Randomized Discontinuation Trials Utility

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J Cltn Ep&miolVol.46, No. 9, PP.959-971, 993Printed n G reat Britain.All rights eserved 0895-4356/936.00 0.00Copyright 1993 ergamon ressLtd

RAND OMIZED DISCONTINUA TION TRIALS: UTILITYAND EFFICIENCY

JACEK A. K OPEC,* MICHAL ABRAHAM OWICZ~ and JOHN M. ESDAILE~Department of Epidemiology and Biostatistics, and Divisions of Rheum atology and ClinicalEpidemiology, Department of Medicine, Montreal General H ospital, McGill University, Montreal,Quebec, Canada H3G lA4

(Received in revised form 14 April 1993)

Abstract-T he random ized discontinuation trial (RD T) is a two-p hase trial. In phas eI all patients are openly treate d w ith the medication being evaluated. In phas e II, thos ewho have responded are randomly assigned to continue the same treatment or switchto placebo. Usually, non-compliers and adverse reactor s identified in phas e I areexcluded from phase II. To investigate the value of this design, we reviewed theadvantages and limitations of discontinuation studies, and compared the RDT designto the classic randomized clinical trial design in terms o f clinical utility and efficiency(sample size). A computer model was used to study the efficiency of the two designsunder a broad range of assumptions.

The RD T design is particularly useful in studying the effect of long-term, non-curativetherapie s, especially w hen the clinically im portant effect is relatively sm all, and the useof placebo should be minimized for ethical or feasibility reas ons. How ever, its use islimited if the objective of an investigation is to estimate the magnitude of absolutetreatment effects and tox ic effects in the source po pulation, or to evaluate a potentiallycurative treatm ent. Our results indicate that selecting respon ders prior to randomizationhas a very strong e ffect on the relative efficiency of the trial. Furthe r improvem ent maybe achieved by excluding non-compliers and adverse reactors. Under the assumptionstested in our model, the sample size required in phase II of an RDT was only 2 0-50%of that in a classic trial.EpidemiologyEfficiency

Statistics Clinical trials Research design Sample size

INTRODUCTIONThe methods of randomized discontinuation(withdrawa l) trials (RDT) have been used in*Research fellow of the National Health Research andDevelopment Program of Canada.TResearch Scholar of the Montreal General Hospital Re-search Institute.$Senior Research Scholar of the Fonds de la recherche enSante du Quebec and V isiting Professor of Medicine,Department of Rheumatology and Immuno logy, Har-vard Medical School, Brigham and Womens Hospital,

Robert B . Brigham Multipurpose Arthritis and Muscu-loskeletal Disease Center, Boston, MA (grants AR36308, AI 07306 and AR 07530).Requests for reprints should be addressed to: Dr John M.Esdaile, Division of Clinical Epidemiology, MontrealGeneral Hospital, Montreal, Quebec, Canada H3G 1AY.

clinical research for two decades. The designwas first described by Amery and Dony [l] in1975, as a method of minimizing the durationand degree of patient exposure to placebo indrug efficacy studies. In the RDT, in contrast tothe classic randomized clinical trial (RCT), onlythose patients who appear to improve whentreated w ith the medication under study (theresponders) are selected for the second, ran-domized phase (Fig. 1).The responders can be identified in two ways.One approach is to give the treatment to alleligible patients for a short period of time priorto randomization (the so-called run-in period).Alternatively, the response among p atients

95 9


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96 0 JACEKA. KOPECet al.treated with the medication of interest in normalclinical practice, sometimes for many years, isevaluated retrospectively. During the openphase, non-compliers and those developingserious adverse reactions are usually excluded.In the second phase, which resembles a tra-ditional, double-blind randomized controlledtrial, the responders are randomly assigned tocontinue the same treatment or switch to pla-cebo. After a suitable period of time, the twogroups are compared in terms of response, orrelapse rates.

Quitkin and Rab kin [2] discussed the utility ofthis design in clinical research in psychiatry andsuggested that it may be particularly suitable forstudying new drugs. They also stated that thedesign is less likely to result in type II errors(false acceptance of the null hypothesis) than theclassic design. Friedman et al. [3, p. 451 pointedout that because a highly selected sample isevaluated, this design can overestimate benefitand underestimate toxicity. These authors alsoobserved th at in discontinuation trials the samegeneral standards should be adhered to that areused with other designs.

Recently, the concept of excluding no n-responders, non -compliants and adverse reac-tors prior to randomization has been discussedby Knipschild et al. [4], in a broader context ofdealing with certain comm on problems in thedesign, analysis and ethics of clinical trials.These authors suggested that a prerandomiza-tion qualification period can be used to ident-ify suitable baseline characteristics in theadmitted patients, adjust the dose of medi-cation, remove placebo responders, determinespecial therapeutic stratifications, and improvethe ethics of informed consent.

The RDT design has been applied to assessthe efficacy of a number of medical interven-tions [5-331. Yet compared to the classic design,it has been used relatively infrequently, and onlyrecently has gained some popularity. Apartfrom its application in efficacy trials, the RDTapproach has been employed to investigate the

PHASE I

optimal d uration of therapies known to beeffective [34-391, and to assess the so calledrebound effect after treatment withdraw al[4@-44].In this paper we are concerned with the useof the RDT design in studies of efficacy,where it can often be considered an alternativeto the classic RCT. In the first part, wereview the advantages and limitations of thisdesign, with an emphasis on its clinical utility.Next, we compare the RDT d esign with theclassic, one-phase RCT in terms of efficiency.Technical de tails, including the formulas forsample size calculation, are provided in theAppendix.

CLINICAL UTILITYDue to the selection of responders prior to

randomization, the difference in response ratesbetween the treatment and placebo groups ob-served in phase II of a discontinuation trialcannot be generalized to the source populationof patients with a given condition, eligible forphase I. It is intuitively rather obvious that thisdifference will generally be larger tha n thatobserved in a classic trial conducted in the samesource population. (Later, we shall discuss con-ditions under which this is true). This apparentselection bias has been viewed by someauthors as a major limitation of the RDT design[3]. However, others have argued that thosesubjects who appear to respond to initial, opentreatment are more likely to receive the medi-cation of interest in normal clinical practice [I].Therefore, the effect observed in this group maybe more meaning ful. For example, in terms ofday-to-day decision makin g, knowing that 80%of patients with rheumatoid arthritis who seemto respond to initial treatment with a new drugmay be expected to improve in the long run (asopposed to, say, 40% on placebo), is at least asinteresting to a clinician as knowing what pro-portion of all patients with rheumatoid arthritisare likely to improve (say, 30% on the drug and

PHASE IISame

f Treatment___._+ Relapse orNo Relapse

SourcePopulation 7 R c Placebo - Relapse orExclusions

No Relapse(N o e s p o n s e , No Com p l i a n c e , T o x i c i t y )

Fig. 1. Schematic representation of the randomized discontinuation trial (RD T) design.


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Randomized Discontinuation Trials 96 120% on placebo), even if the number of initialresponders is relatively low .

Even though the quantitariue result from anRDT does not generally apply to the samepopulation as the result from a classic trial, thequalitative result (i.e. whether or not the treat-ment has any effect at all) does. A statisticallysignificant difference in response rates in phaseII provides evidence that there are some patientsin the source population for whom the treat-ment is effective. In that sense, the RDT designand the classic randomized trial design can,under very broad a ssump tions, be regarded asalternative methods of addressing the samequestion. Furthermore, under some specific as-sumptions to be discussed later, the estimate ofrelative effect (response rate ratio) obtained in adiscontinuation study could also be generalizedto the source population.There are a number of limitations in theapplication of discontinuation studies that donot apply to classic, one-phase randomizedclinical trials. The RDT design cannot be usedto evaluate a definitive irreversible treatment,such as a surgical intervention. In studyingother forms of therapy, a negative resu lt of anRDT may be due to a permanen t, curative effectof treatment in a substantial number of subjects,rather than the lack of any clinically significanteffect. A negative result may also occur if themedication under study has a short-term ben-eficial effect but fails to provide an effectivemaintenance therapy. Although for many dis-eases and treatments, particularly drug thera-pies in most chronic conditions, both situationsseem unlikely, these alternative explanations ofa negative result should always be kept in mind.

A positive response to treatment initiation ina symptomatic patient may involve a differentbiological m echanism than a relapse observedafter treatment withdraw al. In particular, if thewithdraw al of a given medication is likely toproduce a strong rebound effect, distinguish-ing between this effect and reemergence of thenatural disease process m ay be difficult. Forexample, in a study of low-dose prednisolone inrheumatoid arthritis [45], a flare occurring aftersudden discontinuation of therapy w as inter-preted as demonstrating low-dose steroidefficacy. However, others argued that the resultswere more likely to reflect steroid withdrawalsymptoms [46]. Problems of this type may oftenbe avoided by tapering the dose of the drug asopposed to abruptly withdraw ing the medi-cation. Nevertheless, som e understanding of the

biological me chanism involved may be helpfulin interpreting the results of discontinuationtrials.

Quantitative assessme nt of treatment toxicityin the randomized phase of a discontinuationstudy is limited, since most subjects prone toadverse reactions are eliminated in phase I. Asa result, the rates of adverse reactions in thetreatment and placebo groups, as well as thedifference between them, w ill generally be lowerthan in the source population. On the otherhand, the observed rates will apply to thosepatients who are most likely to receive thetreatment over a long period of time.

It has been suggested [47,48] that effectiveblinding in the randomized phase of a trial maybe more difficult to achieve if the patients havealready been exposed to the active treatment orplacebo. In most studies which used the RDTdesign the effectiveness of blinding was notreported, but at least in one study [31] theauthors found that blinding was successful.Nevertheless, the hypothetical risk of unblind-ing may explain the reluctance on the part ofsome researchers to use this design.The RDT design may sometimes be appli-cable in situations where the classic randomizedtrial might be considered unfeasible for ethicalor logistic reasons. The design allows allpatients to obtain any beneficial effect thatmight result from the initial treatment, thusimproving cooperation from both patients andphysicians. A good example is a study of hy-droxychloroquine in systemic lupus erythemato-sus [31]. Although prior to that study the drughad never been conclusively proved to be effec-tive for this disorder, it had been widely used byphysicians and w as believed to have a beneficialeffect. At this stage, randomizing patients withsymptomatic systemic lupus erythematosus toactive drug versus placebo was unacceptable tomany physicians and patients. How ever, neitherpatients nor physicians objected to a randomwithdraw al of treatment among the respon-ders. A randomized discontinuation trial wasthen conducted to demonstrate the efficacy ofthe drug.The design could prove particularly valuablein testing new drugs, as suggested by previousmethodological studies [l, 21. In early stages ofdrug evaluation, open treatment is routinelyused to establish the optimal dose level and tolook for obvious side effects. In a selected groupof responders, the initial treatment could befollowed by a randomized discontinuation


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phase. Such an approach might provide strongevidence of drug efficacy at a relatively low cost.It should be stressed, however, that the possi-bility of a curative effect or a short-term effect(when the results are negative), an d withdrawalsyndrome (when the results are positive)should alw ays be taken into account whendiscontinuation studies are used to evaluate newdrugs.

EFFICIENCYSince selecting patients who are more

likely to respond to a given treatment tendsto increase the difference in response rates, itwill also impro ve the efficiency of the trial.Thus a discontinuation trial conducted amonginitial responders may be expected to requirea smaller sample size than a classic trial ofthe same power, carried out in the generalpopulation of patients. Hallstrom et a l . [49]studie d the relative efficiency of a mod ifiedRDT design, referred to as a predoseddesign, employed in the Cardiac ArrythmiaSuppression Trial [28]. These authors con-cluded that selecting responders may have avery significant impact on the required samplesize and strongly recommended the use of thisdesign.The efficiency of a trial may be furtherimproved by identifying and eliminatingpotential non-com pliers and adverse reactorsprior to randomization. The effect of non-compliance on the required sample size wasstudied by Shork an d Rem ington [50] andHalperin et a l . [51]. Probstfield [47], Lang [52]and Knipschild et a l . [4] discussed the role ofprerandomization screening procedures in im-proving compliance in clinical trials. Brittainand W ittes [48] investigated the effect of misclas-sifying subjects with respect to complianceduring a run-in period on the efficiency of atrial. These authors concluded that the run-inperiod is most effective when there is a highproportion of poor com pliers and a low rate ofmisclassification.In a discontinuation trial, patients who do notcomply w ith the treatment or experience seriousadverse reactions are usually eliminated duringthe initial open phase. This should improve theefficiency of the study over and above what hasbeen achieved by excluding non-responders. Itshould also reduce the bias in the estimate oftreatment effect among those patients who in-itially respond to the treatment.

Genera l mo de lWe used a computer model to compare thesample size required in a discontinuation trial

and in a classic one-phase trial, under equivalentassump tions. The following factors that mightaffect the samp le size have been taken intoaccount: (1) true response rates on placebo a ndon active treatment in the source population; (2)frequency of non-compliance and adverse reac-tions in that population; (3) accuracy of identi-fying three categories of patients in the initialphase of the trial: responders, compliers andtolerators (those who do not experience seriousadverse reactions).

For the comparison between the two designsto be valid, both trials must refer to the samesource population of patients, representing thedomain of interest in terms of standard eligi-bility criteria, such as the diagnosis, treatmentindications and contra-indications, demo-graphic characteristics, etc. The difference isthat in the classic trial all subjects who agree toparticipate are randomized to receive activetreatment versus placebo, w hereas in the discon-tinuation trial only those deemed eligible afterthe initial open treatment are randomized. Ouranalysis is restricted to trials in which treatmentefficacy is measured against placebo rather thanagainst another active intervention, and theoutcome of interest is defined a s a dichotomousresponse to treatment. It may be noted that thismodel applies not only to discontinuation trialsbut to any trial in which subjects are selectedbased on their initial response.

The results presented in this paper are ob-tained under some additional assum ptions.First, we assum e that the treatment does nothave any permanen t, curative effect. In otherwords, patients who respond to active treatmentwill relapse in phase II if the treatment isdiscontinued. We refer to these patients asactive responders. Furthermore, we definespontaneous responders as patients who im-prove, and remain in remission, independentlyof the treatment they are given. We assum e thatthe proportion of spontaneous responders onactive treatment is equal to the proportion ofplacebo respo nders in the same population (i.e.placebo response is not prevented by activemed ication). Finally, the accuracy of identifyingactive responders in phase I is assum ed to be thesame as the accuracy of identifying spontaneousresponders. Although d epartures from theseassump tions may occur in actual trials, they are


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Randomized Discontinuation Trials 96 3difficult to predict given the paucity of empiricaldata on the natural history of many chronicconditions. We shall examine some effects ofserious violations of these assumptions in a latersection of this paper.

The relative sam ple size (RSS) is calculated asthe ratio of the sample size required in a discon-tinuation trial to that in a classic trial. Thus therelative efficiency of the RDT design can bedefined as l/RSS. The sample sizes are based onthe standard, approximate formula for a differ-ence between two proportions [53]. The pro-portions of responders (response rates) on activetreatment and placebo in the randomized phaseof a trial, den oted as r and r,,, respectively, arecalculated using the formulas derived in theAppendix. In all sample size calculations wetake the probability of type I error a = 0.05(two-sided), and the probability of type II error/I = 0.20 (80% power).Ef lec t o f exclu d i ng non responders

It is useful to consider a situation in which therates of non-compliance and adverse reactionsin the source population are zero and there isperfect agreement between the response ob-served in phase I and phase II. Under theseassump tions the response rate in the treatmentgroup of an RD T will be r = 1 O, or 100% (sinceonly responders are selected for phase II), andthe response rate in the placebo group will ber , , = RJR, were R , an d R are, respectively, theresponse rates on placebo and active treatmentin the source population. Note that the differ-ence r d = 1 - R,, , lR s larger than the differenceRD = R - & observed in a classic trial, if1 > R >RQ .

The assump tion of a perfect agreement be-tween treatment response in phase I and phaseII is unrealistic. Published data indicate that inmost trials there will be some patients whoappear to respond to the initial open treatment,but turn out to be non-responders in the secondrandomized phase [6, 7, 9-16, 18, 21-23, 26, 27,30-333. If the results of phase II are considereda gold standard, those patients w ho appear torespond in phase I but fail to respond in phaseII may be referred to as false responders. Simi-larly, some of the true responders may bemisclassified as non-responders in phase I andexcluded from the randomized phase of thetrial. Thus it may be useful to treat the initialassessme nt of response like a diagnostic testwith certain sensitivity and specificity, relativeto the results that would have been observed in

phase II had all subjects been admitted to thatphase. Then the expected absolute effect oftreatment in phase II can be calculated as (seethe Appendix):

r d = r - rO= (R -R , )SE,

(SE , ) (R)+( l -SP , ) ( I -R ) ( )where SE , an d SP , are the sensitivity and specifi-city of identifying the responders in phase I.Both SE , an d SP , are treated in a deterministicrather than stochastic fashion.

It can be shown that r d is greater than RD ifSE, > 1 - SP,, i.e. as long as selecting respon-ders on the basis of results obtained in phase Iis better than random selection. However, ifRD = 0 then r d = 0 as well. This demonstratesthat qualitatively the assessm ent of treatmentefficacy in an RDT is valid for the sourcepopulation (as we stated previously), and ispractically always more efficient than in theclassic trial. Quantitatively, the absolute effect(rate difference) can only be generalized to thepopulation of initial responders. The relativeeffect (rate ratio), on the other hand, remainsthe same as in the source population as long asthe assump tion of equal selection probabilitiesfor active and spontaneous responders holds.The rate ratio will be inflated if active respon-ders are selected with higher probability thanspontaneous responders, and it will be reducedif the reverse is true.

The exclusion of non-responders, even if notcomp lete, has a very strong effect on the relativeefficiency of the trial. The gain in efficiency isparticularly dramatic for small treatment effectsand low placebo response rates (Fig. 2). Forexample, assuming 80% sensitivity and 80%specificity of the criteria for identifying respon -ders, the sample size in a discontinuation trialmay be only 30% of that in a classic trial.Figure 3 show s that im proving the specificity ofthese criteria may significantly reduce the rela-tive sample size, whereas the sensitivity of select-ing responders has much less effect. This isunderstandable, given that the proportion offalse responders among those admitted to thesecond phase depends on the specificity of se-lecting responders to a much greater extent thanon its sensitivity.N on - comp l i an ce and adv er se reac t i o ns .

In this section we examine the effect of ex-cluding potential non-com pliers and dropouts


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90%-

80%-RFi=relative response rate

80%-

20%, I I I / I I1 I 80 I I I 81 I I IV I I I I I I I I II I1 I I s I0.1 0.2 0.3 0.4 0.5 0.8 0.7 0.8REFERENCE (PLACEBO) RESPONSE RATE

IFig. 2. Sample size required in an RDT relative to that in a classic RCT (in X), for three different relativeresponse rates in the source population: 1.2, 1.5 and 2.0. The frequencies of non-compliance and adversereactions are assumed to be zero, and the sensitivity and specificity of identifying responders are assumed

to be 0.8.

due to advers e reactions on the relative compliance; (3) advers e reactions are equallyefficiency of the discontinuation design. To commo n in the treatment and placebo groups;avoid an excessiv e number of arbitrary par- (4) withdrawals due to adverse reactions are notameters , the following additional assump tions included in the final analysis; (5) respond ers,will be made: (1 ) respons e rate in the placebo compliers and tolerators are selected indepen-group is not affected by non-compliance (no dently in pha se I. We recognize that in manycontamination of the control group); (2) re- trials som e of these assump tions may be vio-sponse rate among spontaneous responders (in lated to a varying deg ree. Howev er, both theor-the treatment group ) is not affected by non- etical considerations and the results of our

90%80% SE=sensitivity of identifying respondersSP=specificity of identifying responders1E:;;::yi=0%-

4k 30%- SE=0.9 SP=O.7SE=0.7 SP=O.9

14 %E=SP=O.OO%m I I 1 I 1 I I I 1 I I I I I I I I,,,,,, I I,0.1

&:ERENCE0.;LACEB:j4RESPONifi RATE0.8

Fig. 3. Sample size required in an RDT relative to that in a classic RCT (in %), for different sensitivitiesand specificities of identifying responders. The relative response rate is assumed to be 1.5, and the

frequencies of non-compliance and adverse reactions are assumed to be zero.


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Randomized Discontinuation Trials 96 5

NR excluded60%-

Ii NR+AR excl.z 70%-32 60%- NR+NC excl.;5>!=5 =-

NR+AR+NC excl.

l o% , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , , ,0. 1 0.2 0.3 0.4 0.5 0.6 0.7 0.6 0REFERENCE (PLACEBO) RESPONSE RATE

I-.9

Fig. 4. Effect of excluding non-compliers (NC), adverse reactors (AR) or both, in addition tonon-responders (NR), on the sample size required in an RDT relative to a classic RCT (in %). The relativeresponse rate is assumed to be 1.5, the frequencies of non-compliance and adverse reactions in the sourcepopulation are both assumed to be 0.2 and the sensitivities and specificities of identifying responders,

compliers and tolerators are all assumed to be 0.8.

sensitivity analysis (data not provided) suggestthat these violations are unlikely to have anysubs tantia l effect on the relative efficiency of theRDT design. For the sake of clarity, moretechnical aspects of the model are discussed inthe Appendix.

If the frequency of non-compliance and thefrequency of adverse reactions are similar, ex-cluding non-compliers has a somew hat strongereffect on sample size than excluding adversereactors (Fig. 4). W hen both frequencies areassumed to be 0.2, excluding these two groupsof individuals with 80% sensitivity and 80%specificity m ay reduce the relative sample size bymore than 30%. Given that non-respondershave already been excluded w ith a fairly goodaccuracy, the sample size required in a discon-tinuation trial may be less than 20% of that ina classic trial of similar power (Fig. 4). As therates of non-compliance and adverse reactionsin the source population increase, the samplesize gets smaller relative to that in a classic trial(even though the actual number of subjectsrequired for each type of study will, of course,increase). For exam ple, if both rates were 0.3,the relative sample size could be reduced by asmuch as 50-60%.D epa r t u r e s f r om as sump t i o n s

Amo ng the assump tions of the model dis-cussed in the previous sections, the most critical

is the assump tion that the treatment does nothave a permanent effect. If some of the activeresponders are cured in phase I, the observedresponse rate on placebo will increase (relapserate w ill decrease) and the efficiency of the studywill be reduced. The relationship between therelative sam ple size in a discontinuation trialand the rate of curability in phase I for twolevels of treatment effect is presented in Fig. 5.It is noteworthy that the RD T design is moreefficient than the classic design even if a substan-tial proportion of the subjects are cured, es-pecially for low reference response rates andsmall treatment effects.

We also assumed that the sensitivities ofidentifying spontaneous and active respondersin phase I are the same. If, in fact, activeresponders are identified with a higher sensi-tivity than spontaneous responders (which inmost instance s seems more likely, especially ifthe initial phase is relatively short), the relativeefficiency of the RDT design w ill be furtherimprov ed. If the oppo site is true, the efficiencywill be reduced. This effect is shown in Fig. 6,where we consider two scenarios: selecting100% and 50% of spontaneous responders. Inboth cases we assum e that 80% of active re-sponders are identified. It seems clear that evenvery strong departures from the assump tion ofequal selection probabilities would not invali-date our conclusions,


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0% I I I I I 1 1 1 0 10:2

1 I I I I I I I I I I I0 0.1 0.3 0.4 0.5 0.6 0.7CURABILITY RATE

Fig. 5. Effect of disease curability on the sample size required in an RDT relative to that in a classic RCT(in %), for two relative response rates: 2.0 and 1.5. The reference response rate is assumed to be 0.2, thefrequencies of non-compliance and adverse reactions in the source population are both assumed to be 0.2,and the sensitivities and specificities of identifying responders, compliers and tolerators are all assumed

to be 0.8.

70%

60%-SE(S) =sensitivity of identii ing

spontaneous responders

lw 50%-Y!k3 40%-Wf$ 30%-a

20%-

10% < 3 I 31 11 3 10 10 0 1 10 10 I8 80.1 0.2 0.3 0.4 0.5 0.6REFERENCE (PLACEBO) RESPONSE RATE

Fig. 6. Sample size required in an RDT relative to that in a classic RCT (in %), for three differentsensitivities of identifying spontaneous responders: 1 O, 0.8 and 0.5 (specificity is assumed to be 0.8). Therelative response rate is assumed to be 1.5, the frequencies of non-compliance and adverse reactions areboth assumed to be 0.2, and the sensitivities and specificities of identifying active responders. compliers

and tolerators are all assumed to be 0.8.

Phase I samp l e si ze that needed for a classic trial. The question isparticularly relevant to those trials in which the

In a discontinuation study, only a fraction of first phas e is condu cted prospective ly, since theall subjects initially treated are admitted to the number of subjects available at the onset of therandomized phase. It is, therefore, important to study may be limited.ask whether the initial pool of candidates for the Our analysis show s that the initial num ber ofstudy (phase I sample size) has to be larger than subjects needed in phase I of an RDT tends to


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Randomized Discontinuation Trials 967140%-

SE=.sensitlvity of identifying espondenSP=specificily of identiiing responders

I! 100?6-z 90%-!!is 90?6-a9 70%-$ m-a

509b-

SE=0.7 SP-0.9

4096-n I I I 81 -1(I 11 1 I I0.1 0.2 0.3 0.4 0.5 0.6REFERENCE (PLACEBO) RESPONSE RATE

Fig. 7. The initial (phase I) sample size required in an R DT relative to a classic RC T (in % ), for differentsensitivities and specificities of identifying responders. The relative response rate is assumed to be 1 .5 andthe frequencies of non-compliance and adverse reactions in the source population are both assumed tobe zero.

be slightly lower than in a classic trial, if thesensitivity and specificity of the criteria foridentifying responders are above 0.7 (Fig. 7).Both sensitivity and specificity are important,but for different reasons. High specificity re-duces the numbe r of false responders and thusimproves the efficiency of phase II, whereas highsensitivity allows for a larger proportion of trueresponders to enter the second, randomizedphase. These results also suggest that the initialsample has to be larger than the sample neededfor a classic trial if the methods of selectingresponders are very inaccurate. The exclusion ofnon-compliers is likely to increase the requiredphase I sample size (data not provided), unlessthe sensitivity and, to a lesser degree, specificityof detecting these individuals in phase I are veryhigh.

DISCUSSIONIt is important to emphasize that the

results presented in this paper should be appliedwith caution. Our g oal was to develop a realisticand yet relatively p arsimonious model of theRDT design. In real life, some of the simpli-fying assum ptions built into the model w illnot hold exactly, and the actual values of theparameters needed to calculate the requiredsample size may be difficult to estimate withprecision. Nevertheless, if reasonable estimatesof these parameters can be obtained, the for-

mulas given in the Appendix should providea fairly accurate assessm ent of the responserates that might be expected in phase II of anRDT.

Our results indicate that in those situationswhere the RD T design is applicable, it may offera considerable advantage over the traditionalrandomized trial design. The design might beparticularly useful in studying the effect oflong-term, non-curative therapies, especiallywhen the clinically important effect is relativelysmall and the use of placebo should be mini-mized for ethical or feasibility reasons. It seemsreasonable to expect that identifying and elimi-nating non-responders in phase I may reducethe required sample size by at least 50% , de-pending on the reference response rate and theeffect of treatment. Further reduction maybe achieved by excluding non-com pliers andadverse reactors.

The relative efficiency of the RDT designdepends to a large extent on the accuracy(mainly specificity) of the selection criteria withrespect to treatment response and, to a some-what lesser degree, with respect to patient com-pliance and treatment tolerance. The sensitivityof these criteria becom es an important issue ifthe number of potential candidates for the trialis limited.The findings of a similar study conducted byHallstrom et a l . [49] appear to suggest that thegain in efficiency due to selecting responders


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968 JACEKA. KOPEC et al .

may be even larger than reported here. How-ever, to compare our results with those obtainedby Hallstrom et al., it is necessary to discussbriefly the differences between their model,based on the design of the Cardiac ArrythmiaSuppression Trial (CAST), and our model of atypical discontinuation trial.

In the CAST study, patients who appeared torespond to an antiarrthymic drug by showingsuppression of premature ventricular depo lariz-ations (the interim outcome) were subsequentlyrandomized to a continuation of the drug orplacebo. T hus the selection of responders wasbased on a very specific interim measure ofeffect, different from th e ma in outcom e of inter-est. In principle, this modification of the RDTdesign could be handled within the frameworkoffered in this paper. Hallstrom et a l . made anadditional adjustment for the possible loss of asmall proportion of subjects who may developthe primary outcome during the initial openphase. They also assum ed that the proportion ofpatients responsive to the interim outcome maybe slightly higher in a predosed study than ina classic trial. On the other hand, the resultsprovided by Hallstrom et a l . do not take intoconsideration the additional effect of excludingnon-compliers and adverse reactors during theinitial open treatment. It should also be notedthat these authors provide data that refer to theinitial number of subjects needed, rather thanthe number of subjects randomized. As wepointed out earlier, many discontinuation trialsinclude patients treated with the medication ofinterest in normal clinical practice. Since thesepatients have already been preselected in termsof treatment response, com pliance and toler-ance, we prefer to use the sample size needed forthe randomized phase in assessing relativeefficiency.A more impo rtant but not obvious differencebetween our model and that used by Hallstrome t a l . lies in +he assum ptions concerning thesensitivity and specificity of identifying respon -ders. In our model, these parameters are fixed ap r i o r i , and are allowed to take any values be-tween 0 and 1 (although we provide data foronly a few, selected v alues). By contrast, in theHallstrom et a l . model, the specificity and over-all sensitivity of the initial response in predictingthe primary outcome are determined by thereference response rate, the interim responserate on treatment and the ratio of the primaryoutcome rate among in itial responders to thatamong non-responders. However, these authors

make an implicit assumption that the sensitivityof initial response in identifying those patientswho will ultimately benefit from the treatment(active responders in our model) is 100% ,whereas spontaneous responders are selectedrandomly, i.e. with a sensitivity equal to theoverall proportion of subjects deemed respon-sive to the interim outcome and selected for therandomized phase. This explains the relativelylarge reduction in the initial sample size inHallstrom e t d s study, compared to our datapresented in Fig. 7.The above assum ption implies that the trueeffect of treatment with respect to the primaryoutcome is always mediated through the ob-served suppression of arrythmia. Although thismay seem plausible in the context of the CASTstudy, an analogous assump tion would bedifficult to justify in most discontinuation trials,in which specific tests of interim treatment effectare not available. Nevertheless, once all theabove differences in assum ptions are adjustedfor, the two models give exactly the same re-sults.Although our model was restricted to trials inwhich treatment efficacy is evaluated againstplacebo rather than against another activeintervention, the RDT design could also beused to compare two active treatments. To thisend, a group of patients would have tobe treated simultaneously with two differentmedications. Subsequently, those who appearto respond are randomized into discontinuationof one medication or the other. Since theselection of responders is unlikely to beperfectly ac curate, validity of this appro achhinges on the assump tion of equal selectionprobabilities for subjects responding to differenttreatments.

A final point relates to the problem of maxi-mizing the efficiency of a trial in a more generalcontext. In theory, the selection of subje ctscould be further refined by discontinuing activetherapy in all responders after a period of opentreatment, and randomizing only those whoinitially improved but relapsed during the dis-continuation phase. Since the ratio of active tospontaneous (placebo) responders sho uld bemuch higher among the responders-relapsersthan among initial responders, this approachwould seem optimal in providing qualitativeevidence of treatment efficacy while minimizingthe number of subjects to be randomized andexposed to placebo. However, it might proveimpractical, and the clinical utility of the quan-


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Randomized Discontinuation Trials 969titative result obtained in this way might belimited. 17 .Acknowledgements-The authors wish to thank Dr S.Shapiro for helpful comments on an earlier draft of thismanuscript, and Drs J. C. Bailar III and 0. S. Miettinen foruseful discussions about the topics addressed in this paper.This study was supported in part by grants from the 18.Arthritis Society of Canada, and the Natura l Sciences andEngineering Council of Canada.

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APPENDIXEffect of Excludi ng Non responders

If all subjects in the source population were admitted tophase II, the results of a discontinuation study could bedisplayed in the following 2 x 2 table (the results of phaseII are the gold standard):

TRUE RESPONSEYES NO

PHASE I YESRESPONSE NO

I I I

R 1-R 1.0In this table f , , z , 3 nd f 4 enote proportions and f , +his the proportion of subjects that would normally be admit-ted to-phase II of an RDT. Since the sensitivity of identify-ing responders in phase I is:

SE, =;,and the specificity is:

hSPr=(l-R)then,

f , h = W ) ( R) +( 1 - s pr ) U R) . (A.3)Thus the expected response rate in the treatment group is:

A Wr) CRr=m+fi )=(sE,)(~)+(l -sP,)(I -R) (A.4)

Let R, be the reference response rate, i.e. the proportionof subjects in the source population who respond (im-prove) spontaneously (i.e. when given a placebo), and& theproportion of spontaneous responders admitted to phase II.If we assumed the same sensitivity for identifying active andspontaneous responders, the expected response rate in theplacebo group of a discontinuation trial would be:

.fi (SE,) (R,)r =I fi+ f2)((SE,)(R)+(I -SP,)(l -R) (A5)

From equations (A.4) and (A.S), the expected absolute effectof treatment (response rate difference) in phase II is:

and the relative effect (response rate ratio) is:Rrr =y=RR, (A.7)

r. OThe expected absolute effect of treatment in a classicfy-phase) trial conducted in the same source population

naturally, RD = R - & and the relative effect isRR = R/R,.


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Randomized Discontinuation Trials 97 1Effect of Excluding Non-compliers

It is reasonable to expect that non-compliance will affectonly those subjects who actually respond to active treat-ment, whereas spontaneous responders will not be affected.The proportion of active responders in the source popu-lation is R -R,,. If the rate (frequency) of compliance inphase II is pe , then the response rate in the treatment groupof an RDT will be:

spontaneous responders in phase I, the response rates ontreatment and placebo would be given by the following,general formulas:r= (R-%)(S&)p,+(%)(SE,)(R -%)(SE ,)+(%)(SE ,)+(l -SP,)(l- R)(A.ll)

WKR - 41) P, + &I CR 4,) 6% )c + (4, ) (SE,)r= (SE,)(R)+(l -SP,)(l -R) (A.8) r=(R-R,)(SE,)+(R,)(SE,)+(l-S~,)(l-R)If there is no contamination , response rate in the placebogroup will not be affected by non-compliance.The expected rate of compliance in phase II, pc . can becalculated using the same approach as was used to deriveformulas (A.4) and (AS). If we denote the sensitivity andspecificity of detecting comp liance in phase I by SE , andSP,, respectively, and x, is the rate of compliance in thesource population, then the expected rate of complianceamong those selected for phase II can be calculated as:

(SE,) 6~)Pc=(SE,)(rr,)+(l-SP,)(l-n,)~ A.9)The expected response rates in the classic, one-phase trialcarried out in the source population areR, = (R - R&T, + & in the treatment group, and & in theplacebo group.

Effect of CurabilityLet c be the proportion of active responders who arepermanently cured in phase I. Then the expected responserate on placebo in a discontinuation study is:

r, = SErKR %)c + %)I(SE,)(R)+(l-SP,)(l-R) (A.lO)

Different Selection ProbabilitiesIf we assum ed different selection prob abilities (differentsensitivities of the identification criteria) for active and

(A.12)where SE , and SE , are the sensitivities of the criteria foridentifying active and spontaneous responders, respectively.The values for r and r, obtained using these formulas canbe employed in calculating the sample size.

Effect of Excluding Adverse ReactorsWe are only concerned here with adverse reactionsthat result in a patients withdrawal from the study.We assume that w ithdrawals due to adverse reactions

are not included in the final analysis and that thewithdrawal rate is the same in the treatment and placebogroups (assuming unequal withdrawal rates would notchange the results substantially). If N, denotes thenumber of subjects originally randomized, and p, isthe proportion of patients who tolerate the treatmentin phase II (i.e. do not withdraw due to adverse reactions),then the number of subjects available for analysis issimply:N = N,p,. (A.13)

To calculate p,. we assume that tolerators are identified inphase I with sensitivity SE , and specificity SP,. If n, is thetrue proportion of tolerators in the source population, then,analogously to equation (A.9), we have:(S-9 (n,)

=(SE,)(x,)+(l -SP,)(l -n,) (A.14)

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Randomized Discontinuation Trials Utility