Teriflunomide versus interferon beta-1a (TENERE)

The authors say their own trial cannot support an effectiveness conclusion, and name the three things they did not do about it: more patients, longer treatment, and magnetic resonance imaging (MRI) endpoints. This is their plan, not a new idea, and what they left unspecified is the MRI measure, the comparator schedule, and the sample size.

Question

Does teriflunomide 14 mg differ from subcutaneous interferon beta-1a 44 micrograms on MRI lesion activity over 96 weeks, in a trial sized on an MRI endpoint?

Hypothesis

Teriflunomide 14 mg and subcutaneous interferon beta-1a 44 micrograms produce different annualised rates of combined unique active lesions over 96 weeks.

Attempt type

evaluation
Vocabulary note: None of the five values names a randomised controlled trial in human patients. 'evaluation' is the closest because the object is an intervention being judged against a comparator, but the graph JSON itself uses the free-text value 'randomized trial' for the same thing.

Design

Two arms, randomised one to one, double blind and double dummy: oral teriflunomide 14 mg daily plus sham subcutaneous injections three times weekly, against subcutaneous interferon beta-1a 44 micrograms three times weekly plus oral placebo. Patients are adults with relapsing multiple sclerosis and recent clinical or MRI activity, the OPTIMUM entry criterion. Treatment runs 96 weeks, as in OPERA. MRI at baseline and weeks 24, 48, 72 and 96, the TEMSO schedule, read at one central reading centre blinded to arm and to visit order. Primary endpoint: annualised count of combined unique active lesions by negative binomial regression with a log exposure offset. Secondary: percentage brain volume change by SIENA, annualised relapse rate, confirmed disability accumulation at 12 and 24 weeks, and the TENERE composite time to failure re-run unchanged so the two trials can be read against each other. Intention to treat, with on-treatment and complete-scan sensitivity analyses pre-specified.

Controls

• designated Subcutaneous interferon beta-1a 44 micrograms three times weekly, the same drug, dose and schedule as the TENERE comparator arm and the OPERA comparator arm.
  Rules out: That any difference, or absence of one, comes from having changed the comparator regimen rather than from the drugs themselves.
• known-positive-task Gadolinium-enhancing T1 lesion count as a co-reported MRI measure, pre-specified as the pipeline check. Both TEMSO (teriflunomide against placebo) and OPERA (ocrelizumab against subcutaneous interferon beta-1a) detected large differences on enhancing-lesion measures at these scan intervals.
  Rules out: That a null result on combined unique active lesions reflects an insensitive imaging pipeline, central reader, or scan schedule rather than two drugs with similar effects.
  Vocabulary note: In a clinical trial this is an assay-sensitivity control, not a task. The closest listed kind is known-positive-task because the point is a measure already shown to move.
• within-subject Each patient's own baseline scan is the reference for counting new and enlarging lesions, and each patient's own baseline volume is the reference for SIENA.
  Rules out: That an apparent arm difference is driven by between-patient differences in starting lesion burden or head size rather than by on-study activity.

Sensitivity

Partly derivable. OPTIMUM reports teriflunomide 14 mg at 3.164 combined unique active lesions per year in 566 patients over 108 weeks, and detected a 56 percent rate reduction against that rate at that sample size. The comparator cannot be matched in the same unit: OPERA reports subcutaneous interferon beta-1a 44 micrograms as 0.29 and 0.42 gadolinium-enhancing T1 lesions per scan, which is a different quantity, and OPTIMUM does not publish the negative binomial dispersion parameter. So the sample size is not derivable from published numbers. What is needed is the dispersion parameter for combined unique active lesions, plus one published combined-unique-active-lesion rate for subcutaneous interferon beta-1a 44 micrograms, or a pilot of 40 to 60 patients per arm scanned on the trial schedule. As an order of magnitude, a trial of OPTIMUM's size would be well powered for a 50 percent rate difference and clearly underpowered for 20 percent. For the brain-volume secondary, TEMSO reanalysed with SIENA gives median loss of 0.90 percent at year 2 on teriflunomide 14 mg against 1.29 percent on placebo in 709 patients, so a 0.3 to 0.4 percentage-point difference is measurable at roughly that size.

Would count as

Supported → positive · opposed → negative-no-effect
Inconclusive if: Differential dropout repeats what TENERE saw, where 33 of 104 interferon patients did not complete the core period against 20 of 109 and 22 of 111 on teriflunomide, so the interferon arm contributes too few week-72 and week-96 scans for the primary count; or the sham-injection burden pushes discontinuation in the teriflunomide arm above the rate the sample size assumed, so neither arm is observed as planned.

Already done

• A trial with subcutaneous interferon beta-1a 44 micrograms three times weekly as a double-blind, double-dummy comparator over 96 weeks has been run twice, at 821 and 835 patients, with MRI endpoints: 0.29 and 0.42 gadolinium-enhancing T1 lesions per scan in the interferon arms. (Hauser et al. 2017, New England Journal of Medicine (OPERA I and II), doi:10.1056/NEJMoa1601277)
  So: Supplies the comparator arm's design, duration and MRI activity level, so the interferon side of this design is copied from a trial that worked rather than invented.
• Teriflunomide 14 mg has been run as an active comparator for 108 weeks in 566 patients with MRI endpoints: 3.164 combined unique active lesions per year, annualised relapse rate 0.290, brain volume loss 1.25 percent at week 108. (Kappos et al. 2021, JAMA Neurology (OPTIMUM), doi:10.1001/jamaneurol.2021.0405)
  So: Gives the one published MRI rate for the teriflunomide arm, which is what the sample size has to be anchored on.
• Teriflunomide 14 mg has been blinded against a subcutaneous injectable using a double-dummy design, in two trials totalling 1882 patients with MRI secondary endpoints, with teriflunomide annualised relapse rates of 0.22 and 0.25. (Hauser et al. 2020, New England Journal of Medicine (ASCLEPIOS I and II), doi:10.1056/NEJMoa1917246)
  So: Shows the exact blinding machinery this design needs, oral drug plus sham injection, is executable at scale with teriflunomide, which TENERE did not attempt.
• Teriflunomide's MRI effect against placebo was measured in 1088 patients with scans at baseline, 24, 48, 72 and 108 weeks: total lesion volume increase 67.4 percent lower on 14 mg (p=0.0003), with accumulated enhancing lesions and combined unique activity also favouring teriflunomide. (Wolinsky et al. 2013, Multiple Sclerosis Journal (TEMSO MRI), doi:10.1177/1352458513475723)
  So: Fixes the scan schedule and establishes that the chosen measures respond to teriflunomide, so a null against interferon would not be explained by an unresponsive endpoint.
• A reanalysis of the TEMSO MRI set with SIENA gives median brain volume loss of 0.39 percent at year 1 and 0.90 percent at year 2 on teriflunomide 14 mg, against 0.61 percent and 1.29 percent on placebo, in 808 and 709 patients. (Radue et al. 2017, Neurology Neuroimmunology and Neuroinflammation, doi:10.1212/NXI.0000000000000390)
  So: Supplies the effect size for the brain-volume secondary endpoint and the sample size at which it is detectable.
• The longer-duration half of the authors' own next step was actually run, and cannot answer the comparator question: the TENERE extension moved every arm onto teriflunomide 14 mg, with 89, 89 and 59 patients entering, and extension annualised relapse rates of 0.236, 0.193 and 0.252 over a maximum of 197 weeks. The registry record also confirms the trial declared no MRI outcome of any kind, and single masking of the outcomes assessor only. (Sanofi, ClinicalTrials.gov posted results for NCT00883337 (accessed 2026-10-20), https://clinicaltrials.gov/study/NCT00883337)
  So: The new trial must keep randomised allocation through the long period rather than converting to a switch study, which is the mistake the existing extension made.

Searched: Searched Europe PMC for titles combining teriflunomide and interferon from 2014 onward (eight hits, none a randomised head-to-head), OpenAlex for later teriflunomide head-to-head and MRI-outcome trials, works citing TENERE filtered on MRI and on comparative effectiveness, and ClinicalTrials.gov for teriflunomide plus interferon studies. I looked specifically for a second randomised teriflunomide-versus-interferon trial and for any teriflunomide trial with an MRI primary endpoint against an active comparator, and found neither: every later trial puts teriflunomide 14 mg on the comparator side (OPTIMUM, ASCLEPIOS, ULTIMATE) and the only teriflunomide-plus-interferon phase 3, NCT01252355, was terminated.

Feasibility

A commercial sponsor, or a multi-country academic multiple sclerosis trial network with access to a central MRI reading centre of the kind that read TEMSO and OPERA. · 4 to 5 years from first patient to primary readout, with 96 weeks on treatment · high, because it needs roughly 500 patients per arm on two years of blinded treatment with five central-read MRI scans each, and a double-dummy injection supply
Blockers: Clinical equipoise has largely gone: subcutaneous interferon beta-1a is no longer a usual first-line choice, so recruiting to an interferon arm in 2026 is the main threat to the trial, not the statistics.; Two years of sham subcutaneous injections three times weekly in the oral arm is a large burden to ask an ethics committee and a patient to accept.; No sponsor has a commercial reason to fund a comparison of two older moderate-efficacy drugs.

Strongest objection

A multiple sclerosis trialist would say the question is obsolete and the trial unrecruitable: nobody would now randomise a patient to subcutaneous interferon beta-1a for two years, and the answer is already visible by cross-trial comparison, since teriflunomide's MRI activity in ASCLEPIOS and ULTIMATE sits close to interferon's in OPERA. The reply is that comparing across trials with different populations, eras and reading centres is exactly the kind of inference the TENERE authors said was not robust, but that reply does not solve the recruitment problem.

Not derivable from what is published

• The negative binomial dispersion parameter for combined unique active lesions in either drug, without which the sample size cannot be computed.
• A published combined-unique-active-lesion rate for subcutaneous interferon beta-1a 44 micrograms, in the same unit as OPTIMUM's teriflunomide figure.
• TENERE's own baseline MRI activity distribution, because the registry record confirms the trial collected no MRI outcome at all, so there is no in-trial anchor.
• Whether an interferon comparator arm can be recruited at all in the current treatment landscape, which is a feasibility fact no publication supplies.

The composite endpoint added together two things that moved in opposite directions: teriflunomide 7 mg had far more confirmed relapses (42.2 against 15.4 percent) and far fewer permanent discontinuations (6.4 against 24.0 percent) than interferon, so the composite cancelled out, and the trial cannot say whether either component effect is real.

Question

Do teriflunomide and interferon beta-1a differ on confirmed relapse and on permanent discontinuation when the two are analysed as prioritised competing events?

Hypothesis

A prioritised analysis ranking confirmed relapse above permanent discontinuation recovers a treatment difference in TENERE that the pooled composite cancelled out.

Attempt type

computational
Vocabulary note: This is a secondary analysis of individual patient data from a completed trial, together with a power simulation. 'computational' is the closest of the five; none of them names a re-analysis of trial data.

Design

Request the TENERE individual patient data from the sponsor through a data-sharing platform and re-analyse the 324 randomised patients three ways. First, cause-specific Cox models and Fine and Gray subdistribution hazard models treating confirmed relapse and permanent discontinuation as competing events, so each component gets a hazard ratio and a cumulative incidence rather than being absorbed into one indicator. Second, Pocock's win ratio with confirmed relapse ranked above permanent discontinuation, pre-registering the ranking before unblinding the analysis. Third, a power simulation on the observed component rates, reporting what component difference the 324 patients could have detected. Separate protocol-forced alanine aminotransferase discontinuations from patient-choice discontinuations and repeat the competing-risk analysis with the forced ones censored rather than counted as events. Pre-specify re-running the original composite log-rank in the same code base.

Controls

• internal-positive The teriflunomide 7 mg against interferon contrasts, which the record's own counts make detectable at this sample size: 42.2 against 15.4 percent on confirmed relapse has 99 percent power, and 6.4 against 24.0 percent on permanent discontinuation has 95 percent power, both at alpha 0.05 with 104 and 109 patients.
  Rules out: That a null on the 14 mg component contrasts reflects a broken analysis pipeline or a data-extraction error, rather than a genuine lack of power for a smaller difference.
• designated The original composite log-rank re-run on the received dataset and checked against the published hazard ratios of 1.12 (95 percent confidence interval 0.75 to 1.67) for 7 mg and 0.86 (0.56 to 1.31) for 14 mg.
  Rules out: That any new finding comes from a different dataset, a different population definition or a coding error, rather than from the change of analysis method.
• adversarial-label Permutation of treatment labels within the received dataset, 10000 draws, to build the null distribution of the win ratio and of the subdistribution hazard ratios under the realised sample size and censoring pattern.
  Rules out: That the prioritised statistic manufactures an apparent difference out of the ranking rule itself, which is the standard criticism of win-ratio analyses.

Sensitivity

Derivable from the record's own counts, and this is the main product of the design. At TENERE's realised sample sizes, a two-proportion test at alpha 0.05 two-sided had 31 percent power for the observed 14 mg relapse contrast (15.4 against 23.4 percent, n 104 and 111) and 51 percent power for the observed 14 mg discontinuation contrast (24.0 against 13.5 percent). At 80 percent power and roughly 105 patients per arm, the smallest relapse difference detectable against a 15.4 percent interferon rate is about 32 percent, that is a doubling; detecting 28 percent would need 167 per arm. So the trial could only ever have resolved the 7 mg-sized component effects, which it did, and never the 14 mg-sized ones. These figures are computed from the counts in the record, not taken from a publication.

Would count as

Supported → positive · opposed → inconclusive-underpowered
Inconclusive if: The data request returns only summary tables rather than patient-level records, so competing-risk and win-ratio analyses cannot be fitted; or the dataset has no reason-for-discontinuation coding, so protocol-forced alanine aminotransferase discontinuations cannot be separated from patient-choice ones and the discontinuation component stays uninterpretable.

Already done

• A prioritised win-ratio statistic exists precisely for composites whose components differ in clinical importance, and recovers information that pooling destroys. (Pocock et al. 2012, European Heart Journal, doi:10.1093/eurheartj/ehr352)
  So: Supplies the method and means the design does not have to invent a statistic; the ranking rule is the only thing left to justify.
• Practical guidance on win-ratio analyses, including pre-specification of the hierarchy and of the tie-handling rule, has been published from accumulated trial experience. (Redfors et al. 2020, European Heart Journal, doi:10.1093/eurheartj/ehaa665)
  So: Sets the pre-registration requirements this re-analysis must meet to avoid being dismissed as a fishing expedition.
• The TENERE extension cannot extend the component comparison: 89, 89 and 59 patients entered it and all of them took teriflunomide 14 mg, and extension adverse-event discontinuations were 8, 6 and 5. (Sanofi, ClinicalTrials.gov posted results for NCT00883337 (accessed 2026-10-20), https://clinicaltrials.gov/study/NCT00883337)
  So: Rules out simply adding follow-up to gain power on the components, so the gain has to come from the analysis method or from pooling with other trials.
• Real-world teriflunomide discontinuation is measurable at far better precision than 324 patients allow: 3239 nationwide starters in Denmark between 2013 and 2019, with 72.7 percent of the 3001 who started at least 12 months before cut-off still on treatment at 12 months. (Papp et al. 2021, PLoS One, doi:10.1371/journal.pone.0250820)
  So: Shows the discontinuation component already has a precise answer outside randomisation, so this design should report its competing-risk estimate against that benchmark rather than in isolation.
• Teriflunomide treatment satisfaction, the plausible driver of the low discontinuation rate, is replicated at 1000 patients with a mean Treatment Satisfaction Questionnaire for Medication Global Satisfaction score of 68.2 at week 48, and switchers improving on all four domains. (Coyle et al. 2017, Multiple Sclerosis and Related Disorders (Teri-PRO), doi:10.1016/j.msard.2017.07.006)
  So: The satisfaction side of the discontinuation story is independently supported, which makes the discontinuation component the more credible of the two to pursue.
• A pooled teriflunomide safety dataset exists at scale: 3044 patients across one phase 2 and three phase 3 core studies with more than 1500 patient-years per group, and 2338 patients with up to 12 years of treatment and more than 6800 patient-years including extensions. (Comi et al. 2016, Multiple Sclerosis and Related Disorders, doi:10.1016/j.msard.2015.11.006)
  So: A large discontinuation denominator for teriflunomide exists but only against placebo, so pooling can sharpen the teriflunomide rate and still cannot supply a randomised interferon comparator.

Searched: Searched Europe PMC for composite and treatment-failure endpoint methodology in multiple sclerosis (three hits, both recent ones about disability composites rather than relapse-plus-discontinuation), for win-ratio and hierarchical-composite methods, for teriflunomide pooled and subgroup analyses, and for teriflunomide registry and propensity-matched studies; and searched works citing TENERE for anything re-analysing its components. I looked specifically for a published re-analysis of the TENERE composite or of its components and found none.

Feasibility

A biostatistics or clinical-epidemiology group with an approved data-sharing request to the sponsor, plus a multiple sclerosis clinician to fix the component hierarchy. · 6 to 12 months once data access is granted · low, because it is analyst time on existing data with no new patients, scans or drug
Blockers: Sponsor approval for individual patient data access; I could not verify from the record or the literature whether this 2009 to 2011 trial is listed on any data-sharing platform.; The dataset may not carry per-patient reason-for-discontinuation coding at the granularity the design needs.; The record notes the paper's own Table 2 discontinuation counts do not match its Figure 1 disposition data, so reconciling the dataset against the publication may fail.

Strongest objection

A trialist would say that a better statistic cannot create information that 324 patients do not contain, and that ranking relapse above discontinuation builds in exactly the value judgement the composite was designed to avoid, so the win ratio would mostly recover the relapse result that the annualised relapse rate secondary endpoint already shows (relative risk 1.90, p=0.03 for 7 mg). The honest answer is that the design's real output is the sensitivity statement, not a new effect estimate, which is a less exciting product than the question implies.

Not derivable from what is published

• Whether TENERE individual patient data are obtainable, and under what terms.
• The within-patient variance and censoring detail needed for a credible win-ratio power simulation, as opposed to the two-proportion calculations above.
• Per-patient reason-for-discontinuation coding, including which discontinuations were forced by the alanine aminotransferase rule: the record gives alanine aminotransferase discontinuations as 9, 2 and 4 in the safety population but does not map them onto the intention-to-treat failure counts.
• How the one 14 mg patient who received 7 mg for three months, and the three never-treated interferon patients counted as failures, should be handled in a competing-risk model.

Patients and treating physicians knew which drug they were on, so the endpoints that depend on the patient's own report, treatment satisfaction and fatigue, and the discontinuation half of the composite, could all be driven by knowing you are on a tablet instead of an injection. The authors flag this and do not quantify it. The registry record confirms single masking of the outcomes assessor only.

Question

How much of TENERE's patient-reported advantage for teriflunomide survives when allocation is concealed from the patient by a double-dummy design rather than left open-label?

Hypothesis

Concealing allocation with a double-dummy design removes more than half of the open-label teriflunomide advantage on the treatment satisfaction questionnaire.

Attempt type

evaluation
Vocabulary note: This is a randomised methodological study nested inside a clinical trial, a study-within-a-trial. 'evaluation' is the closest of the five values, but what is being evaluated is a trial design feature, not a treatment.

Design

A randomised study-within-a-trial hosted by any phase 3 trial comparing a daily oral drug against a subcutaneous injectable. Participants are randomised a second time, one to one, to open-label allocation (both arms know their drug, as in TENERE) or to double-dummy allocation (oral arm receives sham injections, injectable arm receives oral placebo). Both strata receive identical assessments: Treatment Satisfaction Questionnaire for Medication and total Fatigue Impact Scale at baseline and weeks 12, 24 and 48, the TENERE timepoint, plus Bang's blinding index at each visit as the manipulation check. The estimand is the interaction: the difference between strata in the treatment-group difference, fitted by mixed model with repeated measures as TENERE used, with the blinding stratum, treatment and their interaction as fixed terms. Secondary estimands are the same interaction on permanent discontinuation and on the TENERE composite.

Controls

• designated The open-label stratum, which reproduces TENERE's conditions exactly, including knowing the drug from day one.
  Rules out: That a small difference in the blinded stratum means concealment does not matter, when it could instead mean the host trial's population simply reports smaller differences than TENERE's did.
• internal-positive Incidence of the two drug-specific adverse events that distinguished the arms in TENERE, influenza-like illness (53.5 percent with interferon against 3.6 and 2.7 percent with teriflunomide) and hair thinning (1.0 percent against 5.5 and 20.0 percent), reported by stratum.
  Rules out: That the double-dummy stratum failed to deliver two genuinely different regimens, for example through a dispensing error substituting sham for active drug.
• adversarial-label Bang's blinding index in the double-dummy stratum at weeks 12, 24 and 48, with a pre-specified threshold above which the stratum is declared functionally unblinded and the primary interaction is reported as void.
  Rules out: That a null interaction is read as evidence that concealment does not matter, when in fact concealment was never achieved.
  Vocabulary note: The listed kind fits: participants are asked to guess the label, and better-than-chance guessing invalidates the manipulation.

Sensitivity

Derivable from the record's standard errors, and the answer is uncomfortable. TENERE's Global Satisfaction difference against interferon was 7.32 points with standard error 3.22, in 104 plus 111 patients. An interaction between two strata has about the square root of two times that standard error, roughly 4.55 at the same per-stratum size, so detecting complete attenuation of a 7.32-point difference at 80 percent power and alpha 0.05 needs a standard error near 2.61, which is an inflation factor of about 3.0: roughly 650 participants per blinding stratum, about 1300 in total. Detecting half attenuation, 3.66 points, needs about 2600 per stratum, more than 5200 in total, which is larger than ASCLEPIOS. The Fatigue Impact Scale difference of 8.13 points with standard error 3.67 needs about 690 per stratum for complete attenuation. So the design is affordable only for the strong hypothesis that concealment wipes the effect out, and is not affordable for the plausible hypothesis that it halves it.

Would count as

Supported → positive · opposed → negative-no-effect
Inconclusive if: Bang's blinding index shows the double-dummy stratum guessed allocation at better than chance, which is likely given that influenza-like illness affected 53.5 percent of interferon patients in TENERE, so the two strata differ in paperwork rather than in what participants actually know; or no host trial with an injectable comparator is running, so the study-within-a-trial has nowhere to sit.

Already done

• In multiple sclerosis specifically, unblinded and blinded neurologists assessing the same patients reached different conclusions: in the Canadian cooperative trial the unblinded but not the blinded assessors found an apparent treatment benefit at 6, 12 and 24 months, and blinding prevented a false positive. (Noseworthy et al. 1994, Neurology, doi:10.1212/WNL.44.1.16)
  So: Establishes both that the bias is real in this disease and that the paired blinded-and-unblinded design is the classic way to measure it, which is what this study-within-a-trial generalises to patient-reported endpoints.
• A validated index exists for quantifying how well participants are blinded, separating random guessing from correct identification. (Bang, Ni and Davis 2004, Controlled Clinical Trials, doi:10.1016/j.cct.2003.10.016)
  So: Supplies the manipulation check without which the design cannot distinguish a null interaction from a failed blind.
• Blinding success is almost never reported: a random sample of placebo-controlled trials showed only a small minority tested or reported it. (Fergusson et al. 2004, BMJ, doi:10.1136/bmj.37952.631667.ee)
  So: Justifies measuring blinding rather than assuming it, and means this design cannot borrow a published blinding-success rate for a comparable trial.
• The double-dummy machinery needed here, oral teriflunomide 14 mg plus sham subcutaneous injection against active subcutaneous drug plus oral placebo, has been built and run in 1882 patients for up to 30 months. (Hauser et al. 2020, New England Journal of Medicine (ASCLEPIOS I and II), doi:10.1056/NEJMoa1917246)
  So: The blinded stratum is not hypothetical: an industry sponsor has already concealed exactly this oral-against-injectable contrast at scale.
• A three-times-weekly subcutaneous interferon beta-1a 44 microgram regimen has been successfully blinded for 96 weeks in 1656 patients. (Hauser et al. 2017, New England Journal of Medicine (OPERA I and II), doi:10.1056/NEJMoa1601277)
  So: Shows the specific comparator schedule TENERE left open-label can be concealed, which is the direct demonstration that TENERE's design choice was avoidable.
• Blinding has been formally assessed in a multiple sclerosis population before, in trials of a cannabis-based medicine. (Wright et al. 2012, Trials, doi:10.1186/1745-6215-13-189)
  So: Gives a precedent for the blinding-assessment procedure in this patient group, including the wording of the guess question.
• The instrument carrying TENERE's largest reported effects has itself been questioned in multiple sclerosis. (Vermersch et al. 2017, Multiple Sclerosis Journal, 'Measuring treatment satisfaction in MS: Is the Treatment Satisfaction Questionnaire for Medication fit for purpose?' (same first author as TENERE), doi:10.1177/1352458516657441)
  So: The design must report domain-level reliability in both strata, because an apparent attenuation could be instrument noise rather than removed bias.

Searched: Searched Europe PMC for blinding plus multiple sclerosis in the title (four hits, the Noseworthy study and its reprint, a Sativex blinding assessment, and a biased-blinding-assessment letter), for blinding-index and success-of-blinding methodology, and for Bang's own blinding papers; checked the ClinicalTrials.gov masking field for NCT00883337, which confirms single masking of the outcomes assessor only; and searched works citing TENERE on treatment satisfaction and adherence. I looked for a randomised comparison of open-label against double-dummy allocation within the same trial, in any disease, and found none.

Feasibility

An academic clinical trials unit able to attach a study-within-a-trial to an ongoing phase 3, funded by a trial-methodology programme rather than by a drug sponsor. · 2 to 3 years, set by the host trial's recruitment · moderate to high, because the extra cost is sham injection supply, dispensing and 48 weeks of extra questionnaires, but the sample size needed is above a thousand
Blockers: No current phase 3 trial is known to randomise against subcutaneous interferon beta-1a, so the host trial would have to use a different injectable and the result would only generalise to TENERE by assumption.; Randomising participants to be deliberately unblinded, when blinding is available, is a hard sell to an ethics committee.; 48 weeks of sham subcutaneous injections three times weekly in the oral arm.

Strongest objection

A trialist would say double-dummy does not blind multiple sclerosis patients to interferon beta: with influenza-like illness in 53.5 percent of interferon patients and hair thinning in 20.0 percent of teriflunomide 14 mg patients, the blind breaks pharmacologically within weeks, so the study would measure the cost of sham injections rather than the value of concealment, and the sample size computed above is spent on a manipulation that does not hold. That objection is strong enough that the honest alternative may be to abandon the randomised version and instead report Bang's blinding index inside existing double-dummy trials.

Not derivable from what is published

• Domain-level standard errors for Treatment Satisfaction Questionnaire for Medication Convenience and Side-Effects in TENERE: the record gives the differences (26.40 and 27.96, 23.92 and 21.77) but standard errors only for Global Satisfaction, so the sensitivity above is derived for Global Satisfaction and the Fatigue Impact Scale only.
• The intraclass correlation across the repeated measures, which a mixed model sample size would need and which would reduce the figures above.
• Whether any trial is currently recruiting with an injectable comparator that could host the study-within-a-trial.
• What fraction of TENERE's 24.0 percent interferon discontinuations were attributable to knowing the allocation rather than to the adverse events themselves, which is the quantity the whole issue is about and which no published source supplies.

The trial's own stopping rule manufactured part of the interferon arm's failure count: alanine aminotransferase (ALT) discontinuations were 9 of 101 treated interferon patients against 2 of 110 and 4 of 110 on teriflunomide, and ALT increase as any adverse event ran at 30.7 against 10.9 and 10.0 percent. The authors note that no dose modification was allowed and that nobody knows whether a graded response would work instead. This is their observation, not a plan; the design below is the untried experiment it implies.

Question

After a confirmed liver enzyme rise above three times the upper limit of normal, does hold-and-rechallenge give fewer 48-week relapses than permanent discontinuation?

Hypothesis

Hold-then-rechallenge halves the 48-week confirmed relapse risk after a liver enzyme trigger, from about 15 percent to 7.5 percent, with no increase in Hy's-law events.

Attempt type

evaluation
Vocabulary note: This is a randomised management-strategy trial triggered by a laboratory event and embedded in a disease registry. 'evaluation' is the closest; none of the five values names a strategy trial, and 'wet-lab' would be plainly wrong for a clinical blood test.

Design

A registry-embedded, event-triggered randomised strategy trial. Patients starting teriflunomide or an interferon beta are enrolled in national multiple sclerosis registries with liver monitoring at the interval the licence in force requires. At a confirmed ALT above three times the upper limit of normal, the patient is randomised one to one to immediate permanent discontinuation, the TENERE rule, or to drug hold with weekly liver panels until ALT falls below twice the upper limit, then rechallenge at the licensed dose with weekly then monthly monitoring. Hard stops in the hold arm: ALT above eight times the upper limit, ALT above five times persisting two weeks, or ALT above three times with bilirubin above twice the upper limit. Primary endpoint: confirmed relapse within 48 weeks of the index ALT event. Co-primary safety endpoint: any Hy's-law case or liver-related serious adverse event. Secondary: retention on the assigned drug, peak ALT, time to ALT normalisation, and causality scored by the Roussel Uclaf method.

Controls

• designated The immediate permanent discontinuation arm, which is the TENERE protocol rule and current labelled practice, with free choice of any subsequent therapy.
  Rules out: That an apparent benefit of rechallenge is really the benefit of any structured follow-up, since both arms get the same monitoring schedule and the same relapse ascertainment.
• background The concurrent registry cohort on the same two drugs who never reach the ALT trigger, supplying the background 48-week confirmed relapse rate and liver-event rate in the same calendar period and the same clinics.
  Rules out: That both arms' relapse rates reflect a secular change in relapse ascertainment or in background therapy rather than anything the strategies did.
• within-subject Each randomised patient's own pre-event ALT trajectory and relapse history, used with Roussel Uclaf causality scoring to attribute the ALT rise to the study drug rather than to alcohol, viral hepatitis or a concomitant drug.
  Rules out: That the trigger population is diluted by patients whose ALT rise had nothing to do with the disease-modifying therapy, in whom neither strategy can help or harm.

Sensitivity

Partly derivable, and the gap is the important part. If the 48-week confirmed relapse risk after an ALT trigger is near TENERE's interferon-arm confirmed relapse rate of 15.4 percent, then detecting a halving to 7.5 percent at 80 percent power and alpha 0.05 two-sided needs about 278 randomised patients per arm; detecting a fall to 10 percent needs about 686 per arm, and to 5 percent about 141 per arm. The event flow is also estimable: at TENERE's ALT-related discontinuation rates of 1.8 to 8.9 percent of treated patients, a nationwide registry of the Danish size, 3239 teriflunomide starters over six years, would yield roughly 60 to 120 triggers, so several national registries are required. What cannot be derived from the record or the literature is the 48-week relapse risk after an unplanned discontinuation, and the proportion of confirmed ALT triggers that resolve on hold. Both need a registry-based pilot before the sample size is anything more than an illustration.

Would count as

Supported → positive · opposed → negative-no-effect
Inconclusive if: Clinicians have already moved to hold-and-rechallenge informally, so the immediate-discontinuation arm cannot be recruited and equipoise fails; or Roussel Uclaf scoring shows most triggers are not drug-attributable, so the randomised population is largely patients in whom neither strategy can act.

Already done

• The direct randomised liver comparison between teriflunomide and interferon beta is this trial alone and is uninformative: a network meta-analysis found only one direct comparison, which reported no liver toxicity cases in either group so no odds ratio could be estimated, and the indirect estimate was an odds ratio of 1.09 with a 95 percent credible interval of 0.02 to 2.16. (Salas et al. 2018, Multiple Sclerosis and Related Disorders, doi:10.1016/j.msard.2018.09.014)
  So: Confirms that nothing in the existing evidence base can settle the management question, so it has to be answered prospectively, and that the question is about management rather than about which drug is more hepatotoxic.
• Teriflunomide's pooled safety programme covers 3044 patients in core studies with more than 1500 patient-years per group and 2338 patients with up to 12 years of exposure and more than 6800 patient-years, with ALT increase among the commonest events at 10 percent or more and at least 2 percent above placebo. (Comi et al. 2016, Multiple Sclerosis and Related Disorders, doi:10.1016/j.msard.2015.11.006)
  So: Gives the denominator for how often the trigger fires across the whole programme, and shows that a large, long safety dataset exists in which no management strategy was ever tested.
• Deliberate rechallenge after drug-induced liver injury has a published framework, including which injuries may be rechallenged and which must not. (Hunt et al. 2017, Hepatology, doi:10.1002/hep.29152)
  So: Supplies the rechallenge protocol and most of the hard stopping rules, so the hold arm is not improvised.
• Current practice guidance for drug, herbal and dietary-supplement induced liver injury defines the severity thresholds and the Hy's-law pattern. (Fontana et al. 2023, Hepatology (AASLD practice guidance, published online 2022), doi:10.1002/hep.32689)
  So: Sets the co-primary safety endpoint definition, which is what makes a null on the safety side interpretable rather than reassuring by default.
• A single national registry can supply both the event flow and the background cohort: 3239 nationwide teriflunomide starters in Denmark between 2013 and 2019, with 72.7 percent of those with 12 months of follow-up still on treatment. (Papp et al. 2021, PLoS One, doi:10.1371/journal.pone.0250820)
  So: Shows the registry-embedded design is practical and sizes how many registries are needed, and shows that ALT-driven stopping is a small part of all discontinuation.
• The literature on disease-modifying therapy and liver injury in relapsing multiple sclerosis is narrative review, not trial evidence. (Biolato et al. 2021, CNS Drugs, 'The Disease-Modifying Therapies of Relapsing-Remitting Multiple Sclerosis and Liver Injury: A Narrative Review', doi:10.1007/s40263-021-00842-9)
  So: Confirms there is no comparative evidence to build on, so the design has to carry its own control rather than rely on a historical rate.

Searched: Searched Europe PMC for teriflunomide with liver, hepatic or alanine in the title (one hit, the indirect comparison above), for rechallenge in drug-induced liver injury, and for works citing TENERE on liver enzyme monitoring; searched ClinicalTrials.gov for a randomised liver-enzyme management or dose-reduction strategy trial and found none, in multiple sclerosis or in any disease. I looked specifically for a trial or cohort reporting outcomes of rechallenge after a disease-modifying therapy ALT trigger and found nothing, which is the finding.

Feasibility

A consortium of national multiple sclerosis registries, Denmark, Sweden and Germany for instance, with a hepatology partner and a trials unit able to run event-triggered randomisation inside routine care. · 4 to 6 years, almost all of it accruing trigger events rather than following patients · moderate, because it adds no new drug and no imaging and rides on registry infrastructure, but it runs long and across several countries
Blockers: Event rate: at 1.8 to 8.9 percent of treated patients, several national registries are needed to randomise a few hundred triggers.; Rechallenge may not be permitted where the licence requires permanent discontinuation at a confirmed ALT above three times the upper limit, which is a regulatory question the design cannot answer for itself.; Asking a patient to accept liver risk to stay on a moderate-efficacy drug, when switching to a different therapy is available, may fail recruitment on its own.

Strongest objection

A hepatologist would say this tests a known hazard for a benefit that can be had another way: the point of stopping at a confirmed ALT above three times the upper limit is to avoid the rare catastrophic case, and the patient can keep disease control by switching to a therapy that does not raise transaminases, so the trial asks for liver risk in exchange for continuity on one particular drug. The counter-argument is that the alternative therapy carries its own risks and that the stopping rule was never validated, but the hepatologist's objection is the one that would stop an ethics committee.

Not derivable from what is published

• The 48-week confirmed relapse risk after an unplanned disease-modifying therapy discontinuation, which is the number the primary endpoint is powered on; the 15.4 percent used above is TENERE's on-treatment interferon-arm rate over a median 60 to 66 weeks, which is a substitute, not the right number.
• The proportion of confirmed ALT triggers above three times the upper limit that resolve on drug hold, and the proportion that recur on rechallenge.
• The liver monitoring interval in force, which the record does not state and which sets how many triggers are detected at all.
• Whether rechallenge after a confirmed ALT above three times the upper limit is permitted under current labelling in the participating countries.
• How many of TENERE's 9, 2 and 4 ALT discontinuations were in patients whose ALT would have fallen on a hold, since the record reports only the counts.