The previous installment of this series on clinical research highlighted some important fundamentals in cohort studies and randomized controlled trials (RCTs). In this article, additional issues that are critical to the understanding of RCTs are discussed, including causal inference, the use of surrogate measures, and the principle of intention to treat (ITT).
The previous installment of this series on clinical research highlighted some important fundamentals in cohort studies and randomized controlled trials (RCTs).1 In this article, additional issues that are critical to the understanding of RCTs are discussed, including causal inference, the use of surrogate measures, and the principle of intention to treat (ITT).
In an earlier installment, various clinical research study designs were discussed, and the differing “levels of scientific evidence” that are associated with each were ad­dressed.2 A comparison of study designs is complex, with the metric being that the study design providing the highest level of scientific evidence is the one that yields the greatest likelihood of cause and effect between the exposure and the outcome. The basic tenet of science is that it is almost impossible to prove something, but it is much easier to disprove it. Causal effect focuses on outcomes among exposed individuals, but what would have happened had they not been exposed? The outcome among exposed individuals is called the factual outcome. To draw inferences, exposed and nonexposed individuals are compared. Ideally, one would go back in time and repeat the same experiment among the same individuals but without the exposure to observe the counterfactual outcome. Because this is impossible, replication of results with multiple studies is the norm. Another basic tenet is that association does not denote causation (even when the association is statistically significant). Consider the finding of an association between coffee drinking and myocardial infarction (MI). Coffee drinking may precipitate (and be causal of) an MI. However, some persons who have had an MI may serendipitously begin to drink more coffee, in which case (instead of a cause-effect relationship) the association would be an “effect-cause” relationship (sometimes referred to as reverse causation). The association between coffee drinking and MI might be mediated by some confounder (eg, persons who drink more coffee may smoke more cigarettes, and it is the smoking that precipitates the MI) (Table). Therefore, observed associations may be spurious as a result of chance (random error) or because of some systematic error (bias) in the study design. In the first conceptual association in the Table, coffee drinking leads to MI, so it is causal. The second association represents a scenario in which MI leads to coffee drinking. An association exists, but coffee drinking is not causal of MI. In the third association, the variable x re­sults in coffee drinking and MI, so it confounds the association between coffee drinking and MI. In the fourth and fifth associations, the results are spurious because of chance or some bias in the way in which the trial was conducted or the subjects were selected.
Because causation cannot be proved, how does one approach the concept of proof? The Bradford Hill criteria for judging causality remain the guiding principles. The replication of studies in which the magnitude of effect is large, biologic plausibility for the cause-effect relationship is provided, temporality and a dose response exist, similar suspected causality is associated with similar exposure outcomes, and systematic bias is avoided go a long way in suggesting that an association is truly causal.
It has been said that “death is a fact, the rest is inference.” Specifi­cation of the outcome of an experimental intervention can be complex. Long-term outcome trials are expensive, loss to follow-up is problematic, and the development of medical and surgical innovations during the course of a long-term trial may present ethical issues that were nonexistent at the initiation of the trial. Shorter-term trials using a surrogate end point may be appropriate. A classic example is the use of blood pressure as a surrogate end point for an outcome of interest such as MI or stroke. Many other examples exist, including fasting glucose level for diabetic complications, bone mineral density for fractures, and a reduction in tumor size for cancer survival. However, the surrogate end point may not reflect the true outcome of interest. An example is the Cardiac Arrhythmia Suppression Trial.3 At the initiation of the trial, a reduction in the frequency and complexity of premature ventricular contractions by means of antiarrhythmic therapy was considered to be an adequate surrogate of a reduction in arrhythmic sudden cardiac death. Many antiarrhythmic therapies were approved using the surrogate end point, until the complete study results suggested otherwise. Changes in the surrogate end point must be predictive of the relevant clinical outcome and should reflect the effect of the experimental intervention on the outcome. These criteria are frequently difficult to fully appreciate, compounded by the fact that many treatments have several effect pathways.
Analytic issues regarding RCTs are also frequently misunderstood. Three common approaches are ITT analysis, compliers-only analysis, and as-treated analysis. With ITT analysis (sometimes referred to as analysis as randomized), everyone assigned to a treatment is counted in a treatment group whether or not he or she received that treatment. This seems counterintuitive because why would one consider a patient as having received a treatment when he or she did not? Is a compliers-only analysis (in which only those patients who were randomized to, received, and complied with the treatment intervention are counted) more logical? The answer lies in randomization, which is the most important reason why RCTs lead to the highest level of scientific evidence. The power of randomization is its ability to balance known and unknown confounders in the intervention and control groups. If all patients randomized to each group are not counted, the integrity of the randomization is compromised, and the strength of the RCT is reduced. Results obtained using a compliers-only analysis would only be equivalent if the same numbers of intervention and control subjects (and for the same reasons) were not compliant, which is unlikely and is why ITT is the preferred analytic method. If a patient was randomized to the intervention group but did not receive the intervention, one can argue that the outcome difference in the control group would be reduced. On the other hand, it is the outcome difference between the intervention and control groups that suggests that the intervention is beneficial. Finally, the as-treated analysis is generally used in a situation in which a medical intervention is compared with a surgical intervention and the medically treated patients cross over at some point to the surgical approach.
Intention to Treat