Auspar attachment 3: Extract from the Supplementary Clinical Evaluation Report for Daclizumab

4.Pharmacokinetics

Pharmacokinetic data was not assessed by this clinical evaluator. Please see Attachment 2, Extract of the CER for a full evaluation.

5.Pharmacodynamics

Pharmacodynamic data was not assessed by this clinical evaluator. Please see Attachment 2, extract of the CER for a full evaluation.

6.Dosage selection for the pivotal studies

6.1.Dosage finding studies

Dose selection for the pivotal efficacy studies was based on studies in subjects with RRMS, performed with an investigational form of daclizumab (DAC Penzberg), manufactured using a different process and cell line.

According to the sponsor:

‘Dose selection for Study 205MS201 was based on results of the Phase 2 Study DAC-1012, which evaluated 2 different dose regimens using a prior investigational form of daclizumab (DAC Penzberg): a high-dose 2 mg/kg subcutaneous (SC) every 2 weeks regimen (equivalent of 300 mg every 4 weeks for a 75 kg body weight) and the low-dose 1 mg/kg subcutaneously every 4 weeks regimen (equivalent of 75 mg every 4 weeks for a 75 kg body weight).’

‘Compared with placebo the effect of DAC Penzberg on reducing new gadolinium (Gd) enhancing lesions, the primary endpoint of Study DAC-1012, was robust and statistically significant in the high-dose arm 2 mg/kg every 2 weeks (p = 0.0038), but was marginal and not statistically significant in the low-dose arm 1 mg/kg every 4 weeks (p = 0.5138). Safety was similar between the low-dose and high-dose regimens. Based on the results of Study DAC-1012, two DAC HYP dosing regimens (150 mg and 300 mg SC every 4 weeks) were selected for further evaluation in Study 205MS201 based on the following considerations:

The low-dose regimen from Study DAC-1012, which is approximately equivalent to a fixed-dose regimen of 75 mg SC every 4 weeks, was considered to be below the lowest efficacious dose. Furthermore, this regimen showed no evidence for an improved safety profile compared to the high-dose regimen. Therefore, DAC HYP doses that were expected to provide similar exposures were not evaluated further.

DAC HYP 300 mg SC every 4 weeks was projected to be approximately equal to the highest efficacious dose (2 mg/kg SC every 2 weeks) evaluated in Study DAC-1012.

DAC HYP 150 mg SC every 4 weeks was projected to be a lowest efficacious dose since it was between the low-dose and high-dose arms in Study DAC-1012.’

6.2.Evaluator’s overall conclusions on dose selection

A full evaluation of these claims is beyond the scope of this SCER, but the sponsor’s selection of 150mg and 300mg as doses worthy of further study appears broadly reasonable.

Based on the results of DAC-1012, 150 mg SC 4-weekly and 300 mg SC 4-weekly were selected for the Phase 2 placebo-controlled study, 205MS201 (later designated as a pivotal study). In Study 205MS201, no difference in efficacy was observed between the 150 mg and 300 mg doses, so the lower dose was selected for the Phase 3 active-controlled study, 205MS301.

As noted by the First Round clinical evaluator, this development path suggests that efficacy plateaus above 150 mg, but it does not establish with certainty whether lower doses could still achieve comparable efficacy with an improved safety profile. The evidence suggests that, for DAC Penzberg, the optimal dose is greater than 75mg 4-weekly, and may be as high as 300 mg 4-weekly. To the extent that DAC HYP is equivalent to DAC Penzberg, Study 205MS201 further narrows down the optimal dose to somewhere above 75mg and up to 150 mg. It is not clear, though, that a 2-weekly dose with a different preparation of daclizumab is sufficient to guide dosing with a 4-weekly regimen of DAC HYP. Also, there is a two-fold range of doses between 75mg and 150 mg, leaving a wide range of doses untested. This represents a significant deficiency in the study program.

7.Clinical efficacy

7.1.Pivotal efficacy studies

7.1.1.Study 205MS201

Study 205MS201 was a ‘multicentre, double-blind, placebo-controlled, dose-ranging study to determine the safety and efficacy of DAC HYP as a monotherapy treatment in subjects with RRMS.’

7.1.1.1.Study design, objectives, locations and dates

Study 205MS201 (n = 600) was a placebo-controlled, double-blind, dose-ranging study in which two different doses of DAC HYP (the proposed dose of 150 mg, as well as 300 mg) were compared to placebo in subjects with RRMS. Per study report, this study was designated as a Phase 2 study, but was subsequently submitted as a pivotal study. It was only modest in size (600 subjects in the ITT population) and duration (52 weeks), so it would not be considered adequate as a standalone pivotal study. Also, it appears to have been designed with the expectation that 300 mg would be the dose subsequently taken to Phase 3 studies, which creates some difficulties in interpreting the statistical results in the 150 mg group. Despite these limitations, the study had most of the features required for a major MS efficacy study and it can be considered a pivotal study alongside the Phase 3 Study 205MS301 (‘MS301’), which used an active control (IFN-beta-1A) in comparison to a single DAC HYP dose of 150 mg for up to 144 weeks.

The study ran from 15 February 2008 to 30 August 2011, and randomised a total of 621 subjects at 78 sites in 9 countries worldwide: the Czech Republic, Germany, Hungary, India, Poland, Russia, Turkey, the Ukraine, and the United Kingdom.

Inclusion criteria

The main inclusion criteria were:

Male and female subjects between the ages of 18 and 55 years, inclusive

A confirmed diagnosis of RRMS according to McDonald Criteria (numbers: 1 to 4)²

Baseline Expanded Disability Status Scale (EDSS) between 0.0 and 5.0, inclusive

Subjects had experienced at least 1 relapse within the 12 months prior to randomisation with a cranial magnetic resonance imaging (MRI) demonstrating lesions consistent with MS or had shown evidence of Gdenhancing lesions of the brain on an MRI performed within the 6 weeks prior to randomisation.³

The main exclusion criterion was:

• 
  Diagnosis of primary progressive, secondary progressive or progressive relapsing MS.
  

These criteria are reasonably standard in large MS efficacy studies. In combination, the inclusion and exclusion criteria attempted to define a cohort of subjects with active RRMS but no substantial ongoing disease progression. The requirement for either one relapse in the last 12 months or an active Gd lesion on MRI ensured that subjects with quiescent disease were not eligible. It is less clear that subjects with secondary progressive or progressive relapsing MS (SPMS or PRMS) were successfully excluded. It seems likely that many subjects with higher EDSS scores at baseline had, in part, reached a progressive phase of their illness, in which identifiable relapses were superimposed on a slowly progressive course. In practice, it is very difficult to distinguish the accumulation of disability that is due to incomplete recovery from relapses from disability that has increased between overt relapses, and the distinction is somewhat artificial, given that many radiological relapses are not recognise clinically. Notionally, SPMS and PRMS were listed as exclusion criteria, but the definitions of these categories required 3 months of continuous worsening, which may be very difficult to identify in clinical practice. Subjects with insidious progression might not get clearly worse over 3 months. Subjects with a fluctuating course including some accelerated periods of worsening around the time of their relapses could be classified by one neurologist as RRMS and by another as SPMS. Because of these ambiguities, subjects could have entered this study despite having SPMS or RPMS.

This is a problem faced by all major studies of RRMS, and the definitional approach taken in this study was acceptable. The same difficulty is faced by clinicians seeking to commence a disease-modifying agent. The potential inclusion of subjects with SPMS or PRMS is likely to have made it more difficult to demonstrate a treatment benefit, as these subjects are usually more treatment resistant.

A more serious concern is that the entry criteria do not match the target population identified in the sponsor’s proposed PI. The proposed indication is:

‘Zinbryta is indicated for the treatment of relapsing forms of multiple sclerosis (MS).’

PRMS is, by definition, a relapsing form of MS, and would be covered by the proposed indication even though it was an explicit exclusion criterion in this pivotal study. Similarly, most neurologists would consider a diagnosis of SPMS to be compatible with the occasional relapse, and therefore have a relapsing form of MS, which would be covered by the proposed indication. Furthermore, given that all SPMS begins with a relapsing course (by definition), SPMS could be considered a ‘relapsing form’ of MS even when the patient has reached a purely progressive phase. The proposed indication in the PI should therefore be reworded to match the entry criteria of the pivotal studies.

Because of the broad range of EDSS scores permitted on study entry, it is also important to confirm whether the benefits were demonstrated across the full EDSS spectrum, making subgroup analyses particularly important.

Additional entry criteria were based on excluding: subjects with significant coexistent illnesses; those in whom exposure to an immune modifying agent could pose an unacceptable risk; and those in whom assessment of efficacy could be difficult because of use of other immune-modifying or disease-modifying agents.

7.1.1.2.Study treatments

Subjects were randomised to one of three regimens in a 1:1:1 ratio:

Placebo, administered by SC injection every 4 weeks

DAC HYP 150 mg, administered by SC injection every 4 weeks

DAC HYP 300 mg, administered by SC injection every 4 weeks

There was no dose titration phase. The planned duration of treatment was 52-weeks with an opportunity to enter a blinded extension study, Study 205MS202. The extension study is not described in this SCER.

Comment: For a description and evaluation of Study 205MS202 (the extension to Study 205MS201) please see Attachment 2, extract of the CER.

Figure 2. Study design, Study 205MS201

Rescue therapy with IFN-β was permitted for ethical reasons, to minimise the potential risks of untreated MS in the placebo arm. At the discretion of the treating clinician, IFN-β was used concomitantly with blinded study drug, starting at or after Month 6, provided the relapse had been confirmed by the Independent Neurology Evaluation Committee (INEC). Apart from rescue IFN-β, other disease-modifying agents were not allowed.

Intravenous methylprednisolone was allowed for treatment of relapses. All other systemic steroid therapy was prohibited.

Symptomatic therapy for spasticity, depression, or fatigue was allowed but clinicians were asked to optimise these as early as possible during screening in an attempt to maintain consistent treatments during the study.

7.1.1.3.Efficacy variables and outcomes

The main efficacy variables were:

Brain MRI outcomes:

Total number of new Gd-enhancing lesions (Gd-enhancing lesions not present on MRI scan performed 4 weeks prior)

New or newly-enlarging T2 hyperintense lesions⁴

Volume of new T1 hypointense lesions

Volume of new or newly-enlarging T2 hyperintense lesions

Volume of non-Gd enhancing T1 hypointense (‘blackholes’) lesions

Brain atrophy

Clinical outcomes:

Clinical relapses

EDSS

Subject Global Assessment (as measured by the Visual Analogue Scale)

Quality of life (QoL) questionnaires (EQ-5D, SF 12, and Multiple Sclerosis Impact Scale-29 (MSIS-29))

Relapses that were determined to meet protocol-defined criteria were subsequently evaluated by the Independent Neurology Evaluation Committee (INEC).

Primary efficacy outcome

The primary efficacy outcome was based on the Annualised Relapse Rate (ARR) between baseline and Week 52, calculated by dividing the number of relapses in each group by the total patient exposure in years.

This is an appropriate primary outcome. The ARR has been used in the majority of MS studies for decades. The primary endpoint used an adjusted form of the ARR, as is standard for MS studies of this nature, with statistical adjustments made on the basis of baseline prognostic factors (relapses, EDSS and age). As per study report:

‘The primary analysis evaluated differences in the annualised relapse rate between each DAC HYP group versus placebo using a negative binomial regression model adjusting for the number of relapses in the year before study entry, baseline EDSS (EDSS ≤ 2.5 versus EDSS > 2.5 points), and baseline age (≤ 35 versus > 35 years).’

Secondary efficacy outcomes

Secondary efficacy outcomes included:

The number of new Gd-enhancing lesions over 5 brain MRI scans at Weeks 8, 12, 16, 20, and 24 (calculated as the sum of these 5 MRIs) in a subset of subjects

The number of new or newly-enlarging T2 hyperintense lesions at Week 52

The proportion of relapsing subjects between baseline and Week 52

QoL as measured by the MSIS-29 physical score at Week 52 compared to baseline.

These secondary endpoints were also reasonable. It is standard practice in MS studies to use radiological markers of disease activity as secondary endpoints. Radiological markers have the advantage of being objective and MRI is usually more sensitive than clinical relapse rate because many plaques may be clinically silent. On the other hand, a treatment that merely improved MRI markers without preventing neuronal dysfunction and disability would not be particularly useful, so MRI markers are not suitable as primary endpoints. Gd lesions are indicators of local breakdown of the blood-brain barrier (BBB), which in the context of MS indicates probable inflammation. T2-weighted MRI is sensitive to water content, which increases in plaques and in other inflammatory areas, so enlarging or new T2 hyperintense lesions in an MS population are likely to indicate plaque growth; isolated lesions could be due to small vessel ischaemia, instead, but in an MS population a plaque is a more likely cause.

The proportion of relapsing subjects, which was used as a secondary endpoint, is also of interest, though it is strongly linked to ARR and generally does not provide major insights not already captured in ARR. Unlike ARR, this endpoint disregards second and subsequent in-study relapses from individuals, so it may be less sensitive to the inclusion of subjects with unusually aggressive disease and multiple relapses.

It is appropriate for a study in MS to use a measure of QoL and MSIS-29 is one validated tool suitable for this purpose. Unfortunately, this measure is subjective, and could potentially be affected by unblinding or other biases.

Other efficacy outcomes

Tertiary study objectives are listed below (as per study report) and included some safety assessments as well as efficacy measures:

‘Tertiary objectives of this study were to determine:

The efficacy of DAC HYP in slowing the progression of disability as measured by at least a 1.0 point increase on the EDSS from baseline EDSS ≥1.0 that was sustained for 12 weeks, or at least a 1.5 point increase on the EDSS from baseline EDSS = 0 that was sustained for 12 weeks

The efficacy of DAC HYP in reducing the number of new or newly-enlarging T2 hyperintense lesions at Week 24 compared to baseline

The efficacy of DAC HYP in reducing the number of Gd-enhancing lesions at Week 52 compared to baseline

The efficacy of DAC HYP in reducing the volume of new T1 hypointense lesions at Week 24 compared to baseline and at Week 52 compared to baseline

The efficacy of DAC HYP in reducing the total lesion volume of new and newly enlarging T2 hyperintense lesions at Week 24 compared to baseline and at Week 52 compared to baseline

The efficacy of DAC HYP in reducing the volume of non-Gd enhancing T1 hypointense (‘blackholes’) lesions at Week 24 compared to baseline and at Week 52 compared to baseline

The efficacy of DAC HYP in reducing brain atrophy on MRI at Week 24 over the 52-week treatment period

The efficacy of DAC HYP in reducing the total lesion volume of T2 hyperintense lesions over the 52-week treatment period

The safety and tolerability of DAC HYP in subjects who have active, relapsing remitting forms of MS

The efficacy of DAC HYP in slowing the time to relapse

The efficacy of DAC HYP on slowing disability progression as measured by the change in EDSS from baseline to Week 52

The efficacy of DAC HYP in improving the subject’s global impression of well-being as measured by a Visual Analogue Scale

The efficacy of DAC HYP in improving quality of life as measured by the MSIS-29 psychological scale, the SF-12 Health Survey (SF-12), and the EQ-5D Health Survey (EQ-5D).’

Disability progression

Of note, none of the primary or secondary endpoints in Study 205MS201 included a measure of disability progression, which was instead listed as the first of 13 tertiary endpoints.

Disability progression was defined as a 1-point worsening of the EDSS, sustained for 12 weeks. (In the case of subjects with a baseline EDSS of 0, a 1.5 worsening was required, which helps to ensure that the disability is clinically significant). This is a standard definition, similar to many other MS studies, which have also defined disability as a sustained EDSS worsening.

The requirement for EDSS worsening to last 12 weeks has two main effects: it gives subjects 12 weeks to recover from a relapse, making it less likely that a relapse will be misinterpreted as disability progression; it also means that, in a 52-week study, subjects must exhibit worsening within 40 weeks of the start of the study. A requirement for longer periods of sustained worsening would be expected to be more specific for true progression, but the endpoint would be less sensitive because of the shorter time period available in which the disability would need to start in order to be counted. For a 52-week study, a 12-week period of sustained worsening is an appropriate compromise.

Guidelines for the conduct of MS studies strongly argue that an ideal MS treatment would be one that slowed disease progression. Ultimately, the accumulation of disability is a major concern for patients and their clinicians. Despite this, most MS treatments currently available reached the market on the strength of their ability to prevent relapses. Many treatments have since been shown to reduce disability progression, as well, but the benefits for this endpoint are less clear cut than the benefits on relapse rate. This partly reflects the fact that disability may be less responsive to immune-modifying treatment, but it may also reflect the fact that disability endpoints are less sensitive than relapse rates for purely methodological reasons. These reasons include the difficulties in distinguishing progression from relapses and the slow rate of progression relative to study duration. Despite its clinical importance, disability progression has often been treated as a minor endpoint in pivotal MS studies, as in this study.

7.1.1.4.Randomisation and blinding methods

Subjects were randomised to each of the three treatment arms in a 1:1:1 ratio, using an Interactive Voice Response System (IVRS).

Blinding was attempted by using identical appearing SC syringes in all three treatment arms, and by using randomisation codes that were not available to clinicians involved in the treatment and rating of patients.

It is possible that unblinding occurred because of tell-tale side effects, such as cutaneous reactions to DAC HYP.

The study took appropriate steps to separate treating and rating clinicians, as follows:

‘To further protect the blind during the study, a separate treating neurologist and examining neurologist were designated at each investigational site. The treating neurologist functioned as the primary treating physician during the study. The examining neurologist conducted all EDSS evaluations and relapse assessments but was not involved in any other aspect of subject care and was instructed to limit all interactions with subjects to the minimum necessary to perform the required neurologic examinations. The examining neurologist remained blinded to treatment, AEs, concomitant medications, laboratory data, MRI data, and any other data that had the potential of revealing the treatment assignment.’

The sponsor apparently made no attempt to assess the degree of unblinding, which could have been achieved by asking subjects to guess their assigned treatment.

7.1.1.5.Analysis populations

The sponsor defined three study populations:

Intent-to-treat (ITT) population: all randomised subjects who received at least 1 dose of study treatment. Note that subjects from one site were prospectively excluded because of systematic misdosing by the unblinded pharmacist.

Efficacy-evaluable (EE) population: all subjects in the ITT population who had no missing MRI data from Weeks 8, 12, 16, 20, and 24 and did not take prohibited alternative MS medications.

Safety population: all subjects who received at least 1 dose of study treatment and had at least 1 post-baseline assessment of the safety parameter being analysed.

The primary efficacy analysis was performed on the ITT population. The number of new Gd-enhancing lesions was evaluated using the EE population, and safety analyses were performed with the safety population.

7.1.1.6.Statistical methods

The primary endpoint was the difference in ARR between each active treatment and placebo. The primary analysis evaluated these differences with a negative binomial regression model, adjusting for the number of relapses in the year before study entry, the baseline EDSS (EDSS ≤ 2.5 versus EDSS > 2.5 points), and the baseline age (≤ 35 versus > 35 years). A traditional significance level of p ≤ 0.05 was used.

The use of two active dose groups increases the chance of finding a significant difference relative to placebo in at least one active group. To control for this multiplicity, a sequential closed testing procedure was used to evaluate the dose groups. Statistical testing for efficacy endpoints used separate comparisons of the DAC HYP 300 mg group versus placebo and the DAC HYP 150 mg group versus placebo. Only if the comparison of 300 mg versus placebo was statistically significant (p ≤ 0.05), was the comparison of 150 mg versus placebo to be tested. If the first comparison (300 mg) was not statistically significant, then the second comparison (150 mg) was not to be considered statistically significant, regardless of the p-value.

Secondary and other endpoints were summarised by treatment group, and tested for treatment differences by a number of different prospectively specified techniques:

negative binomial regression (for number of new Gd+ lesions between Weeks 8 and 24, number of new or newly-enlarging T2 hyperintense lesions)

a Cox-proportional hazards model (for time to first relapse, time to disability progression)

an ordinal logistic regression model (for number of Gd+ lesions at Week 52)

an analysis of covariance (ANCOVA) model (for change in EDSS, volume of new or enlarging T2 hyperintense lesions, volume of new T1 hypointense lesions, and QoL)

Kaplan–Meier survival curve distribution (for the proportion of subjects who were relapse-free and the proportion of subjects who were progression-free).

To control for multiplicity of endpoints, secondary endpoints were rank prioritized, and if statistical significance was not achieved for an endpoint, endpoints of a lower rank were not considered significant.

Tertiary analyses including analysis of disability progression did not include any adjustments for multiplicity.

Overall, these analytical methods were broadly appropriate, but the tertiary endpoint analysis cannot be considered robust because of the lack of correction for multiplicity. Also, in reporting the benefits of active treatment on the proportion of subjects relapsing, the sponsor used an approach based directly on hazard ratios, with the result that the reported figures were inappropriately inflated. This issue is discussed in the results section for this study.

The statistical analysis plan was specified prospectively, but some additional analyses, which are a major focus of this supplementary evaluation report, were conducted in response to suggestions from the EMA, including a post-hoc analysis of the results according to baseline categorisation of subjects as having ‘high disease activity’ or ‘low disease activity’.

Although these additional analyses were potentially informative, they cannot be considered statistically robust because of their post hoc nature.

7.1.1.7.Sample size

The sponsor justified the sample size as follows:

‘It was assumed that if subjects were not allowed to add IFN-β during the study, the annualised relapse rate in the placebo group would be 0.50; however, because subjects were permitted to add IFN-β as a treatment for relapse, the annualised relapse rate in the placebo group would be reduced to 0.476 while the rate in the DAC HYP group would stay the same. In this setting, a sample size of 198 subjects per treatment group would have approximately 90% power to detect a 50% reduction in the annualized relapse rate between a DAC HYP treatment group and placebo. Power was estimated from simulations assuming a negative binomial distribution, a 10% drop out rate, and a 5% type 1 error rate. Based on these assumptions, a sample size of 594 subjects would be required for the study.’

These estimates appear reasonable, and the observed ARR in the placebo group (0.462) was very similar to the prospective estimate of 0.476. Furthermore, the study easily achieved statistical significance for its primary endpoint, indicating that it was, in fact, adequately powered for this endpoint.

The study was not specifically powered for the tertiary endpoint of disability progression, and did not show a significant benefit for this endpoint.

7.1.1.8.Participant flow

A total of 621 subjects were randomised and all received study treatment. Due to systematic, non-random treatment at Site 93, a total of 21 subjects were excluded from the ITT population, leaving 196 subjects in the placebo group, 201 in the DAC HYP 150 mg group and 203 in the DAC HYP 300 mg group.

Of these, 186 completed placebo treatment, 189 completed DAC HYP 150 mg treatment, and 192 completed DAC HYP 300 mg treatment. A small number of subjects in each group completed treatment but did not complete the full follow-up period, as shown in the figure below; in some cases this reflects the enrolment of those subjects in the follow-up extension study.

Figure 3. Participant flow and subject disposition, Study 205MS201

The reported completion rate constitutes fairly good follow-up for a complex study of this nature, and the withdrawals appear reasonably well-balanced across the three treatment groups. The most common reason for early discontinuation was withdrawal of consent, but adverse events (AEs) were more commonly listed as the reason for withdrawal in the active groups, which raises the possibility of withdrawal bias or unblinding.

7.1.1.9.Major protocol violations/deviations

The most serious protocol deviations occurred at Site 93, which was closed for study misconduct after it was discovered that the pharmacist dosed all 21 subjects with active DAC HYP rather than the randomised treatment assignments, including placebo. Data from these subjects were appropriately and prospectively excluded from the primary analysis. The sponsor also carried out sensitivity analyses that included the censored data, and this had no major effect on the results.

A clear summary table of all major protocol deviations was not provided, but has been requested as a clinical question to the sponsor.

7.1.1.10.Baseline data

Baseline demographics were similar across treatment groups. Baseline disease characteristics are summarised in Tables 1 to 4 below. The distribution of concomitant diseases, MS duration and the proportions of patients satisfying individual McDonald criteria were similar across groups. The relapse history was also similar across groups, including the number of relapses in the previous 3 years and previous 12 months, as well as the mean and median time since the last relapse before study entry.

Table 1. Medical history of subjects, Study 205MS201

Table 2. MS history for subjects, Study 205MS201

Table 3. McDonald Criteria for subjects, Study 205MS201

Table 4. Relapse history of subjects, Study 205MS201

For radiological markers of disease severity, there was a slight imbalance across groups, suggesting more active disease in the 150 mg group compared to the placebo and 300 mg groups.

Across the entire study population, the average number of Gd lesions on the baseline MRI was 1.8 ± 3.78, and 44% of subjects had ≥ 1 Gd lesion. The median volume of T2 lesions was 4563.7 mm³. The proportion of subjects with 1 Gd-enhancing lesion on the baseline MRI was higher than average in the DAC HYP 150 mg group: 52%, compared to 45% and 37% in the placebo and DAC HYP 300 mg groups, respectively. Similarly, the median volume of T2 hyperintense lesions was higher in the 150mg group: 5392 mm³ in the DAC HYP 150 mg group, compared to 4492 mm³ and 4113 mm³ in the placebo and DAC HYP 300 mg groups, respectively.

These values were misquoted in the study report, as follows:

‘The median volume of T2 hyperintense lesions was 5392 mm³ in the DAC HYP 150 mg group compared to 4492 mm³ in the DAC HYP 150 mg (sic) group and 4113 mm³ in the placebo (sic) group.’

Table 5. Volume of T2 hyperintense lesions (mm³) at baseline, Study 205MS201

Because they had more active scans, the 150 mg group might be expected to have more relapses during the study, which could potentially bias the study slightly against the 150 mg group for the primary endpoint of ARR. On the other hand, because a high proportion of subjects were having a radiological relapse at baseline, some clinical improvement in EDSS could be expected to arise purely from recovery from baseline relapses; this effect could disguise some progression; potentially this effect could have been more prominent in the 150 mg group. Overall, the discrepancy between groups for this baseline measure was minor and the groups were well-matched for clinical relapse history, so it is not expected to have modified the findings significantly. Also, post hoc comparisons of disability progression for subjects with high and low baseline disease activity did not find a major difference in the estimates of the treatment effect.

Overall, the treatment groups were adequately balanced and they were representative of the population in which DAC HYP would be used.

7.1.1.11.Results for the primary efficacy outcome

The ARR at 52 weeks was significantly lower for subjects randomised to active treatment, relative to the ARR observed with placebo. The adjusted ARR was 0.458 relapses/year in the placebo group, compared to 0.211 in the DAC HYP 150 mg group (a 54% relative reduction; 95% confidence interval (CI), 33% to 68%; p < 0.0001), and 0.230 in the DAC HYP 300 mg group (a 50% relative reduction; 95% CI, 28% to 65%; p = 0.0002). These results are summarised in the table below, reproduced from the sponsor’s submission.

The meaning of the p-values cited next to footnote ‘b’ in the sponsor’s table (see Table 6) was not clear, and the sponsor should be asked to clarify this.

Table 6. Annualised relapse rate by study treatment, Study 205MS201

The observed reduction in relapse rate (approximately 50 to 54%, depending on which dose group is considered) is clinically meaningful and resembles the reported reductions in ARR observed in other recent pivotal studies of different disease-modifying agents, including fingolimod and dimethyl fumarate (BG-12). For the pivotal placebo-controlled fingolimod trial, the ARR was 0.18 in the active group, compared to 0.40 in the placebo group, a relative reduction of 55% (p < 0.001). In the pivotal study of dimethyl fumarate, the reduction in ARR was also similar:

‘The annualised relapse rate at 2 years was 0.17 in the twice-daily BG-12 group and 0.19 in the thrice-daily BG-12 group, as compared with 0.36 in the placebo group, representing relative reductions of 53% and 48% with the two BG-12 regimens, respectively (p < 0.001 for the comparison of each BG-12 regimen with placebo).’⁵

Although comparisons across studies are not formally valid, these relatively recent studies had broadly similar entry criteria and definitions of relapse rate, as well as a similar relapse rate in their respective placebo groups, so they provide useful context for the findings in Study 205MS201.

The first disease-modifying treatments to be marketed for MS, including IFN-β and glatiramer acetate, were associated with an apparent reduction in relapse rate of approximately 30%, but those earlier studies may have recruited a more advanced cohort of MS patients. There has been a general trend to earlier treatment and to more favourable results in recent MS studies, compared to the initial studies performed in the 1990s, so comparison across treatment eras is unreliable.

Given that individual relapses are themselves unpleasant and often disabling, patients would be expected to welcome any treatment that reduced relapses by approximately 50 to 54%. As some accumulation of disability in MS is directly related to incomplete recovery from individual relapses, the prevention of half the expected number of relapses would be expected to reduce long-term disability.

Unfortunately, as discussed elsewhere in this report, the extent to which reductions in ARR correlate with improvements in disease progression has been generally disappointing in MS research. It is therefore necessary to demonstrate such benefits directly. In this study, as will be discussed, a direct benefit in terms of EDSS progression was only confirmed for some progression-related endpoints, but not for the main prospectively identified progression endpoint.

The sponsor also performed a number of additional analyses of the primary efficacy variable, using a variety of statistical techniques, with and without censoring of relapses after rescue therapy, and including unconfirmed relapses. The sponsor performed an analysis in which they only adjusted the ARR for relapses at baseline, instead of relapses, age and EDSS. As shown in the figure below, all of these sensitivity analyses produced concordant results, suggesting that the results of the primary analysis are robust, and did not depend strongly on arbitrary methodological choices.

Figure 4. Primary and additional analyses of annualised relapse rate, Study 205MS201

Overall, these primary efficacy results appear statistically and clinically robust. There was a slight trend in favour of the 150 mg dose over the 300 mg dose, but no formal dose comparison was attempted and the study was not powered to compare the two active doses. The clear superiority of both active doses over placebo and the lack of any substantial differences in the 150 mg and 300 mg groups broadly justify the sponsor’s subsequent development of 150 mg in favour of 300 mg, but leave open the possibility that lower doses could have had comparable efficacy and improve safety.

7.1.1.12.Results for other efficacy outcomes

Radiological measures

Gd-enhanced MRI scans were obtained at Weeks 8, 12, 16, 20, and 24 in a subset of subjects. With active treatment, the number of new Gd-enhancing lesions (calculated as the sum of new lesions across these 5 MRIs) was reduced versus placebo. DAC HYP 150 mg and 300 mg reduced the number of new Gd-enhancing lesions by 69% (p < 0.0001) and 78% (p < 0.0001) respectively, compared to placebo. This result appeared to be robust in a variety of sensitivity analyses, as shown in the Forest plot (Figure 5) below.

Figure 5. New Gd-enhancing lesions, primary and sensitivity analyses, Study 205MS201

New or newly-enlarging T2 hyperintense lesions at Week 52

The MRI data also suggested a substantial reduction in the development of T2 lesions. The adjusted mean number of new or newly enlarging T2 hyperintense lesions at Week 52 was 8.13 (95% CI: 6.65 to 9.94) in the placebo group, compared to 2.42 (95% CI: 1.96 to 2.99) in the DAC HYP 150 mg group (p < 0.0001) and 1.73 (95% CI: 1.39 to 2.15) in the DAC HYP 300 mg group (p < 0.0001). The relative reduction in the number of new or newly enlarging T2 lesions, compared to placebo, was 70% for DAC HYP 150 mg (p < 0.0001) and 79% for DAC HYP 300 mg (p < 0.0001), respectively.

Proportion of relapsing subjects

The Kaplan-Meier estimate for the proportion of subjects who relapsed by Week 52 was 36% in the placebo group, compared to 19% in the DAC HYP 150 mg and 20% in the DAC HYP 300 mg group. The hazard ratio was 0.45 (95% CI: 0.30 to 0.67; p < 0.0001) in the DAC HYP 150 mg group compared to placebo and 0.49 (95% CI: 0.33 to 0.72; p < 0.0003) in the DAC HYP 300 mg group compared to placebo.

The sponsor and the previous CER have suggested that these results indicate that the proportion of relapsing subjects was reduced by 55% in the DAC HYP 150 mg group and by 51% in the DAC HYP 300 mg group, compared to placebo. This does not represent an accurate description of the results. The 55% and 51% reductions appear to have been derived directly from the hazard ratios of 0.45 and 0.49, respectively, and thus refer to the reduction in the proportion relapsing from the ‘at-risk’ (not-yet-relapsed) group at any one moment in time, but do not apply to the cohort over the 52-week time period as a whole. The cited reductions are not plausible. The proportion relapsing in the placebo group was 36%, so if the relative reduction in the proportion relapsing on active treatment was 50%, then 18% of those on active treatment (half of 36%) would have relapsed. Instead, more than 18% of subjects relapsed in both active groups (19% and 20% in the 150 mg and 300 mg groups, respectively), so the proportion relapsing cannot have been reduced by more than 50%.

The relative reduction in the proportion relapsing was actually or 0.47 (47%) for the 150 mg group, and or 0.44 (44%) in the 300 mg group. In other words, for the 150 mg group, the risk of relapse was 0.53 times the risk with placebo (0.5278 x 36% = 19%), and the risk of relapse with 300 mg was 0.56 times the risk with placebo (0.5556 x 36% = 20%). Slightly different values might be obtained if more significant figures were used for the initial proportions. The Study synopsis uses a value of 35% for the proportion relapsing in the placebo group, instead of 36% (possibly due to rounding errors), and if this value were used it would give even lower estimates of the relative reduction with active treatment.

The inflated estimates of risk reduction arise from disregarding the difference between instantaneous hazard ratios and overall risks for a cohort over an extended period of time. The result of conflating these two measures of risk is that the estimates of treatment benefits are exaggerated. By definition, instantaneous hazard ratios ignore subjects who have already experienced the hazard event, and are therefore based on a shrinking denominator, but clinical intuition and decision-making are based on the overall proportion of subjects experiencing the hazard event in a clinically meaningful time period, such as a year of treatment, and use the entire cohort as the denominator.

A review of the documents provided with the submission shows that this error is repeated throughout the submission, and it has been subsequently accepted in good faith by the First Round clinical evaluator. For instance, the Study Report cites the inflated estimates of the reduction in proportion of subjects relapsed (55% for the 150 mg group, instead of 47%; and 51% for the 300 mg group, instead of 44%). The inflated values are also used in the proposed PI, where it is stated that the relative risk reduction for the proportion relapsing on 150 mg was 55%. This should be corrected.

Quality of life

QoL was measured with the MSIS-29 physical score. MSIS-29 scores at Week 52 were compared to baseline. Results for this endpoint were not significant. A p-value that was nominally within the significance range was obtained for the dose group of secondary interest (150 mg) but not for the protocol-specified dose group of primary interest (300 mg). By the prospectively declared sequential closed testing procedure, significance for the 300 mg dose group had to achieve statistical significance before the 150 mg dose group could be tested.

Mean changes in MSIS-29 scores were small compared to the variability within each group, so it is difficult to draw any strong inferences and it is unclear whether the differences observed were clinically meaningful. The mean (± SD) change in the MSIS-29 physical score from baseline to Week 52 was 3.0 (± 13.52) in the placebo group, –1.0 (± 11.80) in the DAC HYP 150 mg group (p = 0.0008 versus placebo), and 1.4 (± 13.53) in the DAC HYP 300 mg group (p = 0.1284 versus placebo).

Even the direction (sign) of the change in MSIS-29 was different across active groups and there was no consistent dose trend.

Overall, this endpoint provides no convincing support for the efficacy of DAC HYP. The sponsor claims that DAC HYP produces benefits in MSIS-29 scores, but this claim is not justified. Where the PI mentions the p-value of 0.0008, it should also mention that this was not formally significant.

Key tertiary endpoint Disability progression

Disability progression, a key tertiary endpoint, was generally underpowered because few subjects demonstrated confirmed disability progression within the time window required and the study was generally too short to provide robust estimates for this endpoint. The overall trends, however, were favourable, and the p-value for the 150 mg group was nominally in the appropriate range (≤ 0.05); this does not imply statistical significance, because the pre-specified approach for handling multiplicity was to use a sequential closed testing procedure, but it is a least suggestive of a benefit on disability progression.

The proportion of subjects with 12-week confirmed disability progression was 25 (13%) in the placebo group, 11 (5%) in the DAC HYP 150 mg group, and 15 (7%) in the DAC HYP 300 mg group. (In the adjusted estimate, the rates were 13.3%, 5.9% and 7.8%, respectively). Relative to placebo, the hazard ratio for disability progression was 0.43 (95% CI: 0.21 to 0.88) in the DAC HYP 150 mg group and 0.57 (95% CI: 0.30 to 1.09) in the DAC HYP 300 mg group.

Table 7. Time to sustained progression, Study 205MS201

As with the proportion relapsing, discussed above, the sponsor and the First Round clinical evaluator cited reductions in the proportions progressing that were directly based on hazard ratios, and this is potentially misleading. The sponsor suggested that the risk of disability progression was reduced by 57% in the DAC HYP 150 mg group (p = 0.0211) and by 43% in the DAC HYP 300 mg group (p = 0.0905), compared with placebo. These calculations were based on hazard ratios and do not accurately reflect the reduction achieved by the entire cohort over one year, but the inflation effect is relatively minor because so few subjects reached the hazard of interest.

As a proportion of the placebo progression rate, the proportion progressing in the 150 mg dose group was 5.9/13.3 (44.4%), consistent with a reduction of 55.6% (not 57%, as claimed). For the 300 mg dose group, the relative proportion progressing was 7.8/13.3 (58.6%), consistent with a reduction of 41.4% (not 43%). These results are similar to those cited by the sponsor, but the PI should be changed to reflect the actual reduction in the proportion, not the inflated estimate based on hazard ratios. Also, a p-value of 0.0211 is cited in the proposed PI without any indication that this result was not statistically significant; the PI should be amended to indicate a non-significant result.

An additional minor endpoint consisted of the risk of 24-week confirmed disability on EDSS. Progression by this definition was reduced in the DAC HYP 150 mg group (p = 0.0037) but not in the DAC HYP 300 mg group (p = 0.1487), compared with placebo. Hazard ratios for 24-week confirmed progression, relative to placebo, were 0.24 (95% CI: 0.09 to 0.63) for DAC HYP 150 mg and 0.60 (95% CI: 0.30 to 1.20) for DAC HYP 300 mg. The results in the 150 mg group cannot be considered significant because there has been no correction for multiplicity and, by the closed testing procedure used for major endpoints, results with 150 mg were only to be considered valid if the 300 mg dose group showed a significant effect.

Subgroup analyses

The sponsor performed a number of subgroup analyses of the primary endpoint (ARR), as shown in the Forest plot below (see Figure 6). A broadly consistent benefit for ARR was observed in most subgroups and despite the reduction in statistical power that comes from analysing subgroups, most comparisons with placebo remained significant. The exceptions were older subjects (age > 35 years) and subjects with previous disease-modifying treatment, where the 95% CIs for the rate ratios extended above unity indicating a non-significant result; however, even for these subgroups, the trends were in favour of active treatment. Reassuringly, a significant benefit was observed in subjects with and without relapses in the previous 12 months, with and without Gd enhancing lesions, and in subjects with both low and high EDSS (≤ 2.5 or > 2.5).

Figure 6. Annualised relapse rate by subgroup, Study 205MS201

Subgroup analysis for high disease activity versus low disease activity

A subgroup analysis based on high disease activity versus low disease activity was the subject of one of the supplementary data submissions. Even prior to receiving this suggestion for additional analyses from the EMA, the sponsor had already conducted and submitted their own post-hoc analysis for high disease activity versus low disease activity subgroups.

In the study report for Study 205MS201, this analysis was summarised as follows:

‘As a post-hoc analysis, the efficacy of DAC HYP was also evaluated in subjects with high disease activity at baseline, defined as ≥ 2 relapses in (the) year prior to randomisation and ≥ 1 Gdenhancing lesion at baseline as well in subjects with and without prior MS treatment experience (excluding steroids). For the analysis in subjects with and without high disease activity, subgroups were evaluated for the primary endpoint (ARR), key secondary endpoints (number of new or enlarging T2 lesions), and tertiary endpoints (number of Gd lesions at Week 52, disease progression) and the DAC HYP 150 and DAC HYP 300 mg groups were combined. The percentage reduction in annualized relapse rate among those with high-disease activity was 51% (95% CI: 5.5% to 74.1%) compared to 51% (95% CI: 31.7% to 65.5%) in the low-disease activity group (see Figure 6 above). Across the other endpoints, DAC HYP demonstrated similarly high efficacy in subjects with both high- and low-disease activity prior to study entry.’

This analysis suggested that, in terms of the proportional reduction in relapse rate, DAC HYP has similar relative efficacy in subjects with both high and low disease activity (reducing ARR by 51% in both subgroups). The absolute benefit, in terms of number of relapses prevented, is expected to be higher in subjects with high disease activity.

Secondary and tertiary endpoints were also assessed according to baseline disease activity, as shown in the tables below. For disease progression, a numerical benefit was observed in both high-activity and low-activity subgroups, but statistical significance was only demonstrated for the low-activity subgroup with the DAC HYP dose groups pooled (hazard ratio = 0.54, 95% CI: 0.30 to 0.97; p = 0.0383). The analysis in the high-activity subgroup was underpowered, with only 30 placebo recipients in the ITT population and 58 subjects in the combined active groups. Active treatment was associated with a superior hazard ratio, and only one high-activity patient progressed on active treatment, compared to four on placebo, so the failure to achieve statistical significance could reflect low patient numbers (hazard ratio = 0.12, 95% CI: 0.01 to 1.07; p = 0.0574).

For radiological endpoints, the results were strong in both high-disease-activity and low-disease-activity subgroups. For both new T2 lesions and Gd lesions, the benefit with active treatment was consistent across both subgroups, and remained statistically significant for dose-pooled DAC HYP data (‘DAC Total’) in both subgroups, as shown in Tables 8 to 10 below.

Table 8. Time to sustained progression by baseline disease activity and treatment, 205MS201

Table 9. Number of new T2 lesions by baseline disease activity and treatment, Study 205MS201

Table 10. Number of Gd-enhancing lesions by disease activity and treatment, Study 205MS201

7.1.1.13.Overall conclusions for Study 205MS201

Overall, this placebo-controlled study was adequately designed and it used entry criteria and endpoints typical of other studies seeking to register disease-modifying agents in MS. The reduction in ARR was 50 to 54% across the two active dose groups, relative to placebo, without any apparent dose trend. A broadly consistent benefit was observed in a number of subgroups based on gender, age, EDSS status and measures of disease activity including a post-hoc definition of disease activity. A favourable trend was observed on disease progression, with nominally significant p-value in one dose group (the proposed dose group, but not the primary dose group in the statistical analysis plan).

The main points of contention between the current evaluator and the sponsor are as follows:

The evaluator does not believe this study justifies the proposed indication because the entry criteria explicitly restricted the study to subjects with RRMS, whereas the indication refers to ‘relapsing forms of MS’.

The evaluator does not accept the sponsor’s calculation of the relative risk reductions for the proportions of subjects that relapsed and the proportions of subjects that progressed, because these were based on instantaneous hazard ratios rather than on the actual proportions that relapsed and progressed over the period of study.

The evaluator notes that, according to the prospective statistical analysis plan, this study did not show a significant effect on disease progression or MSIS-29 scores, whereas the proposed PI appears to indicate that the results for these endpoints were significant.