The architecture of clinical research

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An important consideration in designing a trial is to define and declare the primary outcome measure carefully because defining the primary outcome measure has important implications for the study. I will provide an example from the alpha-1 antitrypsin deficiency literature. Some of you have probably read what has been called the RAPID trial.5 RAPID was a trial of augmentation therapy vs placebo in patients with severe alpha-1 antitrypsin deficiency. The primary outcome measure (which was pre-negotiated with the US Food and Drug Administration [FDA]) was computer tomography (CT) lung density determined at functional residual capacity (FRC) and total lung capacity (TLC). The trial failed to achieve statistical significance in regard to CT lung density, although the study authors argued that CT density measurements made at TLC were more reproducible than those made at FRC. When the results were analyzed by TLC alone, the results were statistically significant, but when they were analyzed with FRC and TLC combined, they were not. In the end, based on the pre-negotiated primary outcome measure of CT density based on both FRC and TLC, the FDA rejected the proposal for a label change to say that augmentation therapy slowed the loss of lung density even though the weight of evidence was clearly in its favor. This case exemplifies just how critical the choice of primary outcome measure can be.

Design of a randomized crossover trial of terbutaline for diaphragmatic function.
Figure 2. Design of a randomized crossover trial of terbutaline for diaphragmatic function. The wash-out period separates the first and the second interventions (begins at the star in the diagram).

The wash-out period refers to an interval in a subset of randomized trials called “crossover trials” in which the primary intervention is discontinued and the patient returns to his baseline state before the comparative maneuver is then implemented (Figure 2).6 In order to perform a crossover trial, it is important that the effects of the initial intervention can “wash out” or be fully extinguished. So, for example, in trials of radiation therapy vs surgery, it is impossible to do a crossover trial because the effects of radiation can never completely wash out nor can those of surgery, which are similarly permanent. For example, we cannot replace the colon once it is resected for cancer or replace the appendix once removed. Therefore, producing a wash-out requires some very specific pharmacokinetic and pharmacodynamic features in order for a crossover trial to be considered. Later talks in this series will discuss the enhanced statistical power of a crossover trial, where one is comparing every patient to him or herself rather than to another patient.

So, there is always an appetite to do a crossover trial as long as the criteria for wash-out can be met, namely again that the primary intervention can dissipate completely to the baseline state before the alternative intervention is implemented.

“Placebo” is a fairly self-evident and well-understood term; placebo refers to the administration of a maneuver in a way that is identical to the principal maneuver except that the placebo is not expected to exert any clinical effect.

“Blinding” is the unawareness of either the investigator or of the patient to which the intervention is being administered. “Single-blinding” refers to the condition in which either the study or the investigator (but not both) is unaware, and “double-blinding” refers to the condition in which both the subjects and the investigators are unaware. There can be some subtle issues that compromise whether the patient is aware of the intervention that he or she is receiving and that can potentially condition the patient’s response, particularly if there is any subjective component of the assessment of the outcome. So, blinding is important.

With these terms describing the elements of a clinical study now described, let us turn to the types of studies that comprise clinical research. The first group of study types is what Dr. Feinstein called descriptive studies—studies that simply describe phenomena without comparison to a control group. As an example of a descriptive study, Sehgal et al7 recently described the workup of a focal, segmental pneumonia in a patient taking pembrolizumab for lung cancer. In this paper, there were four other cases of focal pneumonia accompanying pembrolizumab use that were assembled from the literature, making this descriptive paper a so-called case series. A “case series” differs from a “single case report,” which reports a single patient experience. Though limited in their ability to establish cause and effect, case reports and case series can help researchers develop proof of principle, so I would not discount the value of case reports.8

I can cite a case report from of my own experience that demonstrates this point. In 1987, I saw a patient from Buffalo who had primary biliary cirrhosis and the hepatopulmonary syndrome (HPS). She was so debilitated by her HPS that she could not stand up without desaturating severely. Although she had normal liver synthetic function, she was severely debilitated by her HPS and the decision was made to offer her a liver transplant, which, at that time, was considered to be relatively contraindicated. Much to everyone’s amazement and satisfaction, her HPS completely resolved after the transplant surgery. Her oxygenation and alveolar-arterial oxygen gradient normalized, and her clubbing resolved. We reported this in a case report, which began to affect the way people thought about the feasibility of liver transplant for the HPS.8 The lesson is: do not underestimate the power of a thoughtful case report.

The second group of research study types is called “cohort studies,” in which one actually compares outcomes between 2 groups in the study. Cohort studies fall into the bucket of either “observational cohort studies,” in which allocation to the compared maneuvers is not performed by randomization but by any other strategy, and “randomized trials.” In observational studies, allocation could occur through physician choice, as when the physician prescribes a treatment to 1 group but not another, or by patient choice or circumstance. For example, an observational cohort study of the risk of cigarette smoking would compare outcomes between smokers and non-smokers where the patient choses to smoke under his/her own volition. Alternatively, the circumstances of an exposure could allocate someone to the principal maneuver, as when we are studying the effect of exposure to World Trade Center dust in the firefighters who responded or of exposure to nuclear radiation in Hiroshima survivors. These are examples of observational cohort studies that compare exposed individuals to unexposed individuals, where the exposure did not occur by randomization but by choice or unfortunate circumstance.

In contrast to observational studies, allocation in randomized trials occurs through a formal process. Randomization has the specific purpose of attempting to ensure that patients are allocated to 2 comparative groups from the baseline group with comparable risk for developing the outcome measure. When randomization is effective, differences in study outcomes can be reliably ascribed to the intervention rather than to differences in the baseline susceptibility of the compared groups.

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Basics of study design: Practical considerations

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