Pii: s0895-4356(00)00357-7

Journal of Clinical Epidemiology 54 (2001) 550–557 The randomized placebo-phase design for clinical trials Brian Feldmana,*, Elaine Wangb, Andrew Willanc, John Paul Szalaid aDivision of Rheumatology, The Hospital for Sick Children and the Department of Paediatrics and Public Health Sciences, University of Toronto, Toronto, Ontario, Canada bDepartment of Paediatrics, The Hospital for Sick Children and the University of Toronto, Toronto, Ontario, Canada cDepartment of Clinical Epidemiology and Biostatistics, McMaster University, Hamilton, Ontario, Canada dDepartment of Research Design and Biostatistics, Sunnybrook and Women’s College Health Sciences Centre, and the University of Toronto, Toronto, Ontario, Canada Received 27 September 1999; received in revised form 2 October 2000; accepted 1 November 2000 Abstract
Randomized controlled trials are the criterion standard method for evaluating the effectiveness of medical treatments. There are situ- ations, however, where the possibility of being in the control group in a randomized controlled trial is unacceptable to potential subjectsor their physicians. This lack of acceptance is a reason for poor accrual. We developed and validated a new clinical trial design for survivaldata that may allay concerns about not receiving an investigational product and should be more acceptable. Called the randomized pla-cebo-phase design, this new design asks whether, on average, those subjects who begin active treatment sooner respond sooner than thosewho begin it later. Using Monte Carlo computer simulations, we demonstrated that the design is valid and may offer advantages over tra-ditional randomized controlled trials in some situations. The randomized placebo-phase design may be especially useful when highly po-tent therapies for rare diseases are tested or when accrual may be otherwise difficult.
2001 Elsevier Science Inc. All rights reserved.
Keywords: Clinical trials; Randomization; Blinding; Therapy; Statistics; Efficacy 1. Introduction
rare that there are not enough subjects available for studythe power to detect a true treatment effect will be too lim- Medicine has entered the evidence-based era, one in ited to carry out a comparative trial. These two issues likely which scientific evidence determines the best clinical prac- interact: problems with the acceptability of a study make it tice. This evidence comes from high-quality clinical studies, harder to recruit subjects [1] which makes the recruitment which in turn should form the basis for current treatments.
difficult when the condition being studied is uncommon [3].
However, providing studies of sufficient rigor to support For example, a recent study [4] of the use of intravenous im- treatment recommendations is difficult in many areas of munoglobulin therapy for childhood arthritis failed because medicine. Perceived problems with randomized controlled of poor accrual. For relatively rare conditions, such as child- trials (RCTs) have led, in some situations, to poor accept- hood arthritis, there is a striking paucity of RCTs on which ability by participants, physicians, and researchers [1].
The standard two-arm RCT is the criterion standard for the Some patients, and their referring physicians, cannot ac- evaluation of medical therapies [2] because the RCT is de- cept treatments that are chosen by a process that is analogous signed to limit bias, such as selection and measurement bias.
to the toss of a coin [6–8]. Investigators may also have prob- In some situations, however, an RCT may be difficult to lems with the acceptability of an RCT. If an investigator carry out. For example, when a new therapy offers a poten- knows, or has reason to believe, that one treatment arm is su- tial cure for a previously untreatable and fatal disease, it perior to another it is not ethical to enroll patients in an RCT.
may be unacceptable to have a control group that does not Investigators are required to be in a state of equipoise [8].
receive the new therapy. In addition, when a disease is so Even when the current slate of knowledge allows for reason-able equipoise in the wider medical community, treatment tri-als are usually conducted with the hope, perhaps even the ex- * Corresponding author. The Hospital for Sick Children, 555 Univer- pectation, that the experimental therapy will be better in some sity Ave, Toronto ON M5B 1X8, Canada.
way than the traditional therapy or the placebo. Individual in- Tel.: 416-813-5828; fax: 416-813-4989E-mail address: [email protected] (B. Feldman) vestigators may not believe they have equipoise [9,10].
0895-4356/01/$ – see front matter 2001 Elsevier Science Inc. All rights reserved.
PII: S 0 8 9 5 - 4 3 5 6 ( 0 0 ) 0 0 3 5 7 - 7 B. Feldman et al. / Journal of Clinical Epidemiology 54 (2001) 550–557 Investigators may use a variety of more powerful designs the course of eight subjects, divided into two groups of four, in order to study new therapies with fewer subjects. Cross- who begin an effective experimental treatment at different over trials and n-of-1 studies provide precise information about the treatment response of individual subjects. Cross- Selection bias might occur if those subjects who were over trials may therefore be more statistically powerful than more likely to respond sooner were assigned to start treat- the parallel design RCT [11–13]. These designs, however, ment sooner than those subjects likely to respond later. This do not provide the same quality of information as the RCT, is prevented in the RPPD by randomization of subjects to and they can be used only when the treatment under study is Many new therapies, for example monoclonal antibodies directed against cell receptors (so-called biologics) andgene therapy, are aimed at producing a permanent responseor remission [14–17]. These treatments cannot be studiedwith crossover designs. Other study designs, such as therandomized responder [18] and randomized withdrawal de-sign [19], enroll subjects who have previously shown atreatment response in an open, single-arm phase. Two re-cent studies evaluating biologic treatments for childhood ar-thritis have used the randomized withdrawal design becauseit was felt by the investigators that a placebo controlledstudy would be perceived as being unacceptable by enroll-ing physicians and by patients [20,21]. This design, whileapparently acceptable, does not provide the same quality ofinformation as an RCT, and may require more subjects;only those that show an initial response are entered into therandomized portion of the study.
Because of the limitations of current research designs for evaluating treatment efficacy in the context of rare diseaseslike childhood arthritis, a new study design was evaluated[22]. This design, called the randomized placebo-phase de-sign (RPPD), was developed to study remission-inducing(disease-modifying) therapies using survival endpoints. Allsubjects will receive active treatment is such a study design.
This may lead to greater study acceptance and, in turn,greater recruitment. We describe the features of the RPPDand its usefulness for the study of rare disease, such aschildhood arthritis, by means of computer simulations.
2. Development of the randomized placebo-phase design
We reasoned that the most acceptable clinical trial design would be one in which either the fewest subjects were as-signed to the placebo treatment or subjects were assigned tothe placebo treatment for only a short time. The RPPD fol- Fig. 1. Features of the randomized placebo-phase design (RPPD) trial. (A) lows the second strategy. It belongs to the class of designs Overview of the RPPD. The vertical bars represent the start and finish that includes the RCT in which the assignment of subjects is dates of an RPPD clinical trial. The horizontal arrow indicates the direction random and masked from subjects and assessors to reduce of time. Each horizontal line represents one study subject. The triangles bias. But, in an RPPD, unlike an RCT, all patients receive signify the time when each subject starts the experimental therapy. Thesolid lines represent the time the subjects spend taking the experimental the experimental therapy. It is the time from the enrollment therapy. Subjects are followed until they respond (closed circle). (B) Rep- in the study to the commencement of the experimental treat- resentation of an actual RPPD trial. In actual RPPD trials, subjects enter ment that is randomized in the RPPD.
the trial at various times in the accrual phase. Subjects are randomly The design of the RPPD assumes that a response occurs assigned a period of time on placebo treatment (broken line). At the ran- some time after an effective treatment is begun (during domly determined time subjects blindly switch to active experimental ther-apy (triangles). Subjects who do not respond during the trial (third, sixth which time the treatment effect takes place). Thus, if a ther- and eighth subjects from top), and those who drop out (fourth subject from apy is truly effective, those subjects who begin it sooner top) are censored. Some subjects may respond spontaneously while still on should, on average, respond sooner. Figure 1a demonstrates B. Feldman et al. / Journal of Clinical Epidemiology 54 (2001) 550–557 The design shown in Figure 1a is susceptible to measure- first set of simulations we studied a highly potent treatment, ment bias; subjects and investigators, knowing which subjects typical of the biologic treatments used in arthritis, that produces started treatment sooner, may be more likely to think that there a reliable and often relatively rapid response [21]. The second is a treatment response sooner than if treatment was started late.
set of simulations studied a therapy of moderate potency, also In the RPPD, this is limited by blinding subjects and investiga- seen with biologic treatments. In the third set of simulations, we tors. This blinding is accomplished by starting all subjects on used a treatment of intermediate potency. An example of this an identically appearing and tasting placebo that is switched to sort of treatment would be methotrexate for the treatment of active treatment at the randomly determined time. Subjects and childhood arthritis [24]. Finally, we studied a low potency treat- investigators are unaware of when the switch takes place. Some ment, to which the response is highly variable and may take a subjects may be assigned a placebo phase length of 0: they start long time, similar to gold in the treatment of arthritis [25].
the study taking active treatment. The random duration of theplacebo phase gives the RPPD its name.
The statistical power of the RPPD would be maximized Subjects were enrolled in RPPD trials as described.
if the placebo phase length was limited to two values There was a fixed accrual period. Each subject was then (namely, 0 and the maximum allowed length). However, to randomly assigned a placebo duration, after which therapy preserve blinding there may be situations when subjects with the experimental agent was begun. Subjects were then should be randomly assigned to a placebo phase that might followed until a defined response was achieved, they dropped out, or until the trial ended.
During such a clinical trial (represented by Figure 1b) We assumed a survival (time-to-event) endpoint. We subjects would be recruited at various times after the trial have not evaluated the RPPD for continuous outcomes. It start date. The time taken to respond to active treatment was assumed that the time until response followed an expo- would not be fixed, but would vary from one subject to the nential distribution. The exponential distribution is com- next. Some subjects would be censored; that is, they would monly used to model time-to-event data [26] including time drop out before they respond or finish the trial without re- to treatment responses and time to developing adverse ef- sponding. Drop out might occur completely at random, or fects from medications. The exponential distribution of the might be related in some way to the treatment given, or to time to response assumes that the probability of a subject re- the observation process (see discussion below). In the sponding at any time (assuming he or she has not yet re- RPPD, a Cox proportional hazards regression [23] is used to sponded) remains constant for the length of the trial. It is not determine the statistical significance of the observed treat- known how often this assumption holds true for new experi- ment effect. The dependent variable is the time from the en- mental treatments. However, there is some evidence that try into the study to the time of a response to the treatment.
treatment responses in pediatric rheumatic diseases can be The independent variable is the time from the entry into the adequately characterized by the exponential distribution study to the time of starting experimental therapy, in other [22]. For example, a recent study of a biologic agent used in words, the length of the placebo phase. The length of the the treatment of childhood arthritis produced responses that placebo phase will predict the overall time to a response, if followed an exponential distribution [21, M. Lange (Immu- 3. Characterization of the RPPD
The simulation program was written in the SAS pro- gramming language (version 6.12). All simulations were done on a Digital DEC 5000 minicomputer. Simulation re-sults were analyzed with DataDesk 6.1 [27].
To determine how efficient, how powerful, the RPPD de- sign is, we compared RPPD trials with standard, parallel- 3.2.4. Number of iterations and sample size arm RCTs, using a Monte Carlo computer simulation.
Each simulation run consisted of 500 iterations, or 500 Under the conditions of our assumptions, we hypothe- sized that the RPPD would be less powerful than the RCT if The sample size for each RPPD clinical trial was varied full recruitment into the RCT occurred. Because our simula- tions assumed that the treatment–response times would beexponentially distributed (see below), we hypothesized that 3.2.5. Accrual phase and length of trial the RPPD would approach the RCT in power for the study In a typical clinical trial, subjects are accrued over a fixed period early in the study. In these simulations, the ac-crual phase was kept constant at 90 days and the total trial We simulated four types of therapies that might apply to the In an RPPD trial, subjects are randomly assigned to a treatment of rare diseases, such as childhood arthritis. In the varying duration of placebo therapy before starting active B. Feldman et al. / Journal of Clinical Epidemiology 54 (2001) 550–557 therapy. For this study, individual subjects were randomly assigned a placebo phase length of 0 or 60 days with equal For the baseline simulations it was assumed that no drop- probability. To characterize the loss of statistical power as- outs occurred. We then repeated the simulations under the sociated with allowing the placebo phase to take on a assumption that an average of 10% and 20% of the subjects greater number of values, we repeated the simulations and dropped out before a response was seen. Missing data in the randomly assigned subjects to placebo phase lengths of 0 to form of dropout can be classified as completely random dropout, random dropout or informative dropout [28]. Inour simulations, subjects dropped out in a completely ran- 3.2.7. Median time to a response, untreated dom manner. In an actual clinical trial, the dropout process In some diseases, such as arthritis, subjects may have a may in fact be informative necessitating a more complex spontaneous response, without specific therapy. This phe- nomenon was accounted for in the assumptions. We used aconservative value of a median time to spontaneous re- sponse of 300 days (a baseline daily hazard of 0.0023). Un- Each simulated trial was analyzed with the Cox propor- der this assumption about 20% of the subjects will have a tional hazards regression [23]. The dependent variable was spontaneous response within 3 months. This is similar to the the time from entry into the trial until the time when a re- placebo response seen in many arthritis clinical trials.
sponse occurred. The independent variable was the lengthof the placebo phase. Subjects who did not respond by the 3.2.8. Median time to a response, treated The median response for the highly potent treatment was The Cox regression yields a likelihood-ratio statistic, assumed to be 7 days (a treated daily hazard of 0.099) and which, when the treatment has no effect, has a chi-square for the moderately potent treatment 14 days (hazard of distribution with 1 degree of freedom. A value greater than 0.050). The intermediate potency treatment was assumed to 3.841 is critical for an alpha-error (a false-positive) proba- bring about a response at a median of 42 days (treated daily bility of 0.05. Therefore, a trial was considered positive if hazard of 0.017) while the low potency treatment had a me- those randomized to be treated sooner were observed to re- dian response time of 150 days (hazard of 0.0046).
spond sooner, and the resulting likelihood-ratio statistic was Fig. 2. The power curves for the RPPD. The y-axis represents the power (1-B) expressed as a percentage. The x-axis represents total sample size on a logarith-mic scale. Each of the four curves represents simulations of treatments of different potency as described in Methods.
B. Feldman et al. / Journal of Clinical Epidemiology 54 (2001) 550–557 greater than or equal to 3.841. The validity of this cut-off was confirmed in a previous simulation study [22] by the calculation of the fraction of false-positive trials when an experimental therapy of no effect was simulated.
Power (1 Ϫ beta) was calculated as the fraction of trials (out of 500) in each simulation run that was positive. For each simulated therapy, the results of simulation runs were plotted against sample size to develop power curves.
The power of RPPD simulated studies was compared with the power of RCTs. RCT scenarios used the same as-sumptions and same total sample size as the RPPD simula-tions, but the subjects were randomized into treatment andplacebo arms with equal probability. The power of the intermediate potency treatment is studied, and about 240 sub- RCTs was determined with standard calculations (the time jects to reach a power of 0.80 for the low potency therapy.
to a response in a parallel-group two-arm placebo-con- Table 1 displays the required sample size to reach a trolled trial analyzed with the log-rank test) [29].
power of 0.80 and 0.90 for each simulated therapy and forthe corresponding parallel arms RCT. As hypothesized, theRCT is more powerful, a difference that becomes moremarked with less potent treatments.
4. Results
The effect of a 10% and a 20% dropout rate is displayed The power curves for the RPPD are shown in Figure 2.
in Figure 3 for the highly potent treatment. Under our as- For a highly potent therapy the RPPD reaches a statistical sumption of completely random dropout, the RPPD is quite power of Ͼ0.80 with seven subjects. The statistical power drops off with less potent therapies. For example, the RPPD Figure 4 shows the corresponding power curves for the requires about 31 subjects to reach a power of 0.80 when the RPPD when the placebo phase is allowed to vary between 0 Fig. 3. The power curves for the RPPD studying a highly potent therapy (see Methods). The y-axis represents power expressed as a percentage. The x-axisrepresents total sample size. The solid line represents the baseline case. The other lines represent simulations in which 10% and 20% of subjects drop out onan average.
B. Feldman et al. / Journal of Clinical Epidemiology 54 (2001) 550–557 and 60 days. There is a marked loss of statistical power variability from a small amount of experimental, or random, more apparent for treatments of lower potency.
In contrast, highly potent treatments with a very rapid onset have much less variance in response times. Thiswould suggest that the RPPD might be more useful in the 5. Discussion
study of treatments such as analgesics, antibiotics, and bio- We found that the RPPD clinical trial was able to yield logics, which exert their effects rapidly. Even with highly positive results when experimental therapies of varying effi- potent treatments an RCT would require a smaller sample cacy were studied. These results validate the concept of a size than an RPPD; the decision to implement an RPPD trial treatment trial in which those subjects who are treated would depend on the perceived acceptability of a standard sooner are expected, on average, to respond sooner than We believe that in special circumstances the RPPD In addition, our simulations show that the power of the should be more acceptable to patients, physicians, and in- RPPD, while adequate for highly potent therapies, may not vestigators. In this design, no subjects are required to take a be adequate for therapies that have a more variable result placebo for more than a relatively short time. All subjects, and a longer average time to response. These results were therefore, know that they will receive the experimental predictable, given the assumptions underlying the simula- treatment; furthermore, physicians’ ethical misgivings tions. We assumed that the response to treatment would fol- about RCTs, whether theoretically correct or not, are al- low an exponential distribution (i.e., would be characterized layed. This improvement in the acceptability of the study by a constant conditional probability of a response). The design should mean greater accrual. At this point, the variance of response times under the exponential distribu- greater acceptability of this new design, while reasonable, is tion is the square of the mean response time [26]. Therefore, speculative. Only practical application will be able to deter- the variance in response times was much larger for those mine whether accrual is truly enhanced.
treatments that tended to take a long time to achieve a re- The RPPD might be considered early in the study of new sponse. In our studies of low and intermediate potency ther- treatments. Currently, in new treatment development, the apies, we were trying to predict a large amount of response earliest studies are often open-label case-series. In the Fig. 4. The power curves for the RPPD. The y-axis represents the power (1-B) expressed as a percentage. The x-axis represents total sample size on a logarith-mic scale. Each of the four curves represents simulations of treatments of different potency as described in Methods. In this set of simulations the randomlyassigned placebo phase was allowed to vary anywhere from 0 to 60 days.
B. Feldman et al. / Journal of Clinical Epidemiology 54 (2001) 550–557 RPPD design the assignment to the different lengths of the a useful method for studying new therapies, especially as an placebo phase is random to limit bias. Likewise, measure- alternative to open, uncontrolled trials.
ments of the response to therapy are blind to the knowledgeof the length of the placebo phase. In these ways, the RPPD Acknowledgments
is more rigorous than, and should be preferable to, the case-series design.
We gratefully acknowledge Dr. Colin MacArthur for his These advantages are offset by a decrease in statistical critical review of our manuscript. This article was prepared power and, more importantly, by limitations in the ability to with the assistance of Editorial Services, The Hospital for draw inferences about the size of the treatment effect.
Sick Children, Toronto, Ontario, Canada.
In our simulations, the RPPD was always less powerful This work was presented in part at the American College than the two-arm placebo-controlled RCT with the same to- of Rheumatology Annual Meeting, San Francisco, 1995.
tal sample size; this difference was greater with treatmentsof low potency. Likely, the advantages of the RPPD,namely, potentially greater acceptance and higher accrual, References
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