E U R O P E A N J O U R N A L O F C A N C E R 4 5 ( 2 0 0 9 ) 2 7 5 – 2 8 0
`
`a v a i l a b l e a t w w w . s c i e n c e d i r e c t . c o m
`
`j o u r n a l h o m e p a g e : w w w . e j c o n l i n e . c o m
`
`Optimising the design of phase II oncology trials:
`The importance of randomisation
`
`Mark J. Rataina,*, Daniel J. Sargentb
`aSection of Hematology/Oncology, Department of Medicine, Committee on Clinical Pharmacology and Pharmacogenomics,
`The University of Chicago, Chicago, IL, United States
`bDivision of Biomedical Statistics and Informatics, Mayo Clinic, Rochester, MN, United States
`
`A R T I C L E I N F O
`
`A B S T R A C T
`
`Article history:
`Received 17 October 2008
`Accepted 29 October 2008
`Available online 6 December 2008
`
`Keywords:
`Phase II
`Clinical trial design
`Randomization
`
`Oncology trial end-points continue to receive considerable attention, as illustrated by the
`development and revisions to the RECIST criteria. In this article, we focus the reader away
`from the issue of end-points for phase II trials and towards what we believe to be an even
`more important issue, the fundamental need for randomisation in phase II oncology trials,
`ideally with blinding and dose-ranging. We present arguments to support the proposition
`that randomisation will enable greater clarity in the interpretation of the phase II trial
`results, as well as allowing for more precise estimates of the effect size and sample size
`requirements for definitive phase III trials. Randomisation will also reduce potential bias
`resulting from inter-trial variability, which inflates both type I and II errors if historical con-
`trols are utilised. In the context of a randomised blinded trial, the exact choice of end-point
`is less critical, although we favour end-points such as the change in tumour size or progres-
`sion status at a fixed early time point (i.e. 8–12 weeks after randomisation). Although end-
`points based on RECIST criteria can and should be utilised in randomised phase II trials, we
`do not believe that revision of the RECIST criteria will result in a fundamental improvement
`in drug development decisions in the absence of randomised clinical trials at the phase II
`stage of drug development.
`
`Ó 2008 Elsevier Ltd. All rights reserved.
`
`1.
`
`Introduction
`
`The phase II clinical trial plays a central role in oncology drug
`development. After a phase I trial has determined a tolerable
`dose for a new agent or combination, a well-designed phase II
`trial should provide the information required to make a go/
`no-go decision regarding subsequent phase III testing. As
`phase III trials require several years, hundreds or thousands
`of patients and often tens or hundreds of millions of dollars,
`the information that a quality phase II trial can provide is
`essential to a decision regarding the potential investment in
`a larger trial. In this paper, we present a rationale for the ex-
`
`panded use of randomisation in phase II oncology trials, in or-
`der to better inform this decision-making process.
`
`2.
`
`Why do we do phase II trials?
`
`Phase II trials should be most appropriately viewed as proof of
`concept trials, used for the purpose of determining whether a
`particular agent (or combination) should be studied further.1
`In this sense, they serve a critical filtering mechanism, in
`which a negative trial should lead to the discontinuation of
`development of a new agent for the selected indication.
`Optimising the filtering process is the critical issue: too tight
`
`* Corresponding author: Address: 5841 S, Maryland Ave., MC 2115, Chicago, IL 60637, United States. Tel.: +1 (773) 702 4400; fax: +1 (773) 702
`3969.
`E-mail address: mratain@medicine.bsd.uchicago.edu (M.J. Ratain).
`0959-8049/$ - see front matter Ó 2008 Elsevier Ltd. All rights reserved.
`doi:10.1016/j.ejca.2008.10.029
`
`MYLAN - EXHIBIT 1029
`
`

`
`276
`
`E U R O P E A N J O U R N A L O F C A N C E R 4 5 ( 2 0 0 9 ) 2 7 5 – 2 8 0
`
`a filter will terminate promising agents improperly, but a too
`porous filter will result in an excessive number of costly neg-
`ative phase III trials. In the previous era of oncology drug
`development, there were very few drugs available for the
`study, and as such a porous filter was very appropriate to
`minimise the possibility that a false-negative result would re-
`sult in the discarding of a promising agent.
`In the current era, there are hundreds of investigational
`oncology drugs available for the study. As such, we believe
`that it is more appropriate (at least at a societal level) to use
`a tighter filter, one that only advances to phase III develop-
`ment of those drugs for which there is a high probability of
`success in the phase III trial. We recognise that this strategy
`may be problematic for companies with a single drug in
`development. However, from a societal view, minimising the
`number of phase III trials of ineffective agents is important,
`as patients enrolled on a negative phase III trial may have lost
`the opportunity to participate in the trials of active investiga-
`tional agents, and financial and intellectual resources spent
`on a negative phase III trial similarly would be better spent
`on the development of new agents. Given the patient and
`financial resources required for a phase III trial in the current
`environment, we feel that it is more important to minimise
`the risk of failing to demonstrate the efficacy in phase III trial
`than to be concerned about the lost opportunities subsequent
`to not proceeding to phase III testing.
`We propose that attempting to ensure that phase III trials
`attain success on their specified end-point is best determined
`through the explicit modelling of the relationship of dose to
`both efficacy and toxicity. If an identifiable and reliable rela-
`tionship between dose and the chosen efficacy end-point
`can be established, considerable evidence is provided in sup-
`port of the success of the eventual phase III trial, particularly
`
`Table 1 – Impact of randomisation on strength of
`inference in phase II trial.
`
`if that efficacy signal is apparent at doses with an acceptable
`toxicity. On the other hand, if there is no relationship be-
`tween dose and efficacy, the drug may either be inactive or
`be active with a wide therapeutic index (Table 1).
`The information required to enable the best determination
`of dose–efficacy and dose–toxicity relationships is only
`obtainable from a randomised comparative phase II trial, as
`a single-arm trial only provides information for a single dose.
`Furthermore, unless the efficacy end-point is a response rate,
`it may not even be clear that the drug is efficacious at all, as
`demonstration of a prolonged period of stable disease may
`be due to an inadvertent selection of patients with a favour-
`able natural history, independent of any pharmacological
`drug effect.
`A further factor influencing our endorsement of random-
`ised phase II trials is the reality that a decision to move a drug
`from phase II to III is not a simple ‘thumbs up’ or ‘thumbs
`down’ decision. The standard phase II single-arm design is
`based on the promise that a difference of a single success (typ-
`ically tumour response) determines the phase III go/no-go
`decision. While even proponents of a single-arm trial likely
`realise that this is an artificial construct, the lack of randomi-
`sation in a single-arm trial hinders the ability to judge the tox-
`icity relative to control, to consider alternate end-points that
`may be more sensitive to the treatment effect, and to estimate
`the effect size relative to control that may be expected in the
`envisioned phase III trial.2 These effect sizes are the primary
`determinant of the sample size (and probability of success)
`in the phase III trial, and may also impact phase III end-point
`selection. Drugs may be active but fail in phase III because a
`phase III trial is too small, or because the chosen dose is too
`low (or high). Furthermore, it is important to have a fairly ro-
`bust estimate of the effect size, and the reliability of that esti-
`mate is determined by the sample size in phase II. Every one of
`these factors (effect size, relative toxicity, sensitive end-points
`and dose–efficacy) is better estimated through a direct ran-
`domised comparison at the phase II testing stage.
`
`Phase II
`strategy
`
`Single-arm
`trial
`
`Two-arm
`randomised
`trial with no
`control
`
`Two-arm
`randomised
`trial with
`control
`
`Multiple-arm
`randomised
`trial with
`control
`
`Result
`
`Strength of inference
`
`What are the options for design of phase II
`
`3.
`trials?
`
`Positive signal
`
`Negative signal
`
`Positive signal
`
`Negative signal
`
`Positive signal
`
`Unknown if due to true
`efficacy or bias
`Unknown if due to lack of
`efficacy, bias or wrong end-
`point
`Some sign that one agent
`more promising than
`another, but overall efficacy
`unclear
`Unknown if due to lack of
`efficacy, bias or wrong end-
`point
`Strong efficacy signal, but
`dosing may not be optimised
`
`Negative signal
`Positive signal
`
`Dose ineffective
`Strong efficacy signal, dosing
`able to be optimised
`
`Negative signal
`
`Drug ineffective
`
`Historically, phase II oncology trial designs can be divided into
`three categories: non-randomised (single-arm) trials com-
`pared to historical controls, randomised trials with multi-
`ple-experimental regimens compared to a historical control,
`and randomised trials including a prospective control arm.
`In this section, we provide a brief overview of each of these
`design strategies.
`The single-arm trial has been the most frequently used ap-
`proach to the efficacy evaluation at the phase II level in oncol-
`ogy, although it should be emphasised that this approach is
`rarely used in other therapeutic areas. Although there are
`multiple approaches to the implementation of the single-
`arm design, the overall principle has changed little since the
`design of Gehan.3 Patients are typically enrolled in two stages.
`If sufficient activity is observed at the end of the first stage, ac-
`crual continues to a second stage, and the number of suc-
`cesses (typically tumour responses) at the trial’s conclusion
`determines whether the agent is ‘recommended’ for further
`testing. Multiple variations, including optimal selection of
`
`

`
`E U R O P E A N J O U R N A L O F C A N C E R 4 5 ( 2 0 0 9 ) 2 7 5– 2 8 0
`
`277
`
`interim analysis time points, additional stages of accrual, con-
`siderations for multiple end-points, Bayesian approaches and
`approaches allowing three possible outcomes have been pro-
`posed.4–8 In an era when most new anticancer agents had very
`limited efficacy and thus any evidence of tumour activity was
`sufficient to warrant future testing, the single-arm design pro-
`vided a simple, direct and rapid method to assess an agent’s
`activity. The fundamental assumptions underlying the sin-
`gle-arm phase II trial are that data from the previous studies
`provide an adequately robust estimate of the experience the
`patients from the current trial would have had were they not
`to have received the experimental therapy, and that the end-
`point selected for the trial represents a definitive measure of
`agent activity. Both these assumptions are suspect in the cur-
`rent era. Rapidly changing standards of care in many diseases
`in therapy, imaging and supportive care imply that historical
`data may not be reflective of the results observed in the cur-
`rent clinical practice. This is compounded by the fact that ad-
`vances in tumour biology are segregating disease into marker-
`specific subtypes (e.g. based on Her-2 or K-ras status), for
`which historical data may be totally absent. In addition, new
`agents with novel mechanisms of action imply that standard
`end-points, such as tumour response, may not accurately cap-
`ture an agent’s overall patient benefit. The combination of
`these factors, in our opinion, questions the appropriateness
`of the single-arm trial at a fundamental level.
`A second class of phase II trials includes a randomisation
`to two or more experimental arms, but no prospective control
`arm. The goal of such a trial, often referred to as a selection
`design, is to provide more robust data than are available
`through single-arm trials to select the most promising exper-
`imental regimen to compare to a prospective control in the
`phase III setting. Numerous potential options for such trials
`have been proposed,9–11 all of which rely on an implicit com-
`parison to historical controls in terms of the level of activity
`required to justify moving forward the most promising exper-
`imental regimen to the phase III setting. As these phase II tri-
`als are not designed to establish a new standard of care, little
`concern is paid to the true type I error (the false-positive rate),
`which generally does not account for the multiplicity of test-
`ing (through multiple-experimental arms), as well as to an er-
`ror in the implicit historical control. While these selection
`designs do clearly provide much stronger comparative data
`to select a promising regimen amongst many possible phase
`III trials, the implicit comparison to historical controls confers
`the same disadvantages previously specified for the single-
`arm phase II trial.
`The third class of phase II trials includes a randomisation
`to one or more experimental arms and a prospective control
`arm. This is the standard approach to drug development in
`other therapeutic areas, in which the phase II programme is
`often divided into phase IIa (a two-arm trial for proof of con-
`cept) followed by phase IIb (a dose-ranging trial to optimise
`the phase III design). Two sub-classes of these randomised
`controlled designs have been used: those that formally use
`the control arm in the efficacy determination, and those that
`use the control informally. In the latter design, the control
`arm data are assessed as to its similarity to historical con-
`trols; if the control arm produces results that are ‘similar’ to
`prior experience, then the results from the experimental
`
`arm are considered valid. In our opinion, the inclusion of an
`‘informal’ control arm serves a false purpose. These trials
`are inherently comparative, and if it is recognised that the
`go/no-go decision for phase III testing will be based on many
`factors and will not be dependent on traditional statistical
`significance (p < 0.05), then to ignore the power of randomisa-
`tion to allow direct between-arm comparisons serves no valid
`scientific purpose. If the control arm is used in a formal effi-
`cacy comparison, the method of comparison is similar to that
`of a phase III trial, such as using a chi-squared comparison of
`response rates, or a log-rank comparison of progression-free
`survival (PFS) times. The formal use of the control group in
`the efficacy comparisons has been discussed by Rubinstein
`et al.,12 Fleming and Richardson13 and others.
`
`When is a non-randomised phase II trial
`4.
`sufficient?
`
`We believe non-randomised phase II trials in oncology should
`be the exception, not the rule. With that caveat, we acknowl-
`edge that such trials may be appropriate for trials in which
`the desired outcome (e.g. a partial response) will not occur
`in the absence of the investigational agent, and the rate of
`that outcome for existing agents or regimens is historically
`highly reliable. In this context, a positive phase II trial, defined
`as a response rate greater than some predefined threshold,
`would be evidence for activity, and a negative phase II trial
`would lead to the discontinuation of development for the spe-
`cific indication.
`Importantly, these criteria would never be met by many
`end-points often used in oncology clinical trials, such as ‘clin-
`ical benefit or survival beyond some threshold (unless that
`threshold was inconsistent with the natural history of the dis-
`ease). In addition, combination trials would generally not
`meet these criteria, unless the non-investigational compo-
`nents of the combination were known to be inactive in the
`target patient population. Finally, given the currently rapidly
`changing standards of care in many disease, once a new
`‘standard’ has been defined in any given disease, the histori-
`cal data obtained to date are invalid, due both to the availabil-
`ity of the new standard, and the fact that a new standard may
`change the treatment paradigm in that disease (e.g. poor
`prognosis patients who were previously untreated, thus not
`included in the historical control rates, may now become part
`of the treatment population).
`Additionally, non-randomised trials should never be used
`if there is an uncertainty regarding the optimal dose. The
`maximally tolerated dose has been traditionally utilised for
`phase II evaluation, despite the clear evidence against the
`general validity of the ‘more is better’ paradigm.14 For exam-
`ple, the randomised dose-ranging phase II trial of temsiroli-
`mus in renal cell cancer showed that doses of 25, 75 and
`250 mg weekly were all equally effective, leading to a success-
`ful phase III trial at the lowest dose.15,16
`We acknowledge that many experienced investigators
`continue to advocate the utility response rate as assessed in
`single-arm phase II trials. El-Maraghi and Eisenhauer17 re-
`viewed 89 trials of 19 agents, and concluded that the observa-
`tion of objective responses predicted for an eventual success.
`
`

`
`278
`
`E U R O P E A N J O U R N A L O F C A N C E R 4 5 ( 2 0 0 9 ) 2 7 5 – 2 8 0
`
`Given that the drugs with a 0% response rate in a single-arm
`phase II trial would not proceed to phase III testing, it is not
`surprising that no such agent achieved FDA approval. On
`the other hand, four of the six agents with the response rates
`under 10% were approved, including two agents with the re-
`sponse rates of less than 5% as single agents (cetuximab
`and sorafenib). The authors concluded that ‘even low levels
`of response may be interesting’ and acknowledged that larger
`phase II trials are required. However, the authors do not dis-
`cuss an important implication of their recommendation,
`which is likely the further increase in the number of phase
`III trials that will fail to achieve their desired end-point if all
`the drugs with the response rates of 3–4% (as observed with
`cetuximab and sorafenib) underwent phase III testing. We feel
`that PFS provides a superior signal from which to assess the
`efficacy for such agents, which is clearly assessed optimally
`through a randomised trial.
`Some authors have also suggested that the utility of sin-
`gle-arm trials using PFS or overall survival rates at a prede-
`fined landmark could be improved through the use of a
`model-based, comparison to historical controls. One example
`is a recent study by Korn and colleagues from five cooperative
`groups18 where the authors reported a multivariate prognos-
`tic model for metastatic melanoma, which they proposed
`could be utilised in single-arm phase II trials, as an alterna-
`tive to randomised trials. They suggest that only 63 patients
`would be required in a single-arm trial in this setting to have
`the same type I and II errors as a 220 patient randomised trial.
`While this model-based approach likely does provide some
`improvement compared to an unadjusted comparison to his-
`torical controls, it does not change our fundamental belief in
`the value of randomization: unless the model
`is perfect
`(which it never is), it is impossible to fully adjust the type I
`and II error for inter-trial variability, which in our opinion is
`the primary reason that single-arm phase II results are not
`replicated in phase III trials, as discussed further in the next
`section.
`
`When does a non-randomised phase II trial
`5.
`lead to a phase III trial that fails to achieve success
`on its primary end-point?
`
`As stated previously, the fundamental assumptions that
`could justify a single-arm phase II trial are that data from
`the previous studies provide an adequately robust estimate
`of the experience of the treated patients from the current trial
`were they not to have received the experimental therapy, and
`that the end-point selected for the trial represents a definitive
`measure of agent activity. Not surprisingly, when these
`assumptions are violated (which is common), phase III trials
`have a high rate of failing to demonstrate a significant
`improvement in the primary end-point from the experimen-
`tal therapy.
`From our perspective, the single greatest reason that
`uncontrolled phase II trials generate ‘false’ hope is the inter-
`trial variability in end-point success rates. Statistically, the
`failure to acknowledge the variability in the historical success
`rate inflates the nominal type I error level in the uncontrolled
`phase II trial.19 More importantly, regardless of the trial’s end-
`
`point, rapid advances in treatment outside the study protocol,
`supportive care, imaging modalities (to assess disease status)
`and other factors imply that patient outcomes will likely im-
`prove over time regardless of any new therapy. A likely even
`more dominant factor in the overall patient level success rate
`for a trial is the institutional composition of enrolling physi-
`cians and sites. Patient outcome has been repeatedly shown
`to associate with physician volume, and the patient mix at
`academic medical centres (which conduct the majority of
`phase II trials) differs widely from that in community prac-
`tice. These three factors (statistical underestimation, patient
`outcome drift and patient selection) combine to make the
`true type I error rate for the primary end-point in uncon-
`trolled phase II trials completely unknown (and unknowable).
`Multiple additional factors contribute to difficulty in pre-
`dicting successful phase III trials based on single-arm phase
`II trials. In single-arm trials of drug combinations, it is very
`difficult to distinguish the relative contribution of the stan-
`dard component from the experimental agent. The choice of
`a different end-point in a phase II trial (such as tumour re-
`sponse) compared to phase III (where overall survival or PFS
`is likely to be primary) is problematic, as response rate has
`been repeatedly shown to be a poor surrogate for these
`time-to-event end-points.
`The use of a control arm in a two-arm randomised phase II
`trial, comparing a single experimental regimen to a control,
`alleviates many of the issues above; however, several prob-
`lematic issues remain. As regimen doses and schedules are
`typically established through small phase I trials, with few
`(typically <12) patients treated at the MTD, limited informa-
`tion is available in most cases on the dose–efficacy and
`dose–toxicity relationships for the new agent. One potential
`cause of the failure in phase III trials is the error in the dose
`– either too high resulting in an unacceptable toxicity or too
`low resulting in an inadequate efficacy. This risk can be min-
`imised with a multiple-arm randomised phase II trial, where
`several dose levels are explored initially, and adaptively re-
`moved from the trial based on prespecified criteria.20
`
`What are the considerations in the design
`6.
`of randomised phase II trials?
`
`Although there has been a debate about the value of formal
`statistical comparisons in phase II trials, we feel strongly that
`such comparisons are appropriate, with the caveat that phase
`II trials do not necessarily need to provide reliable definitive
`comparisons at a traditional two-sided type I error of 0.05. Gi-
`ven that the purpose of any phase II trial is to determine
`whether to proceed with further agent development, there
`is only one outcome of interest, superiority of one or more
`experimental arms to the control. In this scenario, we believe
`a one-sided testing framework is appropriate. Given the need
`for phase II trials to be as small as possible and that a phase III
`trial will be required to confirm the efficacy in most cases,
`standard type I error rate control at the 0.05 level is not nec-
`essary. We and others12 propose that a one-sided test of the
`null hypothesis that the true primary outcome is no different
`between treatment and control with a false-positive rate of
`0.20 (type I error) is appropriate. In theory, if every phase III
`
`

`
`E U R O P E A N J O U R N A L O F C A N C E R 4 5 ( 2 0 0 9 ) 2 7 5– 2 8 0
`
`279
`
`trials were required to be justified by a randomised phase II
`trial with p < 0.20, this would lead to a phase III success rate
`of 80%, a significant improvement from the status quo. In
`contrast, in the uncontrolled phase II setting, the true false-
`positive rate is unknown.
`The use of this higher type I error remedies one common
`criticism of randomised phase II trials, that of very low statis-
`tical power.21 In the case of a multiple-experimental arm
`phase II randomised trial with a control, appropriate type I er-
`ror control is necessary to maintain an overall type I error rate
`of 20%, either through adjusting the alpha level for each com-
`parison of control versus treatment, or by comparing the
`experimental treatments to each other to identify the best,
`then comparing that regimen to control. Sample size consid-
`erations typically also dictate a type II error rate of 0.20, for a
`modest effect size (e.g. a hazard ratio of 1.5 in a time-to-event
`end-point, or a difference in response rates of 15–20%),
`although a lower type I and II error rates (e.g. 0.10) should also
`be considered if resources allow.12
`The choice of primary end-point in a randomised phase II
`trial depends on multiple factors. Ideally, a phase II screening
`trial should be a similar as possible to the subsequent phase
`III trial, including choice of primary end-point. Given the
`movement in advanced disease trials towards PFS as a phase
`III primary end-point,22 this is increasingly possible. Although
`overall survival can also be considered as the primary end-
`point for phase II and/or III testing, this would not permit
`the use of crossover designs, especially useful in the phase
`II setting.
`In our opinion, the most promising end-points for ran-
`domised phase II trials involve a comparison of a primary out-
`come measure at a single time point between the treatment
`and control groups. This outcome measure could be a tumour
`assessment at a fixed time point (e.g. change in absolute tu-
`mour size from baseline at 8–12 weeks following treatment
`initiation), or a rate of overall survival or PFS at a fixed time
`point (for example, 3 or 6 months). Such end-points facilitate
`independent radiologic review, eliminate subtle differences in
`scanning frequencies, simply patient scheduling and can be
`chosen to represent clinically meaningful time points. Ongo-
`ing research in multiple disease areas is examining these and
`other end-points to identify which end-points optimally pre-
`dict phase III success. In the future, newer methods such as
`functional imaging or assessment of circulating tumour cells
`may allow even earlier assessment of disease status.
`The validity of almost all end-points is improved by blind-
`ing, a tool infrequently used in oncology trials, particularly
`phase II trials. This is less important when overall survival
`is the primary end-point, but critical for end-points such as
`PFS, since independent radiological review can address bias
`in measurement but not bias in timing of radiological studies.
`When a trial is blinded, one can consider the use of novel end-
`points that incorporate patient-reported outcomes (e.g. time
`to symptomatic progression). In addition, blinding will result
`in a more robust analysis of toxicity attributable to the inves-
`tigational agent, as it controls for the ‘placebo effect’. Blinding
`can be logistically complicated, as it requires the availability
`of either an indistinguishable placebo (for oral agents) or
`sham parenteral dosing (for intravenous or subcutaneous
`agents). Although we feel that blinding should be considered
`
`for all randomised comparative phase II trials, we acknowl-
`edge that the final decision must consider all of these issues.
`The use of blinding also permits the use of the randomised
`discontinuation (or withdrawal) design, in which all eligible
`patients initially receive active treatment for a predefined
`run-in period. In this design, patients with stable disease at
`the end of a run-in period proceed to the randomised portion
`of the study (the primary analysis), in which they are random-
`ised to continued active treatment or placebo. To minimise
`the risk to patients randomised to the placebo arm, all pa-
`tients are offered crossover at progression, and those patients
`who had been randomised to placebo are restarted on open-
`label active treatment (those patients who had been random-
`ised to active treatment are withdrawn). This design is partic-
`ularly useful for the trials of the new agents as a single agent
`where it is hypothesised that the response rate is low, but that
`the drug has a clinically significant antitumour effect. We
`strongly feel that this design is superior in this setting to
`the use of a large single-arm trial, as a positive trial demon-
`strating a low response rate does not provide sufficient infor-
`mation to inform a robust decision to proceed to phase III
`testing.
`
`7.
`
`Conclusions
`
`Randomisation is greatly underutilised in early clinical trials
`in oncology. The use of randomised trials allows complete
`flexibility in the choice of end-points, particularly if blinding
`can be incorporated. This technique is the most powerful
`and reliable technique for distinguishing the effect of a drug
`from a placebo, a necessary predicate for a successful phase
`III trial. Given the large number of agents now available for
`clinical testing, the costs of phase III trials, and the limited
`patient and financial resources, available for such testing,
`the increased use of randomised phase II trials provides a ra-
`tional way to move new agents forward. Although end-points
`based on RECIST criteria can and should be utilised in ran-
`domised phase II trials, we do not believe that revision of
`the RECIST criteria will lead to any fundamental impact on
`improving drug development decisions in the absence of ran-
`domised clinical trials at the phase II stage of the drug
`development.
`
`Conflict of interest statement
`
`None declared.
`
`R E F E R E N C E S
`
`1. Sheiner LB. Learning versus confirming in clinical drug
`development. Clin Pharmacol Ther 1997;61(3):275–91.
`2. De Ridder F. Predicting the outcome of phase III trials using
`phase II data: a case study of clinical trial simulation in late
`stage drug development. Basic Clin Pharmacol Toxicol
`2005;96(3):235–41.
`3. Gehan EA. The determination of the number of patients
`required in a preliminary and a follow-up trial of a new
`chemotherapeutic agent. J Chronic Dis 1961;13:346–53.
`
`

`
`280
`
`E U R O P E A N J O U R N A L O F C A N C E R 4 5 ( 2 0 0 9 ) 2 7 5 – 2 8 0
`
`4. Bryant J, Day R. Incorporating toxicity considerations into the
`design of two-stage phase II clinical trials. Biometrics
`1995;51(4):1372–83.
`5. Chang MN, Therneau TM, Wieand HS, Cha SS. Designs for
`group sequential phase II clinical trials. Biometrics
`1987;43(4):865–74.
`6. Sargent DJ, Chan V, Goldberg RM. A three-outcome design for
`phase II clinical trials. Control Clin Trial 2001;22(2):117–25.
`7. Simon R. Optimal two-stage designs for phase II clinical trials.
`Control Clin Trial 1989;10(1):1–10.
`8. Thall PF, Simon R. Practical Bayesian guidelines for phase IIB
`clinical trials. Biometrics 1994;50(2):337–49.
`9. Sargent DJ, Goldberg RM. A flexible design for multiple armed
`screening trials. Stat Med 2001;20(7):1051–60.
`10. Schaid DJ, Ingle JN, Wieand S, Ahmann DL. A design for phase
`II testing of anticancer agents within a phase III clinical trial.
`Control Clin Trial 1988;9(2):107–18.
`11. Simon R, Thall PF, Ellenberg SS. New designs for the selection
`of treatments to be tested in randomized clinical trials. Stat
`Med 1994;13(5–7):417–29.
`12. Rubinstein LV, Korn EL, Freidlin B, Hunsberger S, Ivy SP, Smith
`MA. Design issues of randomized phase II trials and a
`proposal for phase II screening trials. J Clin Oncol
`2005;23(28):7199–206.
`13. Fleming TR, Richardson BA. Some design issues in trials of
`microbicides for the prevention of HIV infection. J Infect Dis
`2004;190(4):666–74.
`14. Winer EP, Berry DA, Woolf S, et al. Failure of higher-dose
`paclitaxel to improve outcome in patients with metastatic
`
`breast cancer: cancer and leukemia group B trial 9342. J Clin
`Oncol 2004;22(11):2061–8.
`15. Atkins MB, Hidalgo M, Stadler WM, et al. Randomized phase
`II study of multiple dose levels of CCI-779, a novel
`mammalian target of rapamycin kinase inhibitor, in patients
`with advanced refractory renal cell carcinoma. J Clin Oncol
`2004;22(5):909–18.
`16. Hudes G, Carducci M, Tomczak P, et al. Temsirolimus,
`interferon alfa, or both for advanced renal-cell carcinoma. N
`Engl J Med 2007;356(22):2271–81.
`17. El-Maraghi RH, Eisenhauer EA. Review of phase II trial designs
`used in studies of molecular targeted agents: outcomes and
`predictors of success in phase III. J Clin Oncol
`2008;26(8):1346–54.
`18. Korn EL, Liu PY, Lee SJ, et al. Meta-analysis of phase II
`cooperative group trial