Clinical Trial Designs in Oncology

Combinations of Agents

For phase I trials involving a combination of agents, the goal is to identify the doses of each of the agents to be used in the combination. There may be many dose combinations that have acceptable toxicity. For example, for a combination of agents X and Y, both high-dose X plus low-dose Y and low-dose X plus high-dose Y may have acceptable toxicity (but not high-dose X plus high-dose Y), so the choice between the two acceptable combinations (and the dose escalation scheme) will need to be made based on biologic and clinical considerations. If it is known that a certain minimal dose of X is necessary for its effectiveness, then the escalation would be of agent Y, with the dose of X fixed at its appropriate level. In addition, the toxicity profiles of the individual agents may suggest dose escalation schemes.

Late Dose-Limiting Toxicities

For some treatments, some DLTs of concern may occur late—for example, toxicities occurring up to a year after radiation treatment. This can lead to a very long phase I trial if one has to wait a lengthy evaluation period (e.g., 1 year) for each cohort of patients before the next cohort of patients can be treated. One approach to this problem is to model the occurrence of DLT times, for example, by assuming that DLTs are uniformly likely to occur over the evaluation period. If this were true, then one could extrapolate from the early toxicity experience of the patients to allow dose escalation before the patients have been followed for the full evaluation period. An example of this approach is the time-to-event continual reassessment method (although this particular method has apparently not worked well in practice ). If one designs a trial assuming the uniform occurrence of DLTs over the evaluation period and the assumption in reality does not hold, then one is at risk of exposing too many patients to DLTs. For example, if all the DLTs typically occur near the end of the evaluation period, then too many patients may be accrued at that dose level and a higher dose level based on not seeing any early DLTs. Because of this concern, additional constraints on these approaches are useful—for example, not accruing more than three patients at a dose level until the initial three patients at that dose level have been observed for at least one-half the evaluation period.

Biologic End Points

Phase I designs that escalate to find the highest dose level with acceptable toxicity (maximum tolerated dose) are based on the assumptions that (1) higher doses are more effective than lower doses, (2) higher doses are associated with more toxicity than lower doses, and (3) there is a dose with acceptable toxicity that will be effective. As opposed to cytotoxic agents, with targeted agents the first two assumptions may not hold, and with immunologic agents the first assumption may not hold. This suggests the use of a biologic (nontoxicity) end point to guide the dose escalation and to choose the dose for further testing. Although attractive in theory, designs using nontoxicity end points have been infrequent in practice. Instead, it may be preferable to assess the biologic end point at the maximum dose level determined according to DLT, and possibly at lower dose levels for comparison. In the context of a targeted agent, “phase 0 trials” are very small first-in-human trials that are designed not to find the recommended dose of the new agent, but instead to assess the agent's effect on its molecular target through use of low exposures of the agent not expected to cause any toxicity.

Randomized Screening Designs

There are two general situations in which a single-arm phase II trial design will not be appropriate because the results would be difficult to interpret. The first is when the agent is thought to be primarily cytostatic rather than cytotoxic, so an effective agent might not shrink tumors in a nonnegligible proportion of patients. One could, in theory, use a time-to-event end point such as progression-free survival (PFS) or overall survival (OS) in this situation. However, because of trial-to-trial variability in time-to-event outcomes, it can be difficult to identify a benchmark for an experimental treatment to beat in a single-arm trial. The other situation in which a single-arm phase II trial design would not be appropriate is when the treatment being evaluated is a combination of agents (agent X + agent Z), one of which is known to be active (agent Z). The problem is again identifying a null benchmark (e.g., response rate), in this case to isolate the contribution of agent X; there may be some data on the response rate of agent Z alone, but typically not from enough different trials in comparable settings that one could feel comfortable moving the combination therapy forward if its observed response rate was moderately higher than that of the response rate of Z alone.

For situations in which a single-arm design is not appropriate, a randomized screening design is an alternative. In this design, patients are randomized to the experimental treatment versus a control treatment to demonstrate superior activity with use of a phase II end point. Some examples of sample sizes for a response rate end point and a time-to-event end point (e.g., PFS, OS) are shown in Tables 18.1 and 18.2 , respectively. Note that for time-to-event end points, in which the time-to-event (survival) curves are typically compared with a log-rank statistic, the design can be specified in terms of the hazard ratio and the required number of events to be observed. For example, a trial to detect a hazard ratio of 0.5 with 90% power and 10% type I error would require 54 events. If one were targeting an improvement to a median PFS of 6 months (for the experimental treatment) from a median PFS of 3 months (for the control treatment), then one could randomize 62 patients over 1 year; the analysis would be performed when 54 events were observed, which would be about 9 months after the last patient was randomized. There is a choice regarding which patients should be included in the primary analysis of a randomized screening design: an intent-to-treat analysis, which includes all eligible randomized patients, or only those eligible randomized patients who started their assigned treatment. Restricting the analysis to patients starting treatment will provide a more sensitive assessment of treatment efficacy but is subject to bias if substantially more patients in one arm drop out of the trial before starting treatment; in the context of a phase II trial, this is not an issue if the trial is blinded.

Unequal randomization is possible in a screening design, whereby, for example, twice as many patients are randomized to the experimental arm as the control arm. Unequal randomization makes the required sample size larger—for example, 13%, 33%, or 278% larger for 2 : 1, 3 : 1, or 9 : 1 randomization, respectively. It is sometimes justified because it is said that the unequal randomization will make the trial more attractive to patients, thereby speeding accrual (although we know of no hard evidence on this). A better justification for unequal randomization is that in situations with limited experience with use of the experimental agent, it will allow more experience to be obtained (e.g., 40 patients instead of 30 in a 60-patient trial using 2 : 1 randomization instead of 1 : 1 randomization). Other issues concerning randomized screening designs are discussed later in the section on phase III randomized designs.

Randomized Selection Designs

Another type of randomized phase II design is the randomized selection design. In this design, the two (or more) treatment arms are experimental treatments. The goal of the trial is to select which of the treatment arms to take forward to further testing. At the end of the trial, the treatment arm that has the better efficacy outcomes is selected for further development. For example, if response rate was chosen as the outcome, then the arm with the better response would be selected. The sample size for this design is chosen so that there is a high probability that one will not select a worse treatment arm, if in fact there is one that is worse by a specified indifference margin. Selection designs require smaller sample sizes than screening designs because the conclusions from the design are much weaker (demonstrating that treatment X is not much worse than treatment Y instead of demonstrating that treatment X is better than treatment Y). When it is possible to evaluate each arm individually for efficacy—for example, when a response rate end point is being used for evaluating single agents—it is possible to embed within the selection design minimum (single-arm) response rates. For example, one could select the treatment arm with the better response rate provided that the response rate was at least 15%; otherwise, neither arm would warrant further study. The typical use of selection designs is for deciding which of several schedules of a new agent to use for further agent development.

Designs With Biomarkers

Phase II trials offer an opportunity to assess biomarkers for their ability to enable identification of a patient population for which the experimental treatment will be effective or especially effective. Unless there is strong evidence that the treatment will work only in biomarker-positive patients, the phase II trial should not restrict enrollment to such patients. Instead, the trial design should accommodate the possibility that benefit will be restricted but not assume it. For example, in a single-arm trial with a response rate end point, two-stage designs can be used wherein both biomarker-positive and biomarker-negative patients are accrued at the first stage; depending on what responses are seen at the first stage, the trial is either stopped or more biomarker-positive or unselected patients are accrued.

When there is strong evidence that a molecularly targeted agent will work only in biomarker-positive patients and some evidence that its efficacy may not depend on tumor histologic type, a single phase II trial that pools response data across biomarker-positive patients in different histologic groups may be useful. However, in the absence of reliable evidence that the activity level is uniform across these histologic groups, a separate evaluation may have to be conducted in each group to allow for a reliable evaluation. Note that the use of Bayesian hierarchical modeling to borrow information across groups does not work in this setting, although simpler pooled futility rules can be useful.

In settings in which a randomized screening design is used, one would again generally not restrict enrollment to biomarker-positive patients. After enrolling all comers, one could consider in an ad hoc manner the experimental-versus-control treatment effect in the overall group and the biomarker-positive and biomarker-negative subgroups. Alternatively, one could use a formal phase II biomarker trial design that directly addresses the relevant drug development question : Should a phase III trial be performed, and if so, how should the biomarker be incorporated into that design? Phase II designs with multiple biomarkers are discussed later under Designs With Multiple Biomarkers.

Randomization and Stratification

The randomization in a phase III trial is typically 1 : 1 (to avoid the inefficiency of an unbalanced randomization), and, after informed consent has been obtained, is ideally performed right before the experimental treatment is given (to avoid having to include patients who drop out of the trial before receiving the treatment under study). The randomization is typically stratified on a small number of variables thought to be highly associated with outcome to balance the distribution of these variables across the treatment arms and thus ensure that approximately equal proportions of patients in each arm of the trial will have relatively good and bad prognoses (as determined according to these stratifying variables). A stratified analysis can be used even if stratification was not part of the randomization—for example, when the stratifying variable is defined with a biomarker assay that is performed on a prerandomization sample after the randomization. Stratification is more important in smaller trials than larger ones because the chances of a worrying imbalance are larger in a small trial. When outcomes have a subjective component, blinding of the treatment assignment with placebos (when feasible) can remove a concern about potential bias in the trial results.

Multiarm Trials

A trial with multiple experimental arms and a single control arm can be an efficient way to test multiple treatments in a single disease setting. For example, a single randomized clinical trial (RCT) with a control arm and three experimental arms can be 33% smaller than three separate RCTs evaluating each experimental treatment separately. Multiarm trials can add complexity because they may require multiple placebos, restriction of eligibility to ensure that all the agents can be given safely, agreement among multiple industry partners to participate and agreement regarding how the data will be analyzed and shared, complex funding arrangements, and additional regulatory complexities.

A factorial trial design is a multiarm trial in which the arms represent all possible combinations of the experimental and control treatments. For example, in a 2 × 2 factorial design evaluating experimental treatments A and B (relative to no treatment), patients are randomized to one of the following four arms: (1) no treatment (arm C), (2) treatment A (arm A), (3) treatment B (arm B), or (4) treatment A plus treatment B (arm AB). (In some applications, a common backbone treatment will be given in all the arms.) A factorial analysis of a factorial design assumes that the effect of treatment A does not depend on whether the patient received treatment B—that is, the benefit of arm A over arm C is the same as the benefit of arm AB over arm B. (This is equivalent to assuming that that effect of treatment B does not depend on whether the patient received treatment A.) This assumption, which is referred to as no statistical interaction among the treatments, is very strong. When the assumption is satisfied, one can assess the efficacy of A and B in a trial with the same sample size as would be required to assess a single agent, a remarkable savings. However, if the assumption is not true, then a factorial analysis can incorrectly suggest that agents work when they do not, and do not work when they do. Even when a factorial analysis is problematic, the factorial trial design with a nonfactorial analysis is an efficient way to study two treatments and their possible interaction.

When a multiarm trial allows new trial arms to be added as it is ongoing, it is referred to as a “master” protocol or a “platform” trial. The idea is that when promising new agents become available they can be added (possibly along with corresponding control arms). In addition, trial arms are dropped when the questions involving these arms have been answered. An example of a master protocol is the STAMPEDE, which evaluates various agents in addition to a standard hormone therapy for advanced prostate cancer. The advantage of a master protocol is that it allows testing of agents more quickly because a new protocol does not need to be developed for each new treatment. This can be especially important when new treatment arms are suggested by the ongoing discovery of new biomarkers and targeted treatments. For any master protocol, one must avoid potential pressure to add new treatment arms or trial questions that may not be of the highest priority just to keep the trial ongoing.

Noninferiority Trials

In a noninferiority trial, one is interested in showing that the new treatment is not inferior to the standard treatment. These trials arise when the new treatment is expected to be less toxic or more convenient than the standard therapy. The sample size considerations are similar to those of a superiority trial (see Tables 18.1 and 18.2 ) with one important exception: the targeted treatment effect will typically be smaller, leading to much larger trials. The targeted effect is small because one does not want to recommend a new treatment that is inferior to a standard treatment by a nonnegligible amount. In particular, it has been suggested that the targeted difference should be no greater than a fraction of the benefit (e.g., 50%) seen for the standard treatment, which itself may not be large. In designing a noninferiority trial, the role of type I error and power are reversed, so that priority is given to minimizing the probability of declaring noninferiority when the new treatment is actually inferior; this probability should be kept very small (e.g., 2.5%), whereas the probability of declaring noninferiority when the treatments are equally effective could be set at 80% to 90%. For noninferiority trials, using the intention-to-treat principle can be problematic if there are a nonnegligible proportion of patients who do not receive their assigned treatments, because this can lead to underestimation of any true loss in efficacy ; to accommodate this, an additional analysis of only those patients who received their assigned treatments is typically performed.

In some situations, it is expected that the new treatment will actually be modestly better than the standard treatment, but because it is less toxic, it would be sufficient to demonstrate that it is noninferior to the standard treatment. In these special situations, the required sample size can be reduced.