In the prior installment of this series on clinical research, various study designs were introduced, with a brief description of each.1 In this article, 2 of the more important study designs, cohort studies and randomized controlled trials (RCTs), are highlighted.
Recall that a cohort study is much like an RCT except that the intervention in an RCT is investigator controlled, while the intervention in a cohort study is a naturally occurring phenomenon. In a cohort study, it is assumed that the subject at the beginning of the study is “disease free” of the outcome of interest. For example, if the outcome of interest is recurrent myocardial infarction, the subject would have already had an initial myocardial infarction (in that sense, he or she is not disease free); in terms of the outcome of interest (a second infarction), at study outset the subject is obviously free of recurrent infarction. Using colon cancer as another example, one assumes at study outset that the subject is disease free (normal) at the time of enrollment; in fact, he or she may already have undiagnosed colon cancer. This could bias the study results because the exposure of interest (eg, a low-fiber diet) may have nothing to do with the outcome of interest (colon cancer), as the subject already has the outcome irrespective of the exposure. This also raises the question of what is a normal person. It has wittily been suggested that a normal subject is one that has been insufficiently studied! It is assumed that the incorrect assumption of no disease at study outset is equally balanced in the treatment and control groups; that is the expectation but not always the fact. What distinguishes the RCT from other study designs is that the exposure of interest (intervention) is controlled by the investigator.
The RCT is believed to yield the highest level of evidence for causality, particularly when the results of the RCT demonstrate positive findings. This has led to the consideration of RCT results as “gospel.” In fact, there are numerous problems that may adversely affect the results of an RCT. DeMets and Califf2 outlined 11 principles gleaned from RCT analyses, which are briefly summarized as follows: (1) Most current treatment effects are modest at best, and it is becoming more difficult to differentiate outcomes from the natural history of disease. More clinical trial subjects are receiving multiple therapies, and the interaction of therapies may positively or negatively affect the intervention of interest, confounding the results. Because treatment effects are small, it is important to differentiate statistically significant differences from clinically meaningful effects. (2) High-risk patients generally receive the most benefit from interventions, but clinical trials tend to exclude these patients, which limits the generalizability of the study results to the population of patients who might benefit from the investigational therapy. Selection bias is present in all trials, and RCTs are no exception. (3) Most clinical trials are short-term studies, and long-term effects may be more important. Fin­ally, disagreement abounds regarding the definition of an RCT, the most appropriate analytic method, the use of surrogate end points in lieu of the true outcome of interest, and the issue of causal inference as it relates to the application of the study results to “truth,” which will be discussed in a subsequent article.
The strengths of RCTs are numerous. One of the greatest problems in clinical research is the attempt to identically match the subjects in the exposure group to those in the control or comparator group, in order to avoid confounding the trial results. Known dissimilarities can, in part, be accounted for in the study design or analysis. Unknown confounders are the bigger problem. If the sample size is large, randomization tends to balance known and unknown confounders. Consider the example of a trial studying the relationship between coffee drinking (the exposure or “intervention”) and myocardial infarction (the outcome). Suppose an association is found, but in fact more coffee drinkers than nondrinkers smoked cigarettes and it was actually the smoking that was associated with MI. If smoking was a known potential confounder, stratification of coffee drinkers and nondrinkers who smoked versus those who did not smoke would have clarified the ob­served association. If confounding by smoking was unknown, randomization likely would have balanced the number of smokers in the exposed versus the unexposed groups, and confounding of the association with coffee drinking would have been avoided.
Another issue in RCTs is the selection of a control group; when it is ethical, the control group should receive placebo in a double-blind manner. The role of placebo in clinical trials is complex, and the reader is referred to a review of this subject.3 Other considerations are the use of surrogate end points and the method of intention-to-treat analysis, which will be discussed in a subsequent article.
Also important is whether RCTs are designed as superiority trials, equi­v­alency trials, or noninferiority trials. Classically, RCTs were designed as superiority trials, in which it is tested whether the investigational treatment is superior to the comparator treatment. Equivalency trials have in­creased in popularity, and test whether a new treatment is the same as some standard treatment (eg, an equivalency trial might be used when there is no evidence that the new treatment is more effective, but it might be less expensive or associated with fewer adverse effects). Noninferiority studies seek proof that the new treatment is not inferior to standard treatment. The appropriateness of the choice of trial designs is beyond the scope of this discussion but is based on the existent literature, on statistical considerations, and on sample sizes.
Finally, many RCTs are multicenter studies. Despite standard protocols, between-center differences in recruitment, patient selection, culture, and socioeconomics come into play. Each center likely recruits a different number of patients, despite attempts to equalize this and other variables. Although there is no panacea, several design methods minimize this problem. Consider a multicenter trial looking to enroll 100 patients, 10 at each of 10 centers. Should randomization of patients into the control and investigational arms be among the 100 patients, with the possibility that at some centers 8 of the 10 patients might be enrolled in one arm and 2 in the other arm? Or would it be better to use a blocked randomization scheme, with 5 of the 10 patients at each center in each arm? Many considerations influence these decisions.
In summary, cohort investigations and RCTs offer the best likelihood that study results reflect the truth. However, the clinician needs to be aware of the many strengths and limitations of these study designs and approach the results of any trial with healthy skepticism.