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Originally published as JCO Early Release 10.1200/JCO.2009.23.1811 on May 18 2009 © 2009 American Society of Clinical Oncology.
Phase II Trials in Journal of Clinical OncologyHarvard Medical School, Program in Gynecologic Medical Oncology, Beth Israel Deaconess Medical Center, Boston, MA Life for the clinical investigator was much simpler 30 years ago. With only a handful of available cytotoxic agents, often obtained from cell line screens of plant-derived extracts, the progression of trials from phase I to II, and then ultimately to phase III, was well accepted, practical, and intuitive. The single arm phase II study was the principal mechanism for deciding whether to proceed to a randomized phase III trial. These phase II trials often used response rate as the primary end point and were powered to yield a reasonably low false-negative rate (type II error often in the range of 10% or lower) to capture the majority of potentially active regimens. Due to the small number of patients typically enrolled in single arm phase II trials and the reliance on historical controls for an estimation of expected response rate, it was recognized that this design is associated with a fairly high false-positive rate (type I error often in the range of 10% or higher). This was considered to be an acceptable compromise, realizing that the true activity of a new drug would eventually need to be clarified in a phase III trial. Over the past decade, there has been an explosion of new drugs designed to target specific pathways relevant to cancer growth, apoptosis, or angiogenesis. As more of these drugs show some measure of activity in single arm phase II trials, it has become clear that the ability of the standard phase II platform to accurately predict for phase III success is surprisingly low. Specifically, approximately 60% of oncology regimens that have apparently promising activity in single arm phase II trials fail to demonstrate superiority when tested in the phase III setting.1 Although this level of false-positive results might have been acceptable in the 1980s when there was a relative paucity of new compounds, at present there are several concerns over this high attrition rate. The cost of conducting large phase III trials, the ethics of asking patients to participate in a study that is likely to be negative (and which might expose them to unnecessary toxicity), and the burden on clinical investigators to open trials and enroll patients require that we increase the rigor with which we conduct phase II trials. These concerns not only have implications for clinical investigation but also have an important influence on the kinds of phase II trials the editors consider appropriate for publication in Journal of Clinical Oncology (JCO). There are several reasons why the single-arm phase II design might not be predictive of benefit when a new agent or combination is tested in the phase III setting. Typically such designs require a prespecified improvement in response rate, compared to historical control data, as an indication of phase III promise. However, it is well-known that historical control data are moving targets. What was representative 10 years ago might not be representative today, depending on shifts in disease presentation and patient referral patterns (population drift), improvements in radiographic and surgical staging techniques (stage migration), and improvements in the ability to assess response. In addition, the use of response rate as a measure of important clinical activity is not always straightforward; there are now several examples of cytotoxic regimens capable of increasing response rate without translating into improved overall survival.2 Conversely, there are other examples of drugs that yield an important prolongation of survival due to cytostatic mechanisms, without appreciable improvement in response rate.3 These and other issues related to the inadequacy of the single arm phase II design have been well described in several recent reviews.4–6 Despite these concerns, the single arm phase II design continues to have a role in disease settings in which the behavior of historical controls has remained stable over time, the likelihood of response to standard therapeutic options is low, the desired effect size of the novel agent is large, and the drug's mechanism of action is expected to be cytotoxic as opposed to cytostatic (permitting use of response rate as an end point). Some of these features are characteristic of relapsed, platinum-resistant ovarian cancer, where the single arm phase II trial still has a place in identifying single agents with promising activity. Conversely, adding an experimental agent to an active cytotoxic platform (eg, adding a third drug to paclitaxel and carboplatin in newly diagnosed ovarian cancer) may yield uninterpretable results in a single arm phase II trial, because the baseline activity of the regimen is already high, and the ability of this design to reliably distinguish between response rates is low. The randomized phase II trial is a well-known platform for testing the efficacy of novel agents in oncology, with the potential of minimizing some of the pitfalls inherent in the single arm phase II design.7 Such studies fall into three main groups, including randomized selection design ("pick the winner"), in which the best of two or more arms is chosen for further evaluation; randomized comparison design, in which a formal statistical comparison is made between the experimental and control groups; and randomized discontinuation design. It is not the goal of this editorial to discuss any of these designs in depth, although a few points are worth noting. The randomized selection design typically does not involve a standard therapy control but instead randomly enrolls patients onto two or more experimental arms, often evaluating different drug doses or schedules. The "best" arm is usually chosen based on predetermined response criteria but is still subject to the possibility of false-positive results (type I error in the range of 10% to 20%). In the randomized selection design, no formal attempt is made to compare any of the experimental arms with another. This design may be thought of as conducting several phase II trials in parallel, as opposed to sequentially, and can thereby accelerate the transition between phase II and phase III testing.
In contrast to the randomized selection design, the randomized comparison design often incorporates a formal statistical comparison of the experimental groups with a control (which could either be a placebo or standard therapy). Such a randomized phase II study superficially resembles a classical phase III trial, including statistical evaluations using the log-rank test to compare progression-free survivals (PFSs), or the It has been increasingly recognized that not all phase II studies are created equal. Some yield information of critical importance in the decision to proceed (or not to proceed) to a definitive phase III trial, and others produce results that are predictable, ambivalent, or do not move the field. Also, some phase II trials are performed for less well-accepted reasons, such as attempting to justify the use of an approved agent in a nonapproved setting (without the intention of performing a phase III trial for confirmation). Over the years, as we have discussed countless manuscripts during our twice monthly conference calls, the editors have achieved a general consensus regarding the types of phase II studies that would be most appropriate for consideration in JCO. The goal of this editorial is to provide a summary of these criteria to enable contributing authors and the readership to better gauge the likelihood of acceptance of a phase II manuscript in JCO. In addition, the editors hope that this editorial will assist other journals that may be struggling to prioritize the most important types of phase II trials for publication. To encourage submission of phase II studies that have the greatest potential for informing the design of phase III trials, the following categories of trials are appropriate for consideration at JCO (not listed in any particular order). SINGLE ARM PHASE II STUDIES THAT REPRESENT THE FIRST EVIDENCE OF ACTIVITY OF A NEW DRUG CLASS As mentioned here, there are situations in which the single-arm phase II design continues to play an important role in clinical investigation. Priority for this design will be given to studies of novel single agents, as opposed to combinations, since the contribution of the experimental agent will be easier to determine. Under certain circumstances, combination regimens might also be considered, especially if the novel agent has preclinical evidence of synergy with other drugs in the combination. In these cases, priority will be given to combination regimens that demonstrate an effect size large enough to assure the editors and readership that the results are not likely to be due to the other active drugs in the regimen. If these conditions are not met, such combination phase II studies are of lower priority because it is difficult to determine the relative contribution of the experimental agent to that of the other active drugs in the combination. Furthermore, derivative studies involving similar classes of agents that have been previously studied will receive lower priority, although exceptions are possible (see the next three sections). The historical control group used as reference for the single-arm phase II trial must be carefully justified, in order to convince the readership that biases such as population drift or stage migration have been minimized. The statistical considerations of the study must be outlined in detail, including the desired effect size, type I and II error thresholds, and early stopping rules when appropriate (which also applies to all clinical trials submitted to JCO). Finally, a phase II study will be given higher priority if the results of the trial have informed the decision to proceed to phase III testing, as documented by the existence of an ongoing phase III trial that was based on data provided by the phase II trial under consideration. PHASE II STUDIES OF NOVEL AGENTS THAT CONFIRM A CLASS EFFECT, BUT ALSO PROVIDE EVIDENCE OF EXTRAORDINARY AND UNANTICIPATED ACTIVITY COMPARED TO PRIOR AGENTS IN THE SAME CLASS For instance, the first demonstration of impressive activity of a novel tyrosine kinase inhibitor that targets the epidermal growth factor receptor (EGFR), especially if it overcomes resistance in tumors harboring a T790M mutation in the EGFR,8 might fall into this category. Conversely, a derivative study of a novel EGFR inhibitor that shows similar activity to other agents in its class, in the same disease setting, and without any obvious advantage in terms of toxicity profile, would receive lower priority. PHASE II STUDIES OF AN AGENT OR REGIMEN WITH PRIOR PROMISE (BASED ON PREVIOUS REPORTS OF CLINICAL ACTIVITY), BUT THAT ARE CONVINCINGLY NEGATIVE WHEN STUDIED MORE RIGOROUSLY Such negative phase II trials would receive higher priority if the agent was previously thought to be active, but is now convincingly shown to have questionable activity, especially if the study is instrumental in halting further investigation of the drug or ad hoc use of the drug in clinical practice. Negative phase II trials involving a derivative agent belonging to a previously studied class of inactive drugs would receive lower priority. In general, negative phase II trials will be viewed more favorably if correlative pharmacokinetic and pharmacodynamic studies have been performed to determine whether the drug is bioavailable and has affected its intended target (although it is recognized that such targets are often difficult to define). JCO is committed to publishing important negative phase II trials but also recognizes that the large number of such studies makes it imperative to enrich for those that will have the greatest impact on clinical trial development. PHASE II STUDIES OF A SINGLE AGENT OR COMBINATION THAT CONVINCINGLY DEMONSTRATE A NEW, SERIOUS, AND UNANTICIPATED TOXICITY SIGNAL, DESPITE BEING A RATIONAL AND POTENTIALLY ACTIVE REGIMEN Such studies will receive higher priority if the agent or combination is already known to be active and is being considered for evaluation in a phase III trial. Conversely, if the regimen has already been shown to be inactive (and therefore will not be studied further), the report of a novel toxicity signal would receive lower priority. PHASE II STUDIES WITH BIOMARKER CORRELATES THAT VALIDATE MECHANISM OF ACTION, PROVIDE CONVINCING INSIGHT INTO NOVEL PREDICTIVE MARKERS, OR PERMIT ENRICHMENT OF PATIENTS MOST LIKELY TO BENEFIT FROM A NOVEL AGENT These studies might involve markers of biologic activity such as pharmacodynamic end points (eg, tyrosine kinase phosphorylation in tumor biopsies or circulating WBCs), functional radiographic testing (eg, dynamic contrast enhanced magnetic resonance imaging), or analysis of response data based on the presence or absence of a genetic marker (eg, k-ras mutation). It is recognized that such biomarkers are often difficult to interpret in the phase II setting and would be viewed as hypothesis generating. This is especially the case for potential predictive markers, which require a phase III randomized control design for proper evaluation.9 Note that the inclusion of biomarker correlates, while viewed favorably, by itself does not guarantee that the paper will receive high priority in the absence of the other features discussed in the four preceding sections. RANDOMIZED PHASE II STUDIES SUCH AS RANDOMIZED SELECTION, RANDOMIZED COMPARISON, AND RANDOMIZED DISCONTINUATION DESIGNS Because the predictive value of single arm phase II studies is relatively low, JCO recognizes the importance of the randomized phase II design in the evaluation of novel drugs and regimens. However, many of the same considerations as previously discussed will pertain to judging the merits of randomized phase II trials submitted to JCO. These include drug novelty, preclinical rationale for synergy (for combination regimens), convincing effect size, and the influence of the phase II trial in deciding whether the regimen will progress to phase III testing. In addition, several other considerations are relevant to the randomized phase II design. The prospective statistical plan for evaluating data from such studies must be clearly described, especially for studies comparing an experimental arm with a control group. In particular, the rationale for using type I errors well below the 10% range must be clearly defended. This recognizes the fact that the randomized comparison design is generally considered to be hypothesis generating, as opposed to definitive. In such cases, a higher false positive rate is accepted (compared to a phase III trial) to keep patient numbers relatively low while still obtaining enough data to inform the decision to proceed with phase III testing. If a randomized comparison phase II study is designed with a type I error well below 10%, such a study would require larger numbers of patients to conduct, thereby exposing more patients to potential adverse effects in order to answer a question that might have been addressed with a smaller patient cohort. Because of this concern, the justification for using type I errors well below 10% in a randomized phase II design must be convincingly made to the editors, biostatisticians, and reviewers. Unplanned statistical analysis of data from a randomized phase II trial is discouraged. Whenever possible, the end points of the randomized phase II trial should be tailored to the drug's anticipated mechanism of action. For instance, a study involving a drug expected to prolong the duration of stable disease might use an end point such as PFS, as opposed to (or in addition to) response rate. In this regard, it is recognized that the use of PFS as an end point is most reliable when the study is placebo controlled and double blinded (which is the case for many phase III studies, but not always the case for randomized phase II studies due to cost issues). Without double blinding, various forms of bias can exist in the assessment of PFS. For instance, physicians caring for patients randomly assigned to an unblinded control arm might be tempted to assess disease progression earlier than specified by the protocol, based on clinical suspicion of progression. Blinded independent central review of the data from such a study would not always correct for this type of bias and may introduce other kinds of bias that are equally problematic.10 In studies where double blinding is not possible, it has been suggested that an assessment of patients who are progression free at a specified time point (eg, 4 months) might provide a more objective end point compared to PFS,5 although this assumes that patients have not been lost to follow-up before the time point of interest. JCO recognizes the challenges involved in determining the best end points to use in randomized phase II studies and urges authors to directly address these issues in their submitted manuscript. It is recognized that the randomized discontinuation design may be useful in evaluating drugs whose major effect is predicted to be disease stabilization. This design involves initial treatment of all patients with the experimental regimen, continuing the drug in responders, discontinuing it in nonresponders, and randomly assigning only those with stable disease to either continued drug or placebo. Because the "run-in" period in this design is sometimes difficult to predict (ie, how much time does the drug need to induce disease stability?), and because there may be a carry-over effect of the drug into the placebo group after it is discontinued, interpretation of the results of such studies is not always straightforward. A careful discussion of such biases will be important in evaluating the merits of randomized discontinuation trials submitted to JCO for consideration. As has been done for other types of clinical trial designs, including the development of CONSORT guidelines for phase III studies,11 JCO feels that it is important to establish analogous guidelines for evaluating phase II trials. The categories mentioned are not meant to be all inclusive, rigid, or definitive, but rather are intended to illustrate those elements of phase II design that are considered to be most important to the mission of JCO. The editors hope that authors and readers of JCO find this information useful, as they place the results of phase II trials (published in JCO or elsewhere) into proper perspective. AUTHOR'S DISCLOSURES OF POTENTIAL CONFLICTS OF INTEREST The author(s) indicated no potential conflicts of interest. Acknowledgment I thank my fellow editors of JCO for providing helpful comments during the preparation of this editorial. REFERENCES 1. Kola I, Landis J: Can the pharmaceutical industry reduce attrition rates? Nat Rev Drug Discov 3:711–715, 2004.[CrossRef][Medline] 2. Cannistra SA: The ethics of early stopping rules: Who is protecting whom? J Clin Oncol 22:1542–1545, 2004. 3. Ratain MJ, Eisen T, Stadler WM, et al: Phase II placebo-controlled randomized discontinuation trial of sorafenib in patients with metastatic renal cell carcinoma. J Clin Oncol 24:2505–2512, 2006. 4. Korn EL, Arbuck SG, Pluda JM, et al: Clinical trial designs for cytostatic agents: Are new approaches needed? J Clin Oncol 19:265–272, 2001. 5. Rubinstein LV, Korn EL, Freidlin B, et al: Design issues of randomized phase II trials and a proposal for phase II screening trials. J Clin Oncol 23:7199–7206, 2005. 6. Ratain MJ, Sargent DJ: Optimising the design of phase II oncology trials: The importance of randomisation. Eur J Cancer 45:275–280, 2009.[CrossRef][Medline] 7. Wieand HS: Randomized phase II trials: What does randomization gain? J Clin Oncol 23:1794–1795, 2005. 8. Engelman JA, Janne PA: Mechanisms of acquired resistance to epidermal growth factor receptor tyrosine kinase inhibitors in non-small cell lung cancer. Clinical Cancer Res 14:2895–2899, 2008. 9. Sargent DJ, Conley BA, Allegra C, et al: Clinical trial designs for predictive marker validation in cancer treatment trials. J Clin Oncol 23:2020–2027, 2005. 10. Dodd LE, Korn EL, Freidlin B, et al: Blinded independent central review of progression-free survival in phase III clinical trials: Important design element or unnecessary expense? J Clin Oncol 26:3791–3796, 2008. 11. Begg C, Cho M, Eastwood S, et al: Improving the quality of reporting of randomized controlled trials: The CONSORT statement. JAMA 276:637–639, 1996.
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Copyright © 2009 by the American Society of Clinical Oncology, Online ISSN: 1527-7755. Print ISSN: 0732-183X
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2 test for proportions to compare response rates. However, it differs from a phase III trial in several important ways, and a failure to understand these differences can sometimes lead to confusion. Unlike the randomized phase III study, the type I error of a randomized phase II trial is typically high, in the range of 10% to 20%, to keep patient numbers reasonable. Also, the results of a randomized phase II trial conducted in a smaller subset of patients may not reflect those obtained in a more representative population enrolled in a large phase III trial. In addition, an accurate estimation of effect size is often difficult to determine due to the wide confidence intervals typical of a randomized phase II trial. Finally, due to relatively small patient numbers, the toxicity signals and regimen tolerance might also be at variance with what would be observed in a larger phase III trial. For these reasons, the results of a randomized phase II trial using a control group are usually considered to be hypothesis generating and must generally be validated in a larger phase III trial. The typical goal of performing a randomized comparison phase II trial is not to obtain definitive efficacy information, but to identify promising experimental regimens that have a high likelihood of success in the phase III setting. 
