured a large, industry-funded, case-control study conducted by Yale researchers working with top stroke neurologists. (17) FDA reviewers concluded that the study was "one of the best planned, conducted, and most thoroughly analyzed studies reviewed in the last ten years" (18) and that it "demonstrated an increased risk of hemorrhagic stroke associated with PPA use." (19) Subsequently, PPA was removed from the market.

This study looked like a plaintiff's dream come true, and defense lawyers and their experts set out to destroy its credibility. The defendants took multiday depositions of the study's lead investigators and obtained by subpoena about 60 boxes of study documents, including e-mail and medical records from all patients who participated.

Internal records revealed that the PPA manufacturers had developed a strategy to attack the study before they even read it. The defendants unveiled a massive assault on the study in a Daubert brief filed in the multidistrict litigation (MDL), claiming that the study was fatally flawed in several ways, including its design, which industry sponsors had approved. According to the defendants:

* The study results were "fragile" due to small numbers, and the participation rate was too low.

* Cases were misclassified based on the timing of PPA exposure.

* Investigators (whom the industry sponsors had selected) had manipulated the data to find a positive association between PPA and hemorrhagic stroke.

* The control selection process was flawed.

* Investigators failed to account properly for the possibility that the stroke started before PPA ingestion.

* The results were not statistically significant.

* The study did not address (and thus did not answer) questions about every conceivable subpopulation (men, women, children, elderly) and every stroke subtype.

In rejecting this Daubert challenge, the PPA court made no attempt to resolve the many disputed issues concerning the study. Instead, it criticized the defense approach as an "ex post facto dissection" of the study. The court concluded that the defense "fail[ed] to undermine [the study's] reliability," (20) recognizing that scientific studies almost invariably contain flaws.

The court also noted that researchers commonly extrapolate from the subpopulations studied to subpopulations not studied, if certain conditions are met: for instance, if there is no biological reason why they should not apply and if there is a good reason why only select subpopulations are studied. (For example, children are commonly not studied due to difficulties with informed consent--yet, extrapolation from the results of adult studies is common.) Had there been several studies--as there were linking Vioxx and heart attacks--it would have been less likely that the defense would have taken this attack strategy because the defense loses credibility if its strategy is predicated on attacking all the studies.

The plaintiff attorneys had to defend the study against these attacks. Any scientist would understand that limiting a study's application to specific subpopulations is rarely a concern in the real world; however, it became an issue in this litigation and will become one in future cases if the defense believes it can succeed with a lay jury or some judges in making arguments that would never fly with scientists.

To avoid having an entire trial dedicated to proving whether a study is valid and its results reliable, plaintiff attorneys should plan to address these issues quickly and thoroughly. They should counter such criticisms primarily in cross-examination of defense experts, and leave an option for rebuttal expert testimony if needed. (21)

When a single study, no matter how worthy, is the main support for an argument, and the defense proceeds to tear it apart, the best strategy is to expose the defense effort as a litigation tactic and show how it is misleading. Make the credibility of the defense lawyers and experts the issue.

To make sure the study results are in your grasp, have an epidemiologist or a biostatistician available to consult in advance of trial; use basic epidemiology textbooks to gain familiarity with epidemiological terms and concepts; and aim to master the pertinent study-related documents, including the protocol, minutes of meetings, draft reports, and data summaries.

Proving causation in pharmaceutical cases with evidence from epidemiologic studies can make or break a case. Lawyers must understand the basics of epidemiology and develop a strategy for using epidemiological evidence effectively. This evidence can be spun by experts, so that even adverse study results can be presented in a light that advances the defendant's litigation interests. The best way to handle these challenges is to learn and understand the science, present it in a simple and straightforward manner, and identify and expose the spin for what it is.

Epidemiology in plain English 

Epidemiological literature is filled with jargon. These definitions of a few common terms should help you decipher the mathematical and medical lingo.

* Odds ratio. This is an estimate of the risk associated with exposure. An odds ratio greater than 1 means that exposure is associated with an increased risk of a disease or condition; an odds ratio of 2 means a doubling of risk. An odds ratio of 1 means there is no increase in risk, and an odds ratio less than 1 means that the exposure is protective and reduces the risk of getting the disease under study.

* Adjusted odds ratio. This is considered more precise than an odds ratio, as it takes into account that some people in a study may have been exposed to more than one potential risk.

* Attributable risk. Attributable risk, or fraction, quantifies the proportion of disease, among those exposed, that is caused by the exposure.

* Bias. This results from systemic errors in collecting or interpreting data, when noncomparable information is obtained from different study groups. Bias can result in a mistaken assessment of the effect of an exposure on the risk of disease.

* Confidence interval. This indicates the range of values within which the true odds ratio is likely to fall. Studies frequently use a 95 percent confidence interval, which means that if the study were repeated 100 times, one could be 95 percent certain that the range of numbers (or confidence interval) includes the true odds ratio (that is, in 95 of those 100 repetitions, the results would fall within the specified range of values). For example, if polls show that Candidate A will get 55 percent of the vote, plus or minus 3 percent, the confidence interval is 52 percent to 58 percent. If the poll were repeated 100 times, the results for Candidate A would fall between 52 percent and 58 percent 95 times. Study findings that have a narrow confidence interval are considered more precise than those that have a wide interval.

* Confounding. When an association is found, one must assess the study for confounders. A confounder is a risk factor associated with both the disease and exposure. For example, a study may find an association between taking diet pills and heart attacks. Before one can conclude that the diet pills cause heart attacks, one should assess whether obesity--a risk factor for heart attacks and associated with diet pill use--is a confounder. If there is a confounder, then the study results could be subject to multiple interpretations, and additional evidence or analysis is required.

* P values. These measure the probability that a reported association between a drug and condition was due to chance. A Pvalue of .05, which is generally considered the standard for statistical significance, means there is a 5 percent probability the association was due to chance.

* Relative risk. This is the risk of an event occurring (or of a disease developing) relative to exposure. It is the ratio of the probability of the event occurring in the exposed group versus the control (nonexposed) group. For example, if the probability of developing lung cancer among smokers was 20 percent and among nonsmokers 1 percent, the relative risk of cancer associated with smoking would be 20. Smokers would be 20 times as likely as nonsmokers to develop lung cancer.

* Statistical power. This is the probability that a study will detect an adverse effect, if one assumes that a drug confers excess risk. Generally, reliable analyses should have a power of at least 80 percent or better. That means that if an adverse effect exists, the study will detect it 80 percent of the time. The power of a study depends on a number of factors, including the frequency, or incidence, of an adverse effect; the magnitude of the excess risk conferred by the drug; the study's sample size; and the level of statistical significance used to decide whether a finding is due to chance.

* Statistical significance. When a study's P value exceeds .05, or its confidence interval includes 1 (that is, with a lower bound of, say, .8 and an upper bound of, say, 3.2), it is said to lack statistical significance. When a study reports a positive finding--that is, with an odds ratio above 1--that is not statistically significant, the power of the study must be considered. The lack of statistical significance could be due to either lack of a true increase in risk, or it could simply be an indication of insufficient statistical power.

* Type I and II errors. The detection of an effect of exposure when there is no effect is called a Type I error, or false positive. The failure to detect an effect when one exists is called a Type II error, or false negative, and is usually caused by a study not being large enough.--STEVEN ROTMAN

Notes

(1.) Daubert v. Merrell Dow Pharms., Inc., 509 U.S. 579 (1993).

(2.) Lawyers handling pharmaceutical cases should work closely with their epidemiology expert witness and purchase several epidemiology textbooks for easy reference, such as Leon Gordis, Epidemiology (3d ed., Saunders 2005); Charles H. Hennekens & Julie E. Buring, Epidemiology in Medicine (Lippincott, Williams & Wilkins 1987); Modern Epidemiology (Kenneth J. Rothman & Sander Greenland eds., 2d ed., Lippincott, Williams & Wilkins 1998); Kenneth J. Rothman, Epidemiology: An Introduction (Oxford U. Press 2002); Reference Manual on Scientific Evidence (2d ed., Fed. Jud. Ctr. 2000).

(3.) See Reference Manual on Scientific Evidence, supra n. 2, at 374; see also Hennekens & Buring, supra n. 2, at 4.

(4.) Br. of Profs. Kenneth J. Rothman et al., in Support of Petrs., 1992 WL 12006438 at * 11 (Dec. 2, 1992); Daubert, 509 U.S. 579.

(5.) Id.

(6.) The use of epidemiology and the concept of attributable risk for case-specific evidence in the context of a Vioxx case was discussed in J. Paul Sizemore, Embracing Risk Factors in Pharmaceutical Litigation, TRIAL 44 (Nov. 2006).

(7.) Many drug manufacturers admit in product labels that they do not know how the drugs work--take, for example, the labels as shown in the Physicans' Desk Reference (Thomson 2007) for the following widely used drugs: Ativan, Effexor, Fluothane, Inderal, Lodine, Neurontin, and Risperdal.

(8.) Austin Bradford Hill, The Environment and Disease: Association or Causation?, 58 Procs. Royal Socy. Med. 295 (1965). The standards of epidemiological evidence offered by Hill are saddled with reservations and exceptions. Hill was ambivalent about their utility. See Modern Epidemiology, supra n. 2, at 24-25.

(9.) Hill, 58 Procs. Royal Socy. Med., at 295.

(10.) Million Women Study Collaborators (Beral), Breast Cancer and Hormone-Replacement Therapy in the Million Women Study, 362 Lancet 419 (2003).

(11.) For a detailed discussion of clinical trials, see Gale Pearson, Uncover Bias in Clinical Trials, on page 22.

(12.) See e.g. Claire Bombardier et al., Comparison of upper Gastrointestinal Toxicity of Rofecoxib and Naproxen in Patients with Rheumatoid Arthritis: VIGOR Study Group, 343 New Eng. J. Med. 1520 (2000); Robert S. Bresalier et al., Cardiovascular Events Associated with Rofecoxib in a Colorectal Adenoma Chemoprevention Trial (APPROVe), 352 New Eng. J. Med. 1092 (2005) (Erratum, 355 New Eng. J. Med. 221 (2006)); Jeffrey R. Lisse et al., Gastrointestinal Tolerability and Effectiveness of Rofecoxib Versus Naproxen in the Treatment of Osteoarthritis: A Randomized, Controlled Trial (ADVANTAGE), 139 Annals Internal Med. 539 (2003).

(13.) Jacques E. Rossouw et al., Risks and Benefits of Estrogen Plus Progestin in Healthy Postmenopausal Women: Principal Results from the Women's Health Initiative Randomized Controlled Trial, 288 JAMA 321 (2002).

(14.) Most courts will allow a plaintiff to address issues of dose and duration and how recent the study was, as well as questions about subpopulations, with evidence from other sources, such as case reports.

(15.) See Br. of Profs. Kenneth J. Rothman et al., supra n. 4, at ** 3, 4.

(16.) See e.g. Clarice Weinberg, It's Time to Rehabilitate the P-Value, 12 Epidemiology 288 (2001); see also Richard Lempert, Statistics in the Courtroom: Building on Rubinfield, 85 Colum. L. Rev. 1098 (1985).

(17.) In re Phenylpropanolamine Prods. Liab. Litig., 289 F. Supp. 2d 1230, 1235-36 (W.D. Wash. 2003); Walter N. Kernan et al., Phenylpropanolamine and the Risk of Hemorrhagic Stroke, 343 New Eng. J. Med. 1826 (2000).

(18.) Yi Tsong, Statistical Review of Epidemiological Report of the Final Report of the Yale Hemorrhagic Stroke Project App. B16, at www.fda.gov/ ohrms/dockets/ac/00/backgrd/3647b1b_tab02. doc (Sept. 26, 2000).

(19.) Memo from Lois La Grenade & Parivash Nourjah, Div. of Risk Assessment I, FDA, to Charles Ganley, Div. of OTC Drug Prods., FDA, Review of Study Protocol, Final Study Report and Raw Data Regarding the Incidence of Hemorrhagic Stroke Associated with the Use of Phenylpropanolamine 2, at www.fda.gov/ohrms/dockets/dailys/ 00/oct00/102400/c000234.pdf (Sept. 27, 2000).

(20.) See In re Phenylpropanolamine Prods. Liab. Litig., 289 F. Supp. 2d at 1240.

(21.) Rebuttal expert testimony must be disclosed in advance. See Fed. R. Civ. P. 26(a) (2) (C).

STEVEN ROTMAN practices pharmaceutical litigation at Bubalo, Hiestand & Rotman in Louisville and Lexington, Kentucky.