Review of methodological issues of clinical trials in multiple sclerosis

Transcription

1 Journal of the Neurological Sciences 311 S1 (2011) S35 S42 Review of methodological issues of clinical trials in multiple sclerosis Xavier Montalban* Unitat de Neuroimmunologia, Centre d Esclerosi Múltiple de Catalunya (CEM-Cat), Hospital Universitari Vall d Hebron, Barcelona, Spain article info summary Keywords: Multiple sclerosis Clinical trial design Disease-modifying treatments Interferon-beta Glatiramer acetate Surrogate markers Magnetic resonance imaging There are currently six approved disease-modifying therapies available to the physician for the treatment of multiple sclerosis. Their efficacy on clinical and radiological parameters has been demonstrated in Phase III pivotal clinical trials over the past two decades. Perceptions of the relative potency of these treatments have been driven principally by the response measured relative to a placebo group. However, efficacy comparisons between trials is of limited value because of differences in study methodology, in characteristics of the patient populations included, in the behaviour of the placebo group during the trial and in the time at which the trial was conducted. Moreover, and most importantly, the assumption that the efficacy observed in clinical trial settings is the same as that achievable in everyday clinical practice is inevitably flawed. Impressions of the relative efficacy of two treatments may differ dramatically depending on whether absolute or relative differences with respect to placebo are compared. Randomised direct comparative trials are therefore the only objective way to evaluate the relative efficacy of two therapies. It is clear that between-treatment differences are difficult to quantify in short-term studies and require large numbers of patients. Long-term outcome is increasingly important to monitor in spite of the inherent methodological limitations in order to establish the safety profile of a potentially lifelong treatment. New disease-modifying treatments for multiple sclerosis will soon be available. Although these are eagerly awaited, their risk benefit profile, and their place in therapy, will only be adequately understood once real-life and long-term use has been documented as well as it has been for current treatments. Over the last two decades, considerable advances have been made in the methodology of clinical trials in multiple sclerosis. Consensual standardised protocols have been designed and validated for Phase II and Phase III trials, with standardised definitions for short-term clinical and radiological outcome measures. The elaboration and implementation of this methodology were possible through international collaborations, and this has enabled extensive experience to be gained throughout the world. These trials have laid the foundation for an evidence-based medicine approach to the treatment of multiple sclerosis. Clinical trials in multiple sclerosis have to some extent become a victim of their own success, with more and more trials competing for a limited pool of patients and limited resources. Modern trials require large number of patients to generate adequate statistical power and this in turn entails recruitment in many countries across different continents. This increases the complexity and cost of the study, and contract research organisations now play a dominant role in the logistics and administration of these trials. The challenge in conducting trials on a global basis involving large numbers of countries is to ensure that this heterogeneity does not impinge on the reliability of the findings. This may happen due to differences in the patient populations included in different countries, access to or experience with methods in evaluation, for example certain magnetic resonance imaging (MRI) protocols, and also due to ethical considerations. In addition, whether disease-modifying treatments are reimbursed in a given country or not will influence what sort of patients are likely to get included in clinical trial protocols Elsevier B.V. All rights reserved. The choice of comparator group: placebo or active comparator? A critical question in designing clinical trials is the choice of a comparator group. In certain areas of medicine, it is possible to * Correspondence: Dr. Xavier Montalban, Unit of Clinical Neuroimmunology, EUI-2a P, Hospital Universitari Vall d Hebron, Paseig Vall d Hebron , Barcelona, Spain. address: xavier.montalban@unic-em.com (X. Montalban). manage without an internal comparator group since the course of the illness is sufficiently predictable for the efficacy of an intervention to be assessed accurately with respect to a historical control group, a virtual placebo group, or by using a surrogate marker. However, none of these options are available in multiple sclerosis, a heterogeneous and multifaceted disease, whose course is unpredictable in individual patients and cannot be tracked using surrogate markers. For this reason, it is unavoidable for clinical trials in multiple sclerosis to include an internal control group to which X/ $ see front matter 2011 Elsevier B.V. All rights reserved.

2 S36 X. Montalban / Journal of the Neurological Sciences 311 S1 (2011) S35 S42 Patients with relapses (%) % EUSPMS 58% 63% SPECTRIMS 58% 38% NASPMS 29% 37% IMPACT Fig. 1. Percentage of patients with relapses in four placebo-controlled trials of interferon-b in secondary progressive multiple sclerosis [1 4]. Open columns: placebo groups; filled columns: interferon-b groups. From Rovaris et al. [5], Lancet Neurol 2006;5(4): patients can be randomised. Such a group can either be an active comparator or a placebo. The need for an internal comparator group is compounded by the fact that, in spite of ostensibly similar inclusion criteria used in different clinical trials, quite different patient populations may be included, leading to different clinical outcomes on treatment. This is well illustrated by the different clinical trials that have been performed with interferon-b in secondary progressive multiple sclerosis (SPMS). The NASPMS [1] and EUSPMS [2] trials of interferon-b 1b, the SPECTRIMS trial of interferon-b 1a sc [3] and the IMPACT trial of interferon-b 1a im [4] all used very similar inclusion criteria, but outcome was quite different between the trials. The on-trial relapse rates were over two times as high in EUSPMS and SPECTRIMS than in NASPMS and IMPACT, in both the placebo and interferon-b treatment groups (Fig. 1). Even between the EUSPMS and NASPMS trials, which evaluated the same treatment with a very similar protocol, differences in outcome were striking. In the absence of a placebo comparator group, it would have been possible to conclude erroneously that interferon-b 1a im was considerably more effective than interferon-b 1a sc, whereas when compared with placebo, all treatments appear to have comparable, but quite modest, efficacy. Similarly, the proportion of patients in the placebo groups of SPMS trials who acquire confirmed increase of disability ranges from 65% in the SPECTRIMS trial [3] to 22% in the MIMS trial of mitoxantrone [6], in spite of the use of broadly similar entry criteria. The choice between an active comparator and a placebo raises a number of issues. In many countries, including Western Europe, use of a placebo in Phase III trials is no longer feasible in relapsing remitting multiple sclerosis, since ethics committees and regulatory authorities will no longer accept that patients with disabling disease receive placebo for at least two years when treatments with established efficacy exist. Even though their duration is shorter (around six months), use of placebo in Phase II trials is increasingly coming under challenge. Furthermore, the choice of outcome measure is also relevant to the choice of comparator. For example, if the primary endpoint of the trial is annualised relapse rate and it is necessary to keep the patients in the study for two years in order to estimate the relapse rate with sufficient accuracy, then the ethical issue of placebo is more relevant than for a trial where the endpoint can be estimated over a shorter time-span, such as using a reduction in the appearance of contrast-enhancing lesions. The alternative to placebo is the use of an active comparator, and this is increasingly being used in current clinical trials. However, the choice of an active comparator has consequences for the statistical 26% power of the trial and consequently for the sample size required. The power of the study depends on the treatment effect size to be measured, the smaller the difference anticipated between the two groups, the more patients will need to be enrolled in order to observe the treatment effect. Since the relative benefit of an experimental treatment with respect to an active comparator will be smaller than the benefit with respect to placebo, the choice of an active comparator will necessarily inflate patient numbers, and consequently increase the cost and complexity of the study. The choice of placebo or active comparator will also be expected to influence the type of patient included in clinical trials, and thus to have an impact on the outcome of the trial. For example, high risk patients with a poorer short-term prognosis, who present frequent relapses, active disease on MRI or measurable disability progression, are more likely to be included in a clinical trial with an active comparator arm rather than a placebo arm. In contrast, patients with milder disease activity are more likely to be included in a clinical trial with a placebo comparator. Since the two groups of patients have different prognoses, the treatment effect observed is also likely to be different. The choice of study design: efficacy vs effectiveness? It is important to recognise that the information provided by randomised clinical trials, although essential for evaluating the efficacy of experimental treatments, is not directly transposable to everyday conditions of patient care. For this reason, we distinguish between efficacy, which corresponds to the effect of the treatment determined in isolation under ideal conditions in the absence of confounding variables, and effectiveness, which corresponds to the effect of treatment under everyday conditions of care, after taking into account all the other factors that influence patient outcome. One such factor is the heterogeneity of the patient population. When randomised clinical trials are designed to determine efficacy, eligibility criteria are set in order to ensure that a homogeneous sample of patients is included and thus limit the influence of other factors that affect outcome of the trial, such as comorbidities, comedication, age or willingness to take the treatment. However, in everyday care, these factors are frequently present in patients to whom the treatment is prescribed, and the extent to which the efficacy measured in the clinical trial will translate into realworld effectiveness is unknown. Another factor that influences effectiveness is the quality of care, with misdiagnosis of treated patients, failure to prescribe the treatment in accordance with the recommendations, and failure to provide appropriate followup all compromising the quality of care and thus diminishing the effectiveness of the treatment (Fig. 2). In order to evaluate the extent of the mismatch between ideal and everyday treatment conditions, it is useful to conduct observational trials in naturalistic real life conditions which determine the effectiveness of different treatments. Although observational studies (Class II evidence) are not considered to provide the same precision as randomised controlled studies (Class I evidence), due to the number of potential confounding factors, such studies can provide useful information about the impact of treatment in conditions of everyday care. Moreover, there is convincing evidence that the information obtained on the relative benefits of different treatment strategies from well-designed observational studies is qualitatively similar to that obtained in randomised controlled trials [7 9], and it has been suggested that such studies be performed and taken into consideration systematically when assessing healthcare interventions [10]. In addition, observational studies, being conducted in everyday care, are ideally suited for long-term monitoring of the effectiveness and safety of recently-introduced treatments, or for identifying subgroups of patients responding differentially to treatments. The

3 X. Montalban / Journal of the Neurological Sciences 311 S1 (2011) S35 S42 S37 corresponding to less than one relapse in five years) and limited progression of disability (less than one point increase in mean EDSS score) can be maintained over extended periods. Perhaps more importantly, such studies show that long-term treatment does not incur any major safety risk. Several current pivotal trials of experimental therapies include a protocol-defined prospective extension phase. In some cases, these attempt to control for confounding effects due to the evolving natural course of disease by including a placebo control group. An example of this was the extension of the CLARITY pivotal Phase III trial of cladribine [13], which was stopped when this drug was withdrawn for the treatment of multiple sclerosis. This study involved a type of cross-over design in which patients originally randomised to cladribine treatment were to be rerandomised to either cladribine or placebo and the patients in the original placebo group all switched to cladribine. The duration of Phase III clinical trials Fig. 2. Influence of the quality of care on the effectiveness of a treatment. Top (randomised controlled study): the filled segment represents the proportion of patients in whom the treatment is efficacious in a randomised clinical trial. Bottom (observational studies) upper bar: the light grey segment represents the proportion of patients correctly diagnosed; second bar: the darker grey segment represents the proportion of properly diagnosed patients who are prescribed treatment appropriately; third bar: the dark grey segment corresponds to the proportion of properly prescribed patients who are followed up appropriately; lower bar: application of the efficacy rate (98%) to the remaining pool of patients who have been managed correctly (black segment) yields an overall effectiveness rate of 45%. This is compounded by the fact that, in real life, a certain number of patients that could benefit from treatment are not allocated one. information gleaned from such studies can later be applied to the design of future randomised controlled trials, thus improving the pertinence of the latter. The importance of long-term data Collecting information on the long-term effectiveness and safety of treatments for multiple sclerosis is important, since treatment durations in pivotal Phase III trials generally do not exceed two years, which is an insufficient period to determine treatment effects on, for example, disability progression in a reliable manner, nor to identify infrequent treatment side-effects. To collect this information, it is necessary either to perform prospective open label extension studies of randomised controlled trials, in which all patients receive active treatment, or to establish ad hoc patient cohorts in large multiple sclerosis centres that can be followed systematically. These studies have certain limitations, in particular the absence of a comparative placebo group during the observational period, the risk of selective drop-out of poor responders, and the possibility that patients switch treatments. Nonetheless, such studies represent the best that we can do to assess the long-term utility of therapy. An example of this is the long-term, prospective extension study of the North American pivotal trial of glatiramer acetate [11]. After the completion of the double-blind period, all patients originally randomised were invited to enter an open label study in which they received glatiramer acetate and were followed up using a standardised protocol every six months. Fifteen years into the study, 100 patients (43.1%) are still being followed and have received glatiramer acetate continuously over this period [12]. Although it is difficult to draw firm conclusions from a study with no control group from which half the patients are no longer available for evaluation, it appears, at least in patients who continue to take their medication and return for follow-up, that a low relapse rate (<0.20, Currently, Phase III clinical trials in multiple sclerosis generally have a controlled treatment period of two years. Given that it takes time to enrol patients, this means that individual trials can last for up to four years, during which time investigators are blinded to the treatment and, in any case, its efficacy is unknown. The question therefore arises as to whether it is possible to shorten the duration of these trials. Our experience with natalizumab suggests that this may be dangerous and that it is important to monitor responses to new drugs carefully in order to be able to evaluate the risk of rare, exposure-related side effects which may be serious. In the case of natalizumab, the occurrence of progressive multifocal leukoencephalopathy (PML) was only noticed after the controlled phase of the pivotal trials had been completed and the treatment approved in the United States. The use of natalizumab is now governed by a systematic monitoring programme aimed at detecting and managing suspected cases of PML as early as possible. One possible way of minimising the risk of unanticipated safety issues without the need for extravagantly long formal clinical trials would be to give conditional approval for new diseasemodifying treatments on the basis of short-term efficacy and safety data, in which the treatments could be marketed, subject to the implementation of a risk management programme, in which any safety signals could be detected through systematic and targeted pharmacovigilance. As well as safety issues, efficacy considerations also argue against reducing the duration of clinical trials. This is because the ontreatment relapse rate can be expected to be very low in the populations of multiple sclerosis patients currently recruited into experimental treatment trials. In modern trials, this rate now ranges between 0.2 and 0.35, which corresponds to one attack per patient every three to five years. With such low an event rate, it is extremely difficult to detect between-group treatment effects over short follow-up periods, and without inflating the sample size required considerably. The current on-treatment relapse rate is surprising if we compare it with the historical rate reported in the first clinical trials, which ranged from 0.5 to 0.9. The reasons why the relapse rate has dropped so much has given rise to much speculation, but remains poorly understood. A number of hypotheses have been put forward, including a change in the patient s response to treatment, although why such a change should occur also requires adequate explanation. The second hypothesis, which is clearly feasible, is that changes in the definitions of multiple sclerosis and in diagnostic criteria, will influence the treatment effect size. This has been called the Will Rogers phenomenon, and will be discussed in more detail below. Alternatively, differences in endpoints used in the trials, for example in the definitions of relapses and disability progression,

4 S38 X. Montalban / Journal of the Neurological Sciences 311 S1 (2011) S35 S42 could influence the outcome observed. A more rigorous definition of relapse will clearly provide a lower event rate than a more lax one. It is also likely that the type of patients included in trials has changed, with a trend to including patients with more mild disease in experimental treatment trials, patients with more active disease being treated from the outset with existing disease-modifying drugs. Finally, there is the possibility that the natural history may have changed. Indeed, there is increasing epidemiological evidence that the prevalence and incidence of multiple sclerosis are rising and the character of affected patients is changing [14]. In particular, data from the Danish population collected over the last sixty years indicates that the female preponderance of the disease is becoming more pronounced, with a larger representation of women over forty years of age and that disease severity may be declining [15]. Evolving diagnostic criteria and the Will Rogers phenomenon As understanding of multiple sclerosis has grown, so have definitions of the disease changed and diagnostic criteria have evolved. The first formal diagnostic criteria were published in 1965 with the objective of rationalising inclusion of patients in clinical studies [16], and these introduced the notion of demonstration of dissemination in time and space. These Shumacker criteria were exclusively based on clinical considerations. In 1983, Poser and colleagues revisited these criteria to introduce paraclinical evidence to support the diagnosis [17]. The goal of the Poser criteria was to reinforce the distinction between definite and probable multiple sclerosis. Over the following decade, the development of MRI revolutionised evaluation of patients with multiple sclerosis, making it possible to detect lesions directly in the living brain, to follow the evolution of disease activity over time and to visualise subclinical pathology in the brain. In response to this development, an expert group published new diagnostic criteria in 2001, which took into account MRI evidence for dissemination in time and space [18]. These criteria were revised and simplified once more in 2005 [19], and a further revision is underway. A recent proposal from the MAGNIMS consortium of experts in imaging in multiple sclerosis suggests that it may be possible to demonstrate dissemination in time and space, and thus assign a diagnosis of multiple sclerosis, from a single MRI scan in patients presenting with a clinically isolated syndrome (CIS) [20]. The consequence of the application of MRI criteria to the diagnosis of multiple sclerosis is that patients receive a diagnosis earlier, when their disease is less clinically active. The use of the McDonald criteria for defining eligibility for inclusion in clinical trials since 2001 means that patients are being included earlier in the course of their disease. The changing goalposts for the inclusion of patients in clinical trials are a potential source of artefact when comparing treatment outcomes between trials. This is generated by stage migration, also known as the Will Rogers phenomenon [21]. In multiple sclerosis, such a process can be observed following the introduction of the McDonald diagnostic criteria, which allows earlier assignment of a diagnosis of multiple sclerosis in patients with a CIS [22]. We evaluated the probability of reaching a disability threshold of EDSS 3 in a population of 309 patients originally presenting with a CIS who were evaluated a year later and assigned a confirmed diagnosis of multiple sclerosis according to either the Poser or the McDonald criteria. This was the case for 16% of the cohort using the Poser criteria and for 44% using the McDonald criteria. The entire cohort was then followed for a median duration of 84 months. The probability of reaching EDSS 3 was lower (46%) in the patients who had received a diagnosis of multiple sclerosis using the McDonald criteria (27%) than in those fulfilling the Poser criteria (46%). Similarly, this probability was also lower for the CIS patients who failed the McDonald criteria (7%) than in those who failed the Poser criteria (11%). The use of the McDonald criteria thus improves the prognosis of both the CIS and the multiple sclerosis subgroup, due to the transfer of high-risk CIS patients to the multiple sclerosis group, a clear example of the Will Rogers phenomenon [22]. Comparing outcome data between clinical trials The introduction of the McDonald criteria has certainly had an impact on the treatment effect sizes measured in clinical trials. If the annualised relapse rates observed in randomised controlled trials are compared, a striking reduction can be observed between the historical period, when on-treatment relapse rates ranged from 0.5 to 0.87, and more recent studies performed since 2003, when these rates have ranged from 0.16 to 0.37 (Fig. 3). Although at first sight this may suggest that newer treatments are more effective, this may certainly not be the entire explanation, On-treatment annualised relapse rate IFNβ 1b Glatiramer acetate IFNβ 1a i.m. IFNβ 1a s.c. Natalizumab FTY720 Cladribine Historic Modern Fig. 3. On-treatment annualised relapse rates in randomised controlled trials of disease-modifying drugs in multiple sclerosis.

5 X. Montalban / Journal of the Neurological Sciences 311 S1 (2011) S35 S42 S39 Annualised relapse rates Placebo Year Fig. 4. Annualised relapse rates in the placebo group of randomised controlled trials in relapsing remitting multiple sclerosis as a function of publication date. The lines correspond to the best fit to a linear regression weighted for study size. Solid diamond and solid line correspond to relapses defined with a minimum duration of 24 hours. Open circle and broken lines correspond to relapses defined with a minimal duration of 48 hours. Adapted from Inusah et al. [23], 2010 with permission. since a similar decrease can be observed in the placebo group of these trials. A recent report has analysed relapse rates measured in clinical trials in RRMS published over the last fifty years [23]. This demonstrated a downward trend in the relapse rate over time in both the placebo and active treatment arms. The data for the placebo group are illustrated in Fig. 4. The reduction in relapse rate corresponds to 0.36 fewer annual relapses per decade. This downward trend was observed regardless of how relapses were defined (minimal duration of 24 or 48 hours) and independently of the age of the patients at inclusion. The authors of this study considered a number of possible explanations for these observations, including inclusion of patients with less active disease, more accurate determination of relapses, improvements of overall management of patients with multiple sclerosis and changes in diagnostic criteria. They concluded that none of these explanations was entirely satisfactory and proposed instead that the downward trend could be attributed to removal of patients from a trial in the event of a relapse in order to start them on an existing proven therapy. The consequence of clinicians employing such rescue strategies would be to decrease the likelihood of documenting multiple on-trial relapses and thus artificially to truncate the top end of the relapse rate distribution. A consequence of this change over time is that it is not possible to compare outcomes between different clinical trials because of the differential availability of rescue therapies and because the eligibility criteria are also different, leading to inclusion of patients with different baseline characteristics. The fact that the behaviour of the placebo group may vary in an unpredictable way between trials also compromises comparisons between trials, as the effect size of an experimental treatment is usually determined with respect to the placebo group. Treatment effects with respect to placebo can be expressed as either absolute or relative reductions in relapse rate. In principle, assuming all populations are at the same risk of having a relapse, then relative risk reduction should be constant across treatments with the same efficacy. However, the patients that actually get included in clinical trials usually do differ in their intrinsic relapse risk, and this translates into a different number of events in the placebo arm of the trial. For an identical absolute reduction in the number of relapses conferred by the treatment, the higher the number of events in the placebo group, the lower will be the relative risk reduction measured [24] (Fig. 5). The question that then arises is whether the best indicator of treatment effect is the absolute or the relative risk reduction. This is not a trivial issue when attempting to compare the relative efficacy Relative risk of relapse Drug X = 0.5 absolute 33% relative Drug Y = 0.5 absolute 50% relative Drug Z = 0.5 absolute 66% relative Fig. 5. Absolute and relative risk reductions for the risk of relapse with respect to placebo for three hypothetical treatments tested in three clinical trial populations with different intrinsic risks of relapses. Adapted from reference [24] with permission. of different treatments across trials. For example, in the pivotal clinical trials of interferon-b [25 27] and of glatiramer acetate [11], the absolute risk reduction observed ranged from 0.15 to 0.43 relapses per year, which corresponded to a relative risk reduction of 18% to 34%. More recently, the pivotal placebo-controlled clinical trials of natalizumab [28], fingolimod [29] and cladribine [13] have reported relative risk reductions in the range of 55% to 68%, twoto three- fold higher than those observed for the first-generation therapies. However, when expressed as absolute risk reduction, the treatment effect sizes (0.18 to 0.5 fewer relapses per year) are in fact quite similar to those seen with the first-generation therapies. Similar difficulties with comparing efficacy of different treatments can be encountered whatever the outcome measure. For example, the time to first on-trial relapse has been used as a secondary efficacy measure in most pivotal trials. Although this was prolonged compared to placebo in the active treatment arms of all trials, the difference was not always clinically and statistically significant. In the pivotal trials of interferon-b 1b [27] and subcutaneous interferon-b 1a [26], time to first relapse was increased around twofold in the interferon-b treatment arms compared to the placebo arm. In contrast, in the trials of intramuscular interferon-b 1a [25] and glatiramer acetate [11], effects were more modest and not statistically significant. At first sight, this would imply a real difference between these treatments. However, when direct head-to-head trials were performed comparing high-dose interferon-b to glatiramer acetate (REGARD [30] and BEYOND [31]), no differences in time to first relapse were observed. Similarly, when the proportion of relapse-free patients is considered, cursory inspection of the data from placebo-controlled trials would suggest that high-dose interferon-b [26,27] and fingolimod [29] would have a more robust treatment effect than intramuscular interferon-b 1a [25] or glatiramer acetate [11]. However, in direct comparative trials, no advantage with regard to the proportion of relapse-free patients was observed for high-dose interferon-b over glatiramer acetate [30,31] whereas for fingolimod over intramuscular interferon-b 1a the difference was only 10% [32]. The lessons to be drawn from such inconclusive attempts to compare relative treatment effects across trials is that direct headto-head comparisons are the only way to generate unambiguous answers that are not confounded by differences in study populations, study design, statistical power and behaviour of the placebo group. Assessing treatment non-responders and high-risk patients Another difference between patients participating in current trials and the subjects of historical trials is that effective treatments are now available. A consequence of this is that a high proportion of treatment non-responders are likely to be included in contemporary trials. If patients respond well to available disease-modifying

6 S40 X. Montalban / Journal of the Neurological Sciences 311 S1 (2011) S35 S42 Free of disease (%) Absolute difference 29.5% / /600 Placebo Natalizumab Fig. 6. Proportion of patients free from disease in the AFFIRM pivotal randomised placebo-controlled trial of natalizumab. Adapted from reference [37]. treatments and their disease is stabilised, they and their physicians are likely to be unwilling to jeopardise these benefits by participation in a trial where there is a high risk of being randomised either to placebo or to a treatment of unknown efficacy and safety. Treatment failures, on the other hand, may be more likely to participate. Post hoc analyses to determine benefit in special patient groups may also be called for in case of safety issues precluding generalised use. A case in point is the subgroup analysis performed in patients with highly active disease treated with natalizumab that was conducted in the context of the assessment of this therapy by the National Institute of Clinical Excellence in England and Wales [33]. The agency was concerned about unwarranted risk of PML if natalizumab was made generally available as a firstline therapy for all patients. A subgroup analysis of data from the AFFIRM placebo-controlled pivotal trial of natalizumab [28] was performed, restricted to 219 patients with rapidly-evolving severe relapsing remitting multiple sclerosis, defined by two or more disabling relapses in one year, and one or more gadoliniumenhancing lesions on MRI or a significant increase in T2 lesion load compared with a previous MRI. Such patients comprised around one fifth of all patients included in the AFFIRM trial. This subgroup analysis demonstrated an 81% reduction in annualised relapse rate (p<0.001) and a 64% reduction in the risk of sustained disability progression (p = 0.008) compared to placebo in patients treated with natalizumab. These large and robust treatment effects led to a positive recommendation from the agency for the use of natalizumab in this specific subgroup of patients with highly active disease. The need for new endpoints It is clear that new clinical endpoints are required for clinical trials in multiple sclerosis that will enable promising treatments to be tested more rapidly in smaller cohorts of patients. Also, it is important to identify outcome measures that are relevant not just for inflammation but also for neurodegeneration and tissue repair, since these processes are critical for the progression of irreversible disability. Surrogate markers for screening potential therapies in proofof-concept studies are potentially available. Tracking of contrastenhancing lesions as a surrogate marker of inflammatory activity has already proved its worth, and it is now important to identify markers with a comparably high performance for neurodegeneration. Considerable research has been invested in MRI techniques, such as brain atrophy, black holes or magnetisation transfer imaging, which appear promising in this respect. This field is reviewed in detail in another article in this supplement by Inglese [34]. Apart from imaging parameters, biological markers of immune system function may also be useful. For example, in a Phase II pilot study of daclizumab [35], the extent of suppression of new contrastenhancing lesions was correlated with the degree of expansion of CD56 (bright) natural killer (NK) cells in vivo [36]. Such biological markers are, however, likely to be highly specific to the mechanism of action of the treatment under evaluation. Although such surrogate markers may be of great use in the future, clinical outcome measures still remain the gold standard at all stages of clinical development, and are likely to remain so for pivotal Phase III clinical trials well into the future. Given the efficacy of current and emerging therapies for multiple sclerosis, it may be timely to redefine what is considered a treatment response, so that future treatments will offer added value to patients over and above what is achievable with currently available therapies. In this respect, remission may be an appropriate and achievable target for future therapies, and freedom from disease has been mooted as a suitable endpoint for future trials [37]. This has been defined as having no relapses, no three-month sustained disease progression, and an absence of active T2 lesions and T1 Gd+ lesions. That such a goal is attainable has been demonstrated in the AFFIRM study of natalizumab, in which five times as many patients were free from disease in the natalizumab group compared to the placebo group (Fig. 6). The potential problems with such a composite measure of freedom from disease is that any one constituent criterion may dominate the others and thus introduce potential floor or ceiling effects. Currently, it is not possible to rank or weight the clinical relevance of these constituent criteria. If such composite criteria come to be used widely in clinical trials, their performance will have to be validated carefully. The risk of unexpected serious adverse events Experience with natalizumab and PML has raised awareness of the risk of unexpected serious adverse events emerging with new treatments targeting the immune system. Cases of PML were only identified with natalizumab once the treatment had been licensed and made available for everyday practice [38]. The same is true of the cases of treatment-related acute leukaemia associated with the use of mitoxantrone [39]. These situations have arisen because these serious adverse events are sufficiently rare that their incidence cannot be determined with any precision in pivotal clinical trials with treatment exposure limited to two years and a relatively small number of exposed subjects. With therapies currently in development, serious adverse events are occasionally reported. For example, both in the CLARITY trial of cladribine [13] and the TRANSFORMS trial of fingolimod [32], cases of malignancy and serious opportunistic infections were reported in the active treatment arms more frequently than in the comparator group, although it should be noted that in the placebocontrolled FREEDOMS trial of fingolimod [29], such events were also frequent in the placebo group. With the limited number of patients exposed during these trials, it is not possible to determine whether these events represent a spurious association or a real risk. When new treatments are approved by regulatory agencies, active postmarketing surveillance programmes are generally required as part of a risk management programme aimed at evaluating the level of risk of such serious side-effects as quickly as possible.

7 X. Montalban / Journal of the Neurological Sciences 311 S1 (2011) S35 S42 S41 Challenges for the future With the emergence of more and more disease-modifying therapies for multiple sclerosis therapy and as many experimental therapies under investigation in clinical trials, patients and resources for conducting new trials are becoming scarcer. The major challenge for clinical research is thus to find a more efficient way to conduct trials. It may be useful to promote more investigator-initiated studies, and establish academically based clinical trial units and networks. Multiple sclerosis centres which provide comprehensive care for patients and are responsible for long-term patient followup using standardised protocols and data-basing could provide the cornerstone of such networks. These networks could play a role in prioritising clinical trials so that available resources are channelled towards the most promising projects in terms of patient benefit. In parallel, clinical trial methodology needs to evolve to develop smarter trial designs, which allow information to be gained from shorter studies with fewer patients. This is also necessary in order to address the problem of a falling relapse rate in clinical trial populations, as well as the increasing representation of treatment failures in clinical trials. Innovative designs are also required to confront the ethical issues associated with the use of placebo. Such advances could involve the development of surrogate markers, more sophisticated modelling of prognostic factors or the constitution of virtual placebo groups. Unfortunately, to achieve this, much further basic and clinical research will be needed to characterise the underlying pathophysiology and natural history of multiple sclerosis. In addition, it is highly desirable that pharmaceutical companies initiating clinical trials with new experimental treatments for multiple sclerosis plan carefully prospective long-term extensions of their trials, so that important information on long-term effectiveness and safety can be obtained in the most coherent manner. This information can be complemented with information from prospective cohort studies of patients treated in large multiple sclerosis centres. Implementation of active post-marketing surveillance programmes will be important in order to detect suspected unexpected serious adverse drug reactions in a timely manner and thus increase the confidence with which innovative new treatments can be used in everyday practice. In conclusion, remarkable progress has been made in the treatment of multiple sclerosis over the last 25 years, probably unmatched elsewhere in neurology. However, this success creates new and exciting challenges for the design of clinical trials for the next generation of treatments. Expectations for these are high, and efficacy standards may need to be re-orientated to the treatment goal of achieving sustained complete remission. If all patients can be offered this in everyday care, then a further milestone in the treatment of multiple sclerosis will have been reached. Conflict of interest statement Xavier Montalban has received honoraria for speaking at scientific meetings and for participating in clinical trials as a steering committee member or investigator from Bayer Schering Pharma, Biogen Idec, EMD Merck Serono, Genentech, Genzyme, Novartis, Sanofi-Aventis, Teva Pharmaceuticals and Almirall. References 1. Panitch H, Miller A, Paty D, Weinshenker B. Interferon beta-1b in secondary progressive MS: results from a 3-year controlled study. Neurology 2004;63: European Study Group on interferon beta-1b in secondary progressive MS. 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