Clinical Hypertension Research Tools: The Randomized Controlled Clinical Trial

Abstract

The randomized clinical trial is used in hypertension research as a primary mode for evaluating new, promising therapies. Herein, the authors provide an overview of design features of clinical trials, particularly those useful for designing a hypertension therapeutic clinical trial.

A clinical trial is “a planned experiment designed to assess the efficacy of a treatment in man by comparing outcomes in a group of patients treated with a test treatment with those observed in a comparable group of patients receiving a control treatment, where both groups are enrolled, treated, and followed over the same period of time.” ¹ Phase 1 trials have a primary focus of describing adverse experience profiles, phase 2 trials proceed to acquire further safety information and estimates of efficacy, and phase 3 trials are designed to assess efficacy or effectiveness of the novel therapy compared with conventional medical therapy. In this paper, we discuss select clinical trial design issues, with a focus on phase 3 clinical trials. We introduce several matters including the target vs. the studied population and the choice of control group, as well as discuss explanations for observed treatment efficacy and, briefly, blinding and randomization. Sample size, select statistical issues, and some features of multicenter trials are also discussed.

CLINICAL TRIAL DESIGN CONSIDERATIONS

An essential aspect of a clinical trial is a precise hypothesis that drives the fundamental research question. This will govern both the design and analysis of the trial. The hypothesis is based on prior studies and has a plausible biomedical rationale.

One feature of the hypothesis is the specification of the target population to be studied. Often, this target population will be general and may include all individuals with a certain disorder, such as primary hypertension. However, a trial may restrict its study population through its inclusion and exclusion criteria. These criteria are often established to minimize adverse experiences and aimed at those patients who are most likely to benefit. These two issues of generalizability and actual trial patient selection are often in conflict with one another when designing a clinical trial. For example, a trial may not offer an aggressive anticoagulant therapy to all ischemic stroke patients when the most severe cases are expected to have immediate hemorrhage complications. Therefore, patient enrollment may be restricted and generalizability of the trial results suffers, since not all stroke severities are included in the trial. Accordingly, a critical phase of a clinical trial is the precise definition of inclusion/exclusion criteria and their relationship to the initially targeted population of the hypothesis. Trials that recruit a highly restricted subpopulation of patients may yield results validly applicable to this narrow subset, but not generalizable to the larger population. Such trial results are regarded as having internal validity (narrowly generalizable) but not external validity (not broadly generalizable).

Another important aspect of the clinical trial is the clear definition of the treatment regimen. This is critical for all trials, but can be challenging for multicenter trials. Educational measures including training sessions may be put in place to ensure that the treatment protocol is uniformly applied across centers. A related treatment protocol consideration is background care. Oftentimes, individuals are receiving concomitant therapy that continues in the trial. If the findings are to be generalized, it is important to document these background therapies. For some trials, this background care may require uniform definition as well.

A further challenge in designing a clinical trial is the definition of an appropriate comparison or control group. It is often easy to state that the therapy will be compared with a control, but defining this control may be a challenge. Often, a placebo is the appropriate control. This is the situation when there is no accepted therapy for a particular malady. It then may be ethically justifiable to assign patients to a placebo. On the other hand, a nonactive control is not appropriate if an established standard of treatment exists. For example, a new hypertension therapy is not evaluated against a placebo, but against one of the accepted standard treatments. Thus, the choice of control group for a clinical trial requires understanding of current treatment guidelines.

The selection of a primary outcome variable is another critical decision. This end point should be specified on an a priori basis, and meticulous care must be exercised in acquiring this end point for each individual. The primary outcome variable drives the design of the clinical trial, including sample size and statistical power considerations. The choice of the primary outcome variable may involve much deliberation and debate, but must be finalized as a first order of business before a trial can be designed. For some trials, the outcome variable may be defined simply, for example the change (i.e., difference) in systolic blood pressure after 6 months on therapy compared with the systolic blood pressure immediately before therapy. In other cases, the most appropriate outcome might be more complex, involving several end points amalgamated into a single outcome variable. The Trial of Org 10172 in Acute Stroke Treatment (TOAST) ² defined its primary outcome variable as a composite of two variables, namely, the Barthel Index and the Glasgow Outcome Scale. In addition to the primary outcome, the principal secondary outcomes should also be defined and operationalized. As an example, TOAST ² identified several secondary outcome variables including the National Institutes of Health Stroke Scale and a Supplemental Motor Scale. All statistical analyses plans for primary and secondary outcomes should be prespecified when developing the trial design.

There are many features to consider when designing a trial, and the preceding represent a sampling of the issues to consider. Further issues arise in interpreting a trial result. There are essentially four reasons why a trial might find a treatment to be more beneficial than the corresponding control. These include: 1) the two groups have been handled differently during the trial, affording an advantage to individuals receiving the treatment; 2) there has been some bias in how patients were assigned to receive either the treatment or the control; 3) the difference between the treatment and control is simply due to chance; or 4) the treatment is better than the control group. We briefly comment on the first two reasons in the following sections.

DIFFERENTIAL HANDLING OF TREATMENT AND CONTROL GROUPS

With the exception of the special features of the treatment regimen, every effort should be made to identically manage the treatment and control groups during the course of the trial. For example, pills might be available for the placebo group that will seem identical to the treatment pills. Often, the patients may not know which particular treatment they are receiving, and the groups may be managed identically in terms of frequency and intensity of trial assessments. In such an instance, the two treatment groups differ only with regard to the active agent found in the treatment tablets. The groups are otherwise managed in the same manner during the course of the trial. In this setting, one might conclude that differential handling of the two treatment groups is not the explanation for the observed difference.

In a formal sense, many clinical trials are “blinded.” Blinding is a device to help increase objectivity of measurements. In a single‐blind clinical trial, only the patients do not know which particular treatment they are receiving (treatment or control). A more desirable form of masking is double‐blinding. In this situation, not only is the patient blinded to the treatment received, but the treating physician is also blinded to the treatment that the patient is receiving. More generally, it is not the treating physician who would be blinded but the individual who makes the primary assessments of the clinical trial outcomes. Hence, in a setting where it is literally impossible to blind the treating physician, another evaluator who is blind to the patient's treatment would, for instance, assess the patient's blood pressure. Such techniques are common in trials to afford the trial a higher level of objectivity.

There are further variations on blinding that incorporate a third level. This level applies to those analyzing the data. For example, researchers reviewing the data on an ongoing basis with regard to adverse experiences and efficacy might be blinded to the actual treatment group. If a trial reports it was blinded, the reader must carefully examine the paper to understand the blinding used. For example, the TOAST clinical trial was a double‐blind randomized trial in which ischemic stroke patients received either a lower molecular weight heparinoid or placebo. ² Both the patient and evaluating physicians were blinded to the treatment. Even so, the adverse experience profile might be expected to be different in these two groups of patients. Individuals treated with the heparinoid might be expected a priori to have a higher frequency of bleeding events that might actually suggest which treatment a patient is receiving. Hence, a study may be reported as blind, but factors that might break the blind with regard to the objective assessment of the primary outcome variable must be carefully considered.

It is important to bear in mind that the principal concern of blinding in clinical trials is really to achieve a uniform, unbiased assessment of treatment and control patients. This principle might be applied in other ways, e.g., assessing a clinical outcome variable at the same frequency and intensity for both treatment and control patients. If there is a differential assessment schedule, then this might create a bias when interpreting the trial results. Another potential biasing factor is the manner of assigning patients to the treatment or control regimens.

ASSIGNMENT OF PATIENTS TO TREATMENT AND CONTROL GROUPS

There are many ways to assign patients to either treatment or control. The preferred mechanism for assigning individuals to treatment or control therapy is “randomization.” In the simplest case of “complete” randomization, the patient to be enrolled has a 50/50 chance of being randomized to either the treatment or control arm of the trial. Complete randomization is rarely done in a clinical trial because a set number of individuals in each group is often preferred, e.g., an equal number per group.

“Simple” randomization achieves this, often aiming for a balance between the treatment and control groups. For example, if 100 patients are to be enrolled in a trial, then we may aim for 50 in each. Typically, such balance yields maximum precision for making the desired treatment‐control comparison. Morever, with complete randomization, it is possible that, for example, only five individuals would be assigned to the treatment group and 95 to the control group, which generally would not be an optimal assignment. Therefore, simple randomization is most often used for a balanced 50/50 assignment.

Another extension of randomization is to use stratification. For example, men and women may be expected to be different in their response to treatment. Thus, gender might be used as a stratification variable. One would create a randomization schedule for men and a separate randomization schedule for women. This is stratified randomization and, within each gender, 50% would receive treatment and 50% would receive control. Stratification is commonly used in clinical trials. In designing a clinical trial, only very important factors should be considered as candidates for stratification. For example, in a mortality study, stratifying on gender or age would be reasonable. In hypertension clinical trials, stratification on duration of disease or presence/absence of renal disease might also be important factors for stratified randomization schedules. For multicenter clinical trials, the clinical center is typically used as a stratifying variable. One wants each participating center to have a 50/50 split of treatment and control individuals.

If a trial is reported to be a randomized clinical trial, then we should carefully review the details of the randomization. What type of randomization schedule was used; what provisions were in place to ensure that the assigning physicians did not know what treatment was to be used next; what stratification variables were used?

ADDITIONAL DESIGN CONSIDERATIONS

Issues related to blinding and randomization have been discussed, but an equally important consideration is the sample size of the trial. The sample size of a trial depends heavily on the primary outcome variable and the magnitude of the difference expected to be seen between the treatment and control groups with respect to this outcome variable. From a purely statistical perspective, one needs to model the outcome variable in a manner that will permit calculation of the required sample size. Essentially, the goal is to minimize the two types of errors that can be committed from a statistical hypothesis testing perspective. The type I error is that of declaring a benefit of treatment when none exists, and the type II error is that of declaring no benefit when one does exist. The power is the probability in detecting this benefit when it does exist. The aim is to design a study so that there is suitably high power (80% or 90%) to detect an important existing clinical benefit. The sample size calculation involves important study assumptions and precise knowledge about the primary outcome variable.

The simplest outcome variable is dichotomy, where individuals are considered as having a response or not having a response, e.g., lived or died. If such a dichotomy is the basis for the comparison between the treatment and control groups, the fundamental calculation of sample size then depends on a comparison of the two response rates—treatment group vs. control group.

Another common primary outcome variable type is the continuous variable. In this case, the normal distribution is often used as a basis for calculations. For a continuous variable, such as systolic blood pressure, variability estimates (SD) from previous investigations are used to project the sample size needed to have an 80% or 90% power to detect a clinically meaningful treatment benefit.

Other issues related to the sample size calculation relate to the impact of attrition, noncompliance, and logistic issues. These factors can also work to introduce potential bias, reduce the stated power, or minimize the treatment benefit estimate. These factors must be considered in the design of a trial. Finally, we must be mindful of the distinction between bias and precision. A loss of precision results if fewer patients are enrolled than were anticipated. Bias potential exists when patients are lost to follow‐up and cannot definitely be concluded as missing at random. For instance, if there is no complete primary outcome variable assessment for each patient, then the reduced sample size may reflect not only a loss of precision, but a bias that may not be able to be quantified easily. It may be that the patients lost represent different types of patients in the treatment group rather than in the control group.

MULTICENTER VS. SINGLE‐CENTER TRIALS

Much of the medical and hypertension research literature is focused on multicenter clinical trials. There are a number of reasons for this. First, multicenter trials represent the largest investigations in terms of numbers of patients studied. While single‐center trials are valuable in medical research, offering the opportunity for greater study control and tighter precision, the issue of generalizability is a severe limitation. Multicenter trials involve multiple institutions, multiple investigators, and multiple clinical settings; hence, one might regard the results of such trials to be more generalizable than a single‐center trial.

Often, multicenter trials are initiated when a large number of patients need to be accrued and no single site can accomplish the recruitment goal. However, the multicenter feature introduces additional complexities, including some heterogeneity. For example, patients at the various sites may not be similar. There are also issues of ensuring that assessments are done in a uniform way; this may require central laboratories, central reading facilities, site training, and ongoing monitoring and quality control It should also be noted that there are special analytic issues that arise with multicenter trials. For example, with a multicenter trial, there is the issue of using a center as an additional stratifying covariable in the statistical analysis. It is unusual for all centers to have treatment‐control differences that are of the same magnitude, or even going in the same direction. Indeed, if one has a 30‐center clinical trial, it may very well be that the treatment was beneficial at a number of sites but not at other sites. Hence, this needs to be incorporated into the final statistical modeling and in the interpretation of the study results. Even though the initial motivating force for a multicenter trial may have been to increase the patient pool to achieve the desired power considerations, it may very well be that additional heterogeneities have been introduced through the use of the multicenter clinical trial model.

ISSUES OF STATISTICAL ANALYSES

One of the most important considerations in making the treatment vs. control comparison for clinical trial data is deciding who will be included in the treatment group and who will be included in the control group when doing the statistical analysis. At face value, we begin a trial assigning individuals at random to a treatment or a control group. If every individual complies with the treatment in exactly the prescribed manner, and if each patient yields the primary outcome variable assessment, then there are no problems. However, no trials achieve such results.

In most instances, the following scenarios may evolve in one form or another. Individuals are assigned to receive treatment or control therapy. Once assigned, some patients decide that they do not wish to receive such therapy. This is in spite of all the best efforts to appropriately screen individuals and to consent individuals for the study. Thus, some individuals are assigned to a treatment, but will not receive the treatment in the matter prescribed. There are many variations on this theme. An individual might take all of the medication for part of the time or might take a lower percentage of the medication all the time. In addition, some individuals drop out before we obtain their final outcome assessment due to side effects that the patient attributes to the treatment, a strong desire to no longer participate in the study, adverse experiences or outcomes, migration from the area, or loss to follow‐up. Thus, a relatively simple and straightforward statistical analysis plan that was described in the protocol is now compromised by these issues. What should be done?

The most widely accepted analysis for clinical trials is the so‐called intention‐to‐treat (ITT) ³ model. ITT is a method for including individuals into groups to which they are originally assigned. In particular, if a patient was assigned to receive the treatment, then the patient is included in the treatment group for purposes of the statistical analysis. This is done irrespective of whether the patient took the medication or whether the medication was taken in the manner prescribed in the treatment protocol. Randomization assigned the patient to that particular treatment group, and that will be the particular treatment group considered in the analyses. The same would hold true for an individual assigned to a control group. While the ITT analysis is regarded at the primary analysis for most evaluations of phase 3 clinical trials, it is important to keep in mind that there may be other analyses of interest.

An additional analysis is the per‐protocol analysis. With this method, analyses are restricted to the subset of patients who took the treatment in exactly the manner that was prescribed and were followed in exactly the manner that was assigned. Hence, in most instances, a reduced subset of the original pool of randomized individuals are studied. A per‐protocol comparison yields the possibility of dealing with a biased group of individuals insofar as individuals are selected on the basis of what they have done after randomization rather than before randomization. Hence, whether an individual is per‐protocol or non‐protocol is really something that has occurred after the randomization. These individuals were not identified before randomization; hence, the risk of bias is introduced with this comparison. Nevertheless, per‐protocol analyses are done to try to elicit and explain the findings, especially with regard to the relationship between the finding and the intended treatment benefit. In instances where proprietary interests exist, per‐protocol analyses can be especially problematic. In many situations, both an ITT analysis and a per‐protocol analysis are performed and these analyses are then compared. Often, the per‐protocol analysis yields results that differ from the ITT analysis. This is not always the case; therefore, it must be decided beforehand which is going to be the primary analysis. ITT represents the widely accepted standard for the primary analysis. ¹ , ³

CONCLUSIONS

We have described several features of clinical trials, including some key issues such as blinding, randomization, power, multicenter trials, and statistical analyses. There are obviously a number of issues to be considered in designing, or reviewing, a clinical trial. ¹ , ⁴ , ⁵ , ⁶ , ⁷ , ⁸ As noted earlier, future articles in this series will deal with other epidemiologic and biostatistical topics.

Disclosure: The authors acknowledge the research support of the National Institutes of Health Grants #RR01070 from the National Center for Research Resources and #5R01HL072377 from the National Heart, Lung, and Blood Institute.