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`PRIMER ON MULTIPLE SCLEROSIS
`
`EDITED BY
`
`BARBARA S. GressER, MD, FAAN
`Departmentof Neurology
`David Geffen Schoolof Medicine at UCLA
`Los Angeles, CA
`
`OXFORD
`UNIVERSITY PRESS
`
`2011
`
`

`

`OXFORD
`UNIVERSITY PRESS
`
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`
`Library of Congress Cataloging-in-Publication Data
`Primer on multiple sclerosis / edited by Barbara $. Giesser.
`p.:cm.
`Includes bibliographical references and index.
`ISBN 978-0-19-536928-1 (alk. paper)
`1. Multiple sclerosis.
`1. Giesser, Barbara S.
`[DNLM: 1. Multiple Sclerosis. WL 360 P53 2011]
`RCy77.P747 2011
`616.8'34—de22
`
`ISBN-13 9780195369281
`
`2010000644
`
`The science of medicine is a rapidly changing field. As new research and clinical
`experience broaden our knowledge, changes in treatment and drugtherapy occur.
`The author and publisher of this work have checked with sources believed to be
`reliable in their efforts to provide information that is accurate and complete, and in
`accordance with the standards accepted at the time of publication. However, in
`light of the possibility of humanerror or changes in the practice of medicine,nei-
`ther the author, nor the publisher, nor any other party who has beeninvolved in the
`preparation or publication of this work warrants that the information contained
`herein is in every respect accurate or complete. Readers are encouraged to confirm
`the information contained herein with other reliable sources, and are strongly
`advised to check the product information sheet provided by the pharmaceutical
`companyfor each drug theyplan to administer.
`
`987654321
`Printed in the United States of America
`on acid-free paper
`
`

`

`This material may be protected by Copyright law (Title 17 U.S. Code)
`
`
`
`Stephen Krieger, Svenja Oynhausen, and Aaron Miller
`
`been delineated into four subtypes, relapsing-
`Multiple sclerosis (MS) is a disease whose hetero-
`remitting MS (RRMS), secondary progressive MS
`geneity poses unique challenges in making the
`(SPMS), primary progressive MS (PPMS), and
`diagnosis, offering prognosis, and deciding about
`progressive-relapsing MS (PRMS).
`It should be
`treatment. The heterogeneity may pose evengreater
`emphasized that the namesfor the clinical sub-
`challenges in the design ofclinical trials because
`types are oflimited, mostly descriptive applicability.
`it leads to problems of operational definitions,
`ascertainment of clinical data, and selection of
`As theyare based solely on the effects ofthe disease
`that cross the clinical threshold, the categories do
`meaningful outcomes as they pertain to charac-
`not necessarily reflect the true underlying patho-
`terizing the disease course. Applying the results
`logical heterogeneity. In RRMS, for instance, the
`of clinical
`trials to individual patients adds an
`formation of newT2lesionsis far more common
`additional degree ofdifficulty.
`than the occurrence of clinical attacks, indicating
`The natural history of MS has been well charac-
`that even during periods of clinical quiescence,
`terized over the past several decades. Although
`tissue damage continues to accumulate. The sub-
`there are numerous methodological problems
`types also vary in their definitionas they apply to
`with the direct use of natural history controls, the
`the temporal course of MS: PPMS is a discrete
`entire enterprise ofdesigningclinicaltrials for MS
`subtype, but RRMS and SPMS can bothoccurin
`begins with applied natural history. Assumptions
`the sameindividualat different points in his or her
`about the expected behavior of the disease are
`disease course. In addition, the transition from
`implicated in trial design, outcome selection,
`RRMS to SPMS is indistinct and can only be
`entrance criteria, and powercalculations. Clinical
`definitively identified in retrospect. One, therefore,
`trials of MS treatments are typically short term,
`cannot know whether a patient with RRMS has
`relapse, or magnetic resonance imaging (MRI)-
`already begunto progressat the time ofenrollment
`based studies; long-term benefits assessed utilizing
`into an RRMS trial.
`robust clinical measures remain to be definitively
`Nonetheless, these categories are most useful
`established. As the disease course typically spans
`in the context ofclinical trials, where homogenous
`several decades,it is particularly difficult to draw
`populationsare desirable to most clearly discerna
`firm conclusions about the consequence oftreat-
`therapeutic effect, and muchofthe successful work
`ments that have been available for only a fraction
`of this duration. Indeed, it is not clear how best to
`in the field, as well as the focus of this chapter,
`pertains to relapsing-remitting disease. Although
`determine whether, and to what degree, current
`necessary fromatrial design perspective, the use
`medications are influencing the long-term course
`of categories that are not biologically defined
`of the disease (Noseworthy, 2007).
`imposes several assumptions on the planningof a
`A discussion of MS clinical
`trial design and
`trial. As Randy Schapiro (personal communication)
`interpretation must begin withacritical review of
`the operationaldefinitions used to characterize the
`has noted, “There is no relapsing-remitting MS or
`secondary progressive MS—there is only MS.”
`disease. The broad range of MS disease course has
`
`435
`
`

`

`436 Part7 Research
`
`While MS experts debate whether MS is one
`disease or many, confining clinical
`trials to a
`particular disease state not defined by distinct
`pathophysiologic mechanisms may increase both
`false-positive and false-negative results for clinical
`research. The reliance on these classifications
`for clinical trials limits the generalizability of the
`results across the entire MS spectrum,andit typi-
`cally restricts approval and licensure of an agent
`to the subtype of MS in which it has been studied.
`Anerain whichthe subtype-delineationsare likely
`to be updated,as genetics and biomarkers become
`available to better elucidate the pathological sub-
`strates for clinical patterns,is likely beginning.
`Clinical
`trials in MS have, since the early
`1980s, followed a traditional “double-blind, placebo-
`controlled,
`randomized paradigm” (McFarland
`and Reingold, 2005) and have led to the approval
`of six agents for the treatment of MS. The wide-
`spread use ofthese treatments has transformed
`the management of MS and has significantly
`impacted the design of clinical
`trials that are
`needed to find safer and moreeffective therapies
`for relapsing MS andto test newtherapies for other
`as yet untreatable formsofthe disease (McFarland
`and Reingold, 2005). Despite the extraordinary
`advancements in neuroimmunology, rational drug
`development, and clinicaltrial design and analyses,
`clinical
`trials are hampered by an incomplete
`basic understanding of the MS disease process,
`the mechanism of action of the agents under
`investigation, and the ideal way to gauge their
`clinical effectiveness. The hopeis that early treat-
`mentwill impact long-term course and the subse-
`quent developmentofdisability, but there is, as
`yet, little convincing evidence that our current
`agents affect this outcome (Noseworthy, 2007). In
`addition, the currently available therapies are only
`partially effective, have side effects, are difficult to
`deliver, and are expensive. However, the wide-
`spread availability and clinical acceptance ofthese
`agents hasled to a transformation in the design
`of modern MS clinical trials, one that
`is both
`ethically and practically based (McFarland and
`Reingold, 2005). Currently, more than ever, a
`dynamic pipeline of parenteral and oral agents is
`already in phase III testing so that several new
`agents mayreach the market in the next few years.
`This new landscape of MS therapeutics presents
`novel challenges to futureclinical trials, and this
`
`chapter will review the assumptions and design
`considerationsofpivotal and recent MS trials to
`provide a historical perspective on how we have
`arrived at the present momentin considering the
`future of MS research. It will conclude with an
`evaluation ofthe currentstate ofethics ofplacebo-
`controlled trials, as well as an overview of new
`approachesto the study of MS that take a more
`holistic approach than that of the traditional
`clinical trial.
`
`CLINICAL TRIAL OUTCOMES
`MEASUREMENT:AN OVERVIEW
`
`Multiple sclerosis clinical trials must be designed
`to capture the broad array of potential disease
`manifestations across individuals, but they mustdo
`so in a way thatis reproducible and standardized.
`Outcome measures must be multidimensional in
`order to adequately encompass the myriad ways
`MS effects patients both in the short and long
`term. To this end, clinical trials focus on the two
`hallmark characteristics of MS: the occurrence of
`relapses andthe accrual ofdisability. Choice ofthe
`outcome measure depends on the presumed
`mechanism ofaction of the investigated treatment
`andits anticipatedclinicaleffect. It is important to
`choose the most appropriate primary outcome
`measurefor each individualtrial (D’Souzaet al.,
`2008). In addition, a study must be of sufficient
`duration to allow the benefit of the agent
`to
`become evident and have a subject population
`large enough to power the study adequately. As
`long-term disability cannot be adequately assessed
`directly in a short-term clinical trial, all of our
`clinical measures from relapse-based assessments
`to measures of sustained disability in the short
`term can be considered surrogate markers of our
`ultimate long-term therapeutic goals.
`
`Short-Term, Relapse-Based Outcomes
`
`trials of disease-modifying agents for
`Clinical
`MS typically utilize relapse-based endpoints to
`demonstrate therapeutic effect. As short-term
`trials (usually between 1 and 3 years in duration)
`are often underpowered to demonstrate effect on
`long-term disability, endpoints such as the annu-
`alized relapse rate, time to first relapse, and per-
`cent of patients relapse free serve as surrogate
`
`

`

`markers of disease suppression. These trials,
`and in particular their placebo arms, provide an
`instructive data source to characterize the short-
`term behavior of relapsing MS.
`A relapse may be operationally defined as
`an objectively, clinically ascertainable, new orseri-
`ously worsening neurological deficit that persists
`for more than 24 hours, that develops at an inter-
`val of at least 30 days after a previous relapse, and
`is not related to infections. This 1-:month window
`does not necessarily correspond with the actual
`biology of the disease, where often more than one
`area of active inflammation in the central nervous
`system (CNS)exists, each of which runs an inde-
`pendenttime course (D'Souza et al., 2008). Short-
`lived aggravation of the symptoms related to
`elevations in body temperature(e.g., with fever,
`physical exercise, hot showers, warm weather) are
`referred to as Uthoff phenomena or “pseudoexac-
`erbations.” They result from an unmasking of
`subclinical lesions or worsening of chronic symp-
`tomsby transient elevations in temperature, and
`they do not constitute new inflammatory CNS
`activity. Patients cannot always distinguish a true
`exacerbation from a pseudoexacerbation, which is
`significant given that manytrials rely on patients
`to reportthe occurrenceofa relapse.
`Problems comparing the efficacy of various
`treatments are amplified by trial-to-trial variation
`in relapse definition in terms of duration (24 or
`48 hours) and whether a change on the neuro-
`logical exam {as noted by a blinded evaluator) is
`present. Furthermore,trials are inconsistent about
`whether the objective change in the neurological
`examination must correspond with the clinical
`symptomsas described by the patient. The more
`narrow the definition,
`the lower the recorded
`relapse rate. Additionally, changes on the neuro-
`logical examination (particularly changes in reflexes
`or subtle sensory changes) may be noted by the
`examiner in the absence of new symptoms to
`qualify as a relapse. Even with the most rigorous
`relapse criteria, borderline events will always be
`left to the investigators’ judgmentto interpret. If
`the expectationsofthe trial’s sponsorare apparent
`to the investigators and their patients, the relapse
`rate in one group ofpatients might be underesti-
`mated in nonblinded studies (Sorensen, 2008).
`Beyond the issuesof ascertainment, relapse rate
`isa useful, but flawed, measureof MS disease activity.
`
`29. Issues in MS Clinical Trials
`
`437
`
`Suppressing relapses benefits patients both imme-
`diately in terms of functional status, and poten-
`tially in the long term, as relapses are associated
`withsignificant residualdeficits (Lublin etal., 2003).
`In addition, the relapse rate early in the disease
`is an important determinant of accumulation of
`disability later in the disease course. Although
`lowerrelapserates in the early yearsofthe disease
`may portend less eventual disability, whether a
`reduction in relapse rate imposed by treatment
`provides the sameeffect on long-term disability as
`would a relatively relapse-free experience as part
`ofan individual's natural history remains unknown
`(Noseworthyet al., 2006).
`
`Long-Term Observational Studies and
`Disability-Based Outcomes
`
`The maximum clinical variability of MS is seen
`in the short term after disease onset; the illness
`becomes more predictable upon long-term obser-
`vation. Muchofthe data on long-term outcomes
`in MS comesfrom severallongitudinally followed
`cohorts and not from randomized clinical trials.
`As natural-history studies, these are largely com-
`prised of patients who did not receive disease-
`modifying treatments; because of the availability
`of treatment,it is no longerfeasible to follow such
`cohorts prospectively in the modern era, Three
`cohorts that provide large-scale, prospective analy-
`ses of untreated populations are those from
`Lyon, France (Confavreux et al., 2000), Sweden
`(Runmarker and Andersen, 1993), and London,
`Ontario (Weinshenker et al., 1991). Long-term
`prognosis is often described using time to devel-
`opmentofdisability landmarks in the Expanded
`Disability Status Score (EDSS). These include
`EDSS4, the development of moderate disability
`with preserved gait; EDSS 6, the need for assis-
`tance with ambulation; and EDSS 7, the need for
`a wheelchair for mobility. While these classifica-
`tions are limited by their focus on mobility, they
`provide a meaningful windowinto the time course
`of accrual of disability and reflect particular out-
`comes of great concern to patients diagnosed
`with MS.
`The EDSS remains the criterion standard by
`which disability is measured in both the long and
`the short
`term.
`In short-term studies lasting
`from 1 to several years, “sustained disability” as
`
`

`

`438 Part7 Research
`
`an outcomevariable requires a measured change
`on the EDSS being reproduced at
`two points
`separatedin time,usually by 6 months,Ifa patient
`“changes by 1 point on the EDSS,” however,this
`could mean a variety of things depending on
`where along the scale the patient is, and vary even
`further depending on what
`functional system
`brought about the change in EDSS step. In addi-
`tion, persistent or sustained increases in physical
`impairment may occur because ofa failure to
`completely recover from a relapse or from the
`slow accrual of disability that characterizes pro-
`gressive MS. Theuseof “sustained disability” as a
`clinical endpointfails to elucidate this distinction.
`As these processes are likely based on varying
`pathophysiology, lumping them togetherasa sin-
`gle clinical endpoint may not adequately capture
`the biologic responseto a therapeutic agent.
`The EDSS has a number oflimitations that
`bear mention when consideringits use in clinical
`trials. It is weighted toward ambulatory disability
`but is insensitive to other aspects of MS-related
`impairment, in particular cognitive dysfunction.
`Although a numerical scale,
`it
`is ordinal and
`categorical
`in nature and neither quantitative
`nor linear. The EDSS is thus notideally suited to
`the deltas and changes in the “mean” thatarefre-
`quently used as outcomevariables. As an assess-
`menttool, the EDSS hasonly moderateinter-relater
`reliability particularly at the lower range,
`is not
`entirely objective, and can have great fluctuation
`particularly at
`the lower levels.
`In its highest
`levels, the scale becomes a subjective description
`ofa patient's home care needs, and thuspatients
`in the upper strata of EDSSarerarely included in
`clinicaltrials.
`
`ISSUES IN CLINICAL TRIAL DESIGN AND
`INTERPRETATION
`
`Reconsidering the EvolutionofPivotal Trials
`
`The 1990ssaw the publication oflarge clinicaltri-
`als evaluating the three brands ofinterferon beta
`and glatirameracetate as disease-modifying drugs
`in MS, and their subsequent regulatory approval
`and evolution into standard of care. Although the
`individual disease-modifying agents are discussed
`in previous chapters, someofthe implications of
`
`the pivotal trials on the design and interpretation
`of subsequent andrecent studies will be reviewed
`here,
`The randomized, placebo-controlled paradigm
`ofthe pivotal trials demonstratednot only efficacy
`of the agents studied but pronounced placebo
`effects on relapse rates when comparing prestudy
`with on-study exacerbation rates in the placebo
`group (D'Souza et al., 2008). The results of the
`interferon B-1b pivotal
`trial
`reported in 1993
`(IFN B Multiple Sclerosis Study Group, 1993) are
`an archetypeforthis period in MS clinical research,
`and they demonstrated an annualized relapse rate
`of 0.78 in the interferon group versus 1.27 in the
`placebo group. Thestudywascriticized for issues
`of relapse-ascertainment and confirmation, as
`relapses were self-reported and not universally
`confirmed by an examining neurologist. Three
`years later, in the weekly interferon B-1a study
`(Jacobs et al., 1996), the placebo group had an
`annualized relapse rate of 0.82, which was com-
`parable to that of the rate of 0.84 in the placebo
`group of the pivotal
`trial of glatiramer acetate
`(Johnson et al., 1995).
`It was already clear that
`although there was a comparable degreeofrela-
`tive relapse rate reduction between the agents,the
`actual annualized relapse rates varied consider-
`ably betweentrials. All the values arelikely to be
`skewed toward higher attack rates, as patients
`were selected for these studies on the basis of
`high prestudyclinical disease activity. The relapse
`rate may then “regress towards the mean” once
`these patients have been enrolled in thetrial, in
`part explaining the extentof the apparent placebo
`effect. The efficacy of placebo mayalsoreflect the
`impactof the comprehensivecare provided totrial
`participants (D'Souzaetal., 2008). The pivotaltri-
`als’ placebo group results underscore the impor-
`tance ofrandomized, placebo-controlled trials and
`why positive head-to-head equivalency studies
`alone cannotbe used to prove an agent's efficacy,
`nor have they been considered sufficient evidence
`for regulatory approval.
`The interferon B-1b pivotal trial did not demon-
`strate a statistically significant effect on disability,
`andasthetrial enrolled ambulatory,relapsing-re-
`mitting patients it was likely underpowered to
`assess this outcome. In contrast, the pivotaltrial
`of weekly intramuscular interferon B-ia (Jacobs
`et al., 1996) utilized disability as the primary
`
`SL
`
`

`

`outcome measure and demonstrated a slower rate
`of accumulation ofdisability for the treated group,
`which was defined in advance as deterioration
`by 2 1 point on the EDSS for 2 6 months. In the
`subsequentpivotaltrials ofnatalizumab, AFFIRM
`(Polman et al., 2006) and SENTINEL (Rudick
`et al., 2006), disability endpoints were also met,
`with sustained disability defined as persisting for
`23 months.
`A significant issue in the pivotal trials was that
`of the success ofthe blinding. Type and degree of
`blinding play an important role in the adjudica-
`tion ofpatient-reported symptomsandtheirascer-
`tainment by an evaluator. As the majority of
`treatments tested including glatiramer acetate,
`interferons, and mitoxantrone have easily recog-
`nized side effects or hallmarks such as injection
`site reactions,
`it
`is likely that the patients were
`able to correctly guess whether they were receiv-
`ing placebo or active drug, which can confound
`the results given the subjective nature ofrelapses
`as assessed in these trials. Unscheduled symptom-
`initiated studyvisits and the methodsofascertain-
`ment of relapses at these visits should be equal
`across treatment arms to ensure thatrelapse assess-
`ment is not affected by systematic ascertainment
`bias. Modern double-blind studies have employed
`both a treating-neurologist and blinded evaluat-
`ing neurologist to conductthe trial assessments.
`However, as oral and parenteral agents now in
`development have distinct modes of administra-
`tion fromthe self-injected therapies with which
`they are being compared, this has necessitated
`using single-blind designs where maintenance of
`evaluator blinding is of paramount importance.
`Nonetheless,
`the lack of a double-blind design
`must be considered wheninterpreting thesetrials,
`which include the phase II and III
`trials of
`alemtuzumab(Coles etal., 2008).
`
`Extension Trials and Long-Term
`Observational Studies
`
`Giventhatclinical trials must establish efficacy in
`a short time frame, extensiontrials and open-label
`follow-up can provide a greater window into the
`benefit and safety profile of a therapeutic agent in
`the long term.In addition, there are ethical reasons
`to design an extension study,as it ensures contin-
`ued access of an agent to the study population.
`
`29. Issues in MS Clinical Trials
`
`439
`
`Typically, at the conclusion of a randomized con-
`trolled study, patients in the treatment group
`continue on the study drug, and patients initially
`randomized to the control group are offered the
`active drug and continue to be followed, albeit
`usually with a reduced frequencyof assessments
`than during the randomized phaseofthetrial.
`Although extension trials are frequently cited
`as evidence of the long-term efficacy of an
`agent, the quality of the data obtained in such
`an investigation is clearly inferior to that of the
`randomized phase, as the extension is open-label,
`uncontrolled, and the study population may exhibit
`self-selection by the patients who responded to
`the drug in theinitial trial. Thus, extensiontrials
`may exhibit a significant selection bias toward
`“responders” andare of limited value in obtaining
`data that can be generalized overall regarding
`drug efficacy. In addition, extension trials are of
`limited impact with regard to outcome measures
`as they are generally no longerblinded, although
`to address this concern more recent trials have
`re-randomized the placebo group into a dose-
`blinded extension.
`To provide even longer term assessments of
`the impactofa therapeutic agent, nonrandomized
`long-term observational studies have been under-
`taken lasting over a decade. These are in essence
`interminableextensiontrials, and their data suffer,
`at best, from similar methodological limitations.
`Large, long-term observational data sets for both
`the interferons andglatiramer have been analyzed
`(Ebers and Traboulsee, 2009; Rovaris et al., 2007)
`and are ofgreatest value in providing information
`about safety and long-term survival, while the
`“sustained efficacy” described in these data sets
`is confounded by enormous dropoutrates, the
`unavoidablebias favoring responders, and the lack
`of an effective intention-to-treat analysis. These
`observational studies blur the distinction between
`research andclinical practice, and while they may
`attempt to quantify outcomesseen in “real world”
`standard ofcare, they lack the rigor and generaliz-
`ability of well-performedclinical trials. That said,
`carefully designed long-term observational studies
`with specific hypotheses and preplanned analyses
`havethe potential to provide valuable information
`that cannot be captured during the short-term
`randomizedclinical trials of agents currently in
`testing.
`
`

`

`440 Part7 Research
`
`The Problem ofCross-Trial Comparison
`
`The reductionin relapse rate in the pivotaltrial of
`weekly interferon B-1a (Jacobset al., 1996)at 18%
`was more modest than that seen in the interferon
`B-1b pivotal trial. In the weekly interferon B-1a
`trial, the relapse rate declined from 1.2 to 0.61
`in the treatment group versus 1,2 to 0.82 in the
`placebo group. These twotrials underscore the
`problemsof cross-trial comparison evenfor stud-
`ies done in the sameera, as the raw annualized
`relapse rate outcome would appearto favor weekly
`interferon B-1a as opposed to the 0.78 seen with
`interferon B-1b, while the relative reduction
`versus placebo favors the latter. Which drug is
`“better?” As discussed later in this chapter, this
`issue becomesall the more pronounced when one
`comparesthe results of the pivotal trials to those
`done in the “postmillennial” or “McDonald era”
`where an on-drug relapse rate of 0.78 or 0.61
`would be considered an utterfailure in the context
`of the current standard ofefficacy.
`Another example ofthe difficulties in compar-
`ing between two trials comes from the studies
`of the effect of subcutaneous interferon B-1b on
`disease progression in SPMS.Theinitial European
`study demonstrated that
`treatment with inter-
`feron B-1b wasassociated with a higher probability
`of stabilization of progression of disability com-
`pared to placebo, The therapeutic effect on this
`outcome measure, however, was not replicated in
`a North American study using a comparable but
`not identical study design (Panitch et al., 2004).
`Giventhe heterogeneity of MS in termsofclinical
`course and variable outcome, subtle variations in
`such factors as inclusion criteria, matching of
`study cohorts, selection ofoutcomevariables, and
`statistical analyses are sufficient to render study
`results incomparable.
`In the pivotal trial era, however, head-to-head
`studies were not performed. The Food and Drug
`Administration (FDA) does not accept “equiva-
`lency trials” as sufficient evidence for licensing
`approval, particularly as one could reasonably con-
`clude from equivalence in a head-to-head study
`either that an agent
`is equally as effective or
`equally as ineffective as its comparator. This posi-
`tion favored the use of placebo-controlled trials,
`particularly asit statistically easier to demonstrate
`superiority of an investigational drug, with a
`
`smaller sample size, when compared with an inef-
`fective placebo than versus a partially-effective
`comparator.
`The head-to-head trial era in MS began with
`the developmentof subcutaneousinterferon B-1a
`given three times a week.As it is the same mole-
`cule as once-weekly interferon B-1ba, in order to
`expedite regulatory approval as Rebif, the FDA
`required positive head-to-head superiority studies
`before it could enter the market in the United
`States. Head-to-head comparisonsoftherelative
`efficacy of high- and low-dose interferon B-1a
`used as their relapse-based outcome the propor-
`tion of relapse-free and MRIactivity-free patients.
`While both the INCOMIN (Durelli et al., 2002)
`and EVIDENCE studies (Panitch et al., 2002)
`demonstrated an advantage of high-dose inter-
`feron, by choosing as the primary outcome mea-
`sure the “proportion of relapse-free patients”
`rather than the overall relapse rate, these trials
`evaluate the number of optimal responders and
`maynotreflect a differential of general effective-
`ness across the population. They nonetheless
`weresufficient to justify the licensure of subcuta-
`neous interferon B-1a in the United States, and
`they established a head-to-head trial paradigm
`that not all subsequent such studies were able to
`replicate.
`
`The McDonald-Era Clinical Trials:
`Head-to-Head andClinically Isolated
`SyndromeTrial Designs
`
`Head-to-head studies
`
`active-
`of
`implementation
`successful
`The
`including the head-to-head
`comparator
`trials,
`studies of high- versus low-dose interferon in the
`EVIDENCE and INCOMIN trials, led to the design
`and recruitment of several head-to-head trials of
`high-dose interferon B versus glatiramer acetate
`(Copaxone). Recruiting during the McDonald era,
`the BEYOND and REGARDtrials (Mikoletal.,
`2008; see also Achiron and Fredrikson, 2009)
`failed to show a difference on relapse-based out-
`comesbetweeneitherof the interferon B products
`and glatirameracetate. Thesetrials differ consid-
`erably in design, but the commonfactor involved
`in both trials’ failure to reach their relapse-based
`primaryendpoints was the loweventrate observed
`
`

`

`in all groups. The REGARDstudy wasa 2-year,
`randomized, open-label, head-to-head compara-
`tive study of subcutaneousinterferon B-1a 44 Lg
`three times a week and glatiramer acetate, which
`showed no difference in the primary outcome
`measure, timetofirst relapse, or the proportion of
`patients who wererelapse free. The sample size
`and powercalculations,as previously described in
`the example above,are predicated on assumptions
`of an expected event rate. Although the annual-
`ized relapse rates in the REGARD study were
`almost
`identical (0.30 for interferon B-1a and
`0.29 for glatiramer acetate),
`they were much
`lower than those reported in landmarktrials (0.87
`for interferon B-1a and 0.59 for glatiramer acetate)
`(Sorensen, 2008). The revised McDonaldcriteria
`allowed for the use of MRI to establish the diagno-
`sis of MS; since manylesions detectable on MRI
`are clinically silent, these revised criteria allow a
`diagnosis ofconfirmed MS to be madeearlier than
`would have been possible usingclinical manifes-
`tationsof relapses alone (Lublin, 2005). The inclu-
`sion ofthis new population in the postmillennial
`trials shifted the curve toward patients less likely
`to experience relapses in the short term.
`A second consideration in the REGARD trial
`was the selection oftime to first relapse as the
`primary outcomevariable. Time to first relapse
`on treatmentis a robust parameter, evenin trials
`with high dropout rates. However,
`it does not
`make use of the second and subsequentrelapses
`in the courseofa trial, and thusit is particularly
`sensitive to differences in time course of thera-
`peutic onset. It favors drugs with rapid onset, as
`comparedto those with a more delayed but perhaps
`in the long run an equivalentor better-sustained
`effect (D’Souza et al., 2008). There are competing
`influences on trial design, where the goal is to
`assess a meaningful benefit in aslittle time as
`possible, but to be done in such a way as to dem-
`onstrate efficacy for a product intended for long-
`term use in a lifelong disease. It is of particular
`note that REGARD failed to demonstrate the pur-
`ported more rapid time of onset of interferon B
`over glatiramer acetate.
`Clearly the use ofhistorical controls,particularly
`in the modern era of across-the-board decrease in
`observed relapse rates, imparts an unacceptably
`high degree of false-positive error. But what are
`the other implications ofthe relapse rates of the
`
`29. Issues in MS Clinical Trials
`
`441
`
`McDonald era onclinical trial design and inter-
`pretation? One consideration is how to interpret
`the results of the AFFIRM trial (Polman et al.,
`2006) conducted at the outset of the McDonald
`era, which demonstrated the 68% reduction in
`relapserate that natalizumab (Tysabri) established,
`approximately twice as great a reduction as the
`existing injectable therapies achieved in their
`pivotal trials. These sameinjectable agents, how-
`ever, demonstrated approximately an 80% reduc-
`tion in relapse rate in the BEYOND and REGARD
`trials of the past few years. Is AFFIRM the last
`trial of the pivotal era orthe first of the McDonald
`era? There have been no head-to-head studies to
`elucidate this.
`Either way, for most patients with MS,relapses
`are a
`relatively infrequent event.
`In studies
`planned for short duration, only a small percent-
`ageofpatients will experience a relapse. It may be
`difficult
`to ascertain which of these patients
`respond optimally and which experiencedeither a
`more mild form ofthe disease, or just a period of
`disease quiescence unrelated to the therapeutic
`intervention (Walton, 2007). Ifmost patient