Efficacy, Safety and Pharmacokinetics of Teriflunomide in Pediatric Patients With Relapsing Forms of Multiple Sclerosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Safety and Pharmacokinetics of Teriflunomide in Pediatric Patients With Relapsing Forms of Multiple Sclerosis (NCT02201108), a randomized phase 3 study. The primary outcome is Time to First Confirmed Clinical Relapse.

2. Clinical Question

The clinical question is about the timing of a confirmed relapse, rather than simply whether a participant ever experienced one. A participant without a confirmed relapse was considered relapse-free through the end of Week 96. Relapses had to meet the registry’s clinical definition and be confirmed by an independent Relapse Adjudication Panel.

The study also set out to assess MRI measures, cognitive function, safety, tolerability and pharmacokinetics. Those objectives broaden the trial’s scope, but the primary statistical comparison remains the time-to-event comparison during the double-blind period. Results for the additional measures should be interpreted in light of their secondary status and the information available for each outcome.

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group trial comparing teriflunomide with placebo. The registry lists 166 participants as enrolled. The primary outcome analysis included 57 participants in the placebo group and 109 in the teriflunomide group, analysed according to randomized allocation.

The official title describes a two-year, multicenter, double-blind, placebo-controlled period followed by an open-label extension. The registry lists the study as starting on 2014-07-16, reaching primary completion on 2019-10-25, and having completed status. The double-blind comparison is the relevant randomized comparison for the primary endpoint; treatment groups in the extension reflect different treatment sequences and are not the same comparison.

Teriflunomide was administered orally once daily. The registry describes three dosage levels—3.5, 7 or 14 mg—to reach a 14 mg adult equivalent. The placebo arm received matching tablets. The posted primary analysis used the intent-to-treat population, defined as all randomized participants analysed according to the treatment allocated by randomization.

The registry lists 22 outcome measures and 21 posted secondary outcomes. These cover relapse status over time, MRI lesion measures and brain-volume measures, alongside the primary relapse endpoint and the trial’s other objectives. A full account of the original sample-size justification, planned interim analyses, and the statistical plan beyond what is specified for the reported primary test is not reported in the registry record. The planning illustrations on this page are not evidence of the trial’s original design assumptions.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Participants were randomly assigned to receive either teriflunomide or placebo in a 2:1 ratio via Interactive Voice Response System. Randomization was stratified by the country and participant's pubertal status.

Double-blind Period (up to Week 96)

Reasons for not completing this period:

Open Label Period (up to Week 192)

Reasons for not completing this period:

Extension Period (Up to Week 492)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on Intent-to-treat (ITT) population, which consisted of all randomized participants analyzed according to the treatment allocated by randomization.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Analysis was performed on all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Time to First Confirmed Clinical Relapse, measured over Baseline up to Week 96.

The primary endpoint was time to first confirmed clinical relapse, measured from randomization through Week 96 and recorded in weeks. It represents the time until a participant’s first event meeting the trial’s relapse definition. A participant with no confirmed relapse was considered relapse-free through the end of Week 96.

The registry defines a relapse as new or recurrent neurological symptoms not associated with fever or infection, lasting at least 24 hours, and accompanied by new objective findings on neurological examination. The findings had to be documented using the standardized, quantified functional system score. The registry states that confirmed relapses were reviewed by an independent Relapse Adjudication Panel.

Time-to-event endpoints retain information about when an event occurs, rather than reducing the outcome to a simple event/no-event count. That is useful when participants can experience a first relapse at different points during follow-up, or remain without a confirmed relapse through the endpoint window. The analysis asks whether the timing pattern differs between randomized groups.

The reported group summaries are medians with full ranges. A median describes the midpoint of the observed time distribution; it does not describe every participant’s experience. The comparison between groups is instead summarized by the reported hazard ratio and its confidence interval, with the stratified log-rank test also reported. The registry record does not report additional detail on how incomplete follow-up was handled beyond its statement that participants without a confirmed relapse were considered relapse-free until the end of Week 96.

7. Results Posted in the Registry

• Double-Blind Treatment Period: Placebo vs Double-Blind Treatment Period: Teriflunomide: hazard ratio 0.66 (95% CI 0.39–1.11), reported p = 0.295 (as reported in the registry).

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

OL: Time to First Confirmed Clinical Relapse

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Placebo/Teriflunomide vs Teriflunomide/ Teriflunomide: hazard ratio 0.69 (95% CI 0.37–1.30) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo/Teriflunomide vs Teriflunomide/ Teriflunomide and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span several related domains: relapse-free status over scheduled follow-up points, MRI measures of lesions and brain volume, and cognitive function, safety, tolerability, and pharmacokinetics as study objectives. This range reflects an interest in disease activity and other aspects of the trial beyond the primary time-to-first-relapse endpoint.

The registry lists 21 posted secondary outcomes among 22 outcome measures. Their results should be read as additional evidence that complements, rather than replaces, the primary comparison. In particular, MRI outcomes measure imaging changes and are not interchangeable with a confirmed clinical relapse. Likewise, a relapse-free proportion at a particular time point is not the same estimand as time to first relapse across follow-up.

The posted material does not support a single overall pattern across all secondary results from the information. The outcome list alone cannot establish whether results consistently favored either group, and the individual secondary results should be read in their tables rather than inferred from the list of measures. The open-label extension has a different treatment-sequence comparison and should not be combined with the blinded primary result as if it were the same randomized contrast.

Multiple outcomes create multiple opportunities for apparently notable findings. Unless the analysis plan controls for those opportunities, isolated secondary results can be less persuasive than a prespecified primary result because chance findings become more likely across a broad set of tests. Whether multiplicity was controlled, and by what method, is not reported in the registry record. Secondary findings therefore require attention to their estimates, uncertainty, analysis methods, and their status within the overall testing plan.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Probability of Participants Who Were Clinical Relapse Free at Weeks 24, 48, 72, 96, 120, 144, 168 and 192
• Brain Magnetic Resonance Imaging (MRI) Assessment: Number of New or Enlarged T2 Lesions Per MRI Scan
• Brain Magnetic Resonance Imaging Assessment: Number of T1 Gadolinium (Gd)-Enhancing T1 Lesions Per MRI Scan
• Brain Magnetic Resonance Imaging Assessment: Change From Baseline in Volume of T2 Lesions at Weeks 24, 36, 48, 72, 96, 144 and 192
• Brain Magnetic Resonance Imaging Assessment: Change From Baseline in Volume of T1 Hypointense Lesions
• Brain Magnetic Resonance Imaging Assessment: Number of New T1 Hypointense Lesions Per MRI Scan
• Brain Magnetic Resonance Imaging Assessment: Percentage of Participants Free of New or Enlarged MRI T2-Lesions
• Brain Magnetic Resonance Imaging Assessment: Percent Change From Baseline in Brain Volume at Weeks 24, 36, 48, 72, 96, 144 and 192

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. Each participant’s event time is the interval from randomization to the first confirmed clinical relapse. For participants without a confirmed relapse, the registry says they were considered relapse-free until the end of Week 96. This approach allows the analysis to use the timing of events, rather than treating all follow-up as if it ended at one common event time.

What does the hazard ratio summarize?

A hazard ratio summarizes the relative event rate between groups over the period being analysed. Here, the registry reports the comparison as placebo versus teriflunomide, with a hazard ratio of 0.657. A value at the no-difference reference would indicate equal relative event rates under the hazard-ratio interpretation; a value below that reference points toward a lower event rate in the first-listed group relative to the second-listed group, and a value above it points in the other direction. The estimate is a summary of event timing, not a direct statement about the probability that any individual participant will relapse.

The hazard ratio should not be read in isolation. Its meaning depends on the comparison order, and its precision depends on the confidence interval. It also compresses a time-varying pattern into one summary. The registry does not report the model details or diagnostics needed to assess assumptions about how the relative event rate behaves over time, so those details cannot be evaluated from the record.

What does the stratified log-rank test do?

The registry names a stratified log-rank test as the method for the primary comparison. In general, a log-rank test compares event-time patterns between groups while taking account of when events occur and how long participants contribute follow-up. A stratified version performs the comparison within strata and combines information across them. The registry does not identify the stratification factors in the information. It is therefore not possible to describe what those strata were or how they were selected.

The test’s reported p value is 0.295. A p value describes how compatible the observed data are with a specified no-difference statistical model, given the test and its assumptions. It is not the probability that the treatment effect is zero, and it does not measure the size or importance of an effect. Here it should be read alongside the reported confidence interval, not as a stand-alone verdict.

How should the median and range be read?

The registry reports median times of 39.14 weeks for placebo and 75.29 weeks for teriflunomide, with full ranges from 0.1 to 98.0 weeks and from 0.1 to 98.7 weeks, respectively. The median locates the midpoint of the reported time distribution. The range gives the reported endpoints of that distribution; it does not show how observations are spread between those endpoints. Neither summary replaces the time-to-event comparison, and the ranges do not communicate the uncertainty around the medians.

The endpoint description also specifies how a relapse was defined and independently confirmed. A clear event definition supports consistent classification, but the registry summary does not give further detail on adjudication procedures, missing observations, or any sensitivity analyses. Those elements should not be assumed from the use of an independent panel.

Which participants were analysed?

The primary analysis used the intent-to-treat population: all randomized participants analysed according to the treatment allocated by randomization. This preserves the randomized group assignment in the primary comparison, even if a participant’s later treatment differs from the assigned group. The registry lists 57 participants in the placebo analysis group and 109 in the teriflunomide analysis group. It does not give further detail on analysis-set exclusions, adherence, or the handling of data that were unavailable for particular participants.

The registry also reports secondary outcomes and an open-label extension comparison. These involve other measures or treatment sequences and should not be substituted for the primary blinded comparison. Methods for the secondary outcomes beyond their listed measures and timeframes are not reported in the registry record. In particular, the record does not establish whether or how multiplicity was controlled across the many outcomes.

11. Confidence Intervals and Precision

The 95% confidence interval for the primary hazard ratio runs from 0.388 to 1.113 around a reported estimate of 0.657. A confidence interval expresses uncertainty in the estimated comparison under the analysis method. It is not a range that contains the true effect with a probability that can be assigned after observing the data. A wider interval indicates less precision than a narrower interval would, and the interval spans both sides of the no-difference reference value.

That span matters for interpretation. The point estimate is below the reference, but the interval also includes values that do not indicate a difference in relative event rates. Thus the data do not pin down the direction and magnitude of the comparison precisely enough to treat the point estimate as conclusive. The reported p value, 0.295, is consistent with the uncertainty conveyed by the interval; neither should be interpreted as proof of equivalence.

The reported medians add descriptive information but do not resolve this uncertainty. The full ranges show the observed endpoints of the reported time distributions, not the precision of the hazard ratio or the distribution of times within each group. Precision is influenced by the event and follow-up information available to the analysis, but the registry record does not provide the event count for the primary analysis or enough information to quantify those contributions separately.

The extension comparison also has a confidence interval, from 0.37 to 1.296 around a reported hazard ratio of 0.693. It too spans the no-difference reference. Because this is an open-label treatment-sequence comparison, its precision and design context should be considered separately from the primary double-blind comparison. Neither interval supports a claim of exact equality between groups.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size table and curve are planning illustrations based on the observed effect, not the trial’s original design calculation. For this time-to-event analysis, the entries are the total number of events required, not participants per arm. The table shows planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect, with separate columns for 80% and 90% power. For example, planning for 100% of the observed effect gives 178 total events for 80% power and 239 for 90% power.

In plain language, the 80% power column describes the event total that the illustration associates with an 80% chance of detecting the stated effect under its assumptions, if that effect were real. The 90% power column uses a higher chance of detection and therefore shows a larger required event total. These are design-planning quantities, not descriptions of the result that this completed trial achieved.

The planning assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. For time-to-event tables, the method for translating the effect into required events is identified as Schoenfeld. The registry’s original sample-size assumptions are not reported in the registry record.

As the target effect becomes smaller, it is harder to distinguish from random variation, so the illustration requires more events. The curve visualizes the same planning relationship across the stated effect fractions and power targets. This is not observed power; it is a forward-looking illustration of event requirements under the listed assumptions.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.657, so ln(HR) = -0.4201.
2. d = 4 × (1.96 + 0.842)² / [ln(0.657)]² = 177.9, rounded up to 178 events in total for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
hr <- 0.657                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(2201108)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 178 (80% power), 239 (90% power)
 75% of observed effect: events = 317 (80% power), 424 (90% power)
 50% of observed effect: events = 712 (80% power), 953 (90% power)
Simulated power with 178 events: 0.772 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 291 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 166 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 9.03230769230769          # control-arm median, months (converted from the posted unit)
hr          <- 0.657          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
      N: 214         p (1-sided)   0.0001
  Events: 80        ~HR at bound   0.4360
   Month: 18    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.66   0.0338
   IA 2: 67%                   Z   2.5114
      N: 292         p (1-sided)   0.0060
 Events: 160        ~HR at bound   0.6721
   Month: 28    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.66   0.5603
       Final                   Z   1.9930
      N: 292         p (1-sided)   0.0231
 Events: 240        ~HR at bound   0.7730
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.66   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a stratified log-rank test, with a hazard ratio of 0.657, a 95% confidence interval from 0.388 to 1.113, and a p value of 0.295. This is the posted analysis to use when describing the primary result. The record does not flag a discrepancy between the sponsor analysis and a recalculation.

A simple recalculation from posted summary statistics, where available, is not a substitute for the sponsor’s analysis. A time-to-event comparison depends on the timing of events and follow-up, information that cannot generally be reconstructed from group medians alone. The registry’s reported hazard ratio and test should therefore remain the main inferential summaries.

No separate recalculated primary hazard ratio or test result is reported in the registry record. The table and plot can help readers inspect the posted results and their uncertainty, but should not be treated as a new analysis that supersedes the sponsor’s reported method or estimate.

16. Multiplicity, Missing Data and Analysis Populations

The trial includes a primary endpoint and a broad set of secondary outcomes, including relapse measures, MRI assessments, cognitive function, safety, tolerability, and pharmacokinetics. Testing many outcomes raises a multiplicity issue: even when there is no real difference on any measure, testing a collection of outcomes can produce some apparently unusual results by chance. Statistical plans can address this in different ways, but the approach used should be stated to interpret secondary p values as a family of evidence.

The registry record does not report whether multiplicity was controlled, which outcomes were included in any adjustment, or whether a hierarchy of testing was used. It also does not report planned interim analyses. These details should not be inferred from the number of outcomes or from the presence of a reported primary analysis. Without them, the primary endpoint can be distinguished from secondary outcomes, but the strength of evidence across the secondary outcome set cannot be assessed as a single confirmatory family.

The primary population is described as the intent-to-treat population, consisting of all randomized participants analysed according to assigned treatment. That definition is useful, but the registry does not provide a fuller account of missing-data procedures, analysis-set exclusions, or sensitivity analyses for unavailable outcome data. For the primary endpoint, participants without a confirmed relapse were considered relapse-free until the end of Week 96. Further details on censoring and other incomplete follow-up situations are not reported in the registry record.

Missing outcome information can affect both the estimate and its precision, particularly when the availability of data differs between groups or relates to participants’ outcomes. The record does not establish whether those conditions occurred. It is therefore appropriate to describe the stated analysis population and endpoint rule, while recognizing that the registry summary does not allow a full evaluation of missing-data handling or the broader statistical plan.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: alanine aminotransferase increased (3.8%), asthma (3.8%), bradycardia (3.7%), sudden hearing loss (3.7%), complicated appendicitis (3.7%).

For the double-blind treatment period, the registry lists 6 participants with serious adverse events among 57 at risk in the placebo group, and 12 among 109 at risk in the teriflunomide group. It reports 0 deaths in each of those groups. These are participant counts as displayed in the registry; they should not be converted into comparative rates without an analysis that accounts for the relevant exposure and follow-up.

The safety record also lists results for open-label treatment sequences and an extension period. Those groups represent different periods and treatment histories, so they should not be treated as additional randomized placebo-versus-teriflunomide comparisons. Serious adverse event counts describe events classified as serious in the registry, not all adverse events or the overall balance of risks.

The registry lists several serious adverse event terms, each with a displayed percentage, but those terms do not by themselves establish a causal relationship to treatment. The summary does not provide enough detail to compare exposure-adjusted safety or determine how individual events were assessed. Safety interpretation should remain descriptive and separate from the primary efficacy endpoint.

18. What the Result Does, and Does Not, Mean

The primary result is an estimate of the relative timing of first confirmed clinical relapse during the double-blind period, together with uncertainty around that estimate. The reported hazard ratio is 0.657, and its 95% confidence interval ranges from 0.388 to 1.113. Since the interval includes the no-difference reference and the reported p value is 0.295, the posted analysis does not establish a clear difference between the randomized groups on this endpoint.

That conclusion is not the same as showing that the groups are identical. The interval remains compatible with a range of possible comparisons, and the point estimate is only one part of the evidence. Nor does the result answer every question raised by the trial: the primary endpoint concerns a first confirmed relapse through Week 96, while MRI outcomes, cognition, safety, tolerability, pharmacokinetics, and longer follow-up involve different measures or timeframes.

The results also should not be interpreted as a treatment recommendation. They describe the posted comparison in the trial population and under the endpoint definition and analysis reported in the registry. The record does not provide enough information to extend this single primary result to other populations, settings, treatment durations, or outcomes.

The open-label extension is a separate context. Its listed treatment groups reflect treatment sequences, and its comparison should not be read as though it retained the original blinded placebo contrast. The study’s stated safety counts are also descriptive and do not, by themselves, establish whether an adverse event was caused by treatment.

In short, the primary estimate points in one direction, but its uncertainty is substantial enough that the registry result does not settle whether the groups differed in time to first confirmed relapse. The distinction between an uncertain estimate and evidence of equivalence is central to reading this result.

19. Why This Trial Matters Statistically

This trial offers a useful example of why clinical trial interpretation should distinguish an effect estimate from its precision. The reported hazard ratio gives a compact summary of the primary time-to-event comparison, while its confidence interval shows that the estimate remains uncertain. Reading only the point estimate would miss that the interval includes the no-difference reference.

It also illustrates the value of matching the method to the endpoint. The primary outcome concerns when a confirmed relapse occurs, so the registry reports a time-to-event analysis rather than only a count of participants with events. The endpoint definition, independent relapse adjudication, and intent-to-treat population all help explain what the analysis represents, while the registry’s missing methodological details mark the limits of what can be concluded.

The study’s secondary outcomes make another statistical point: a wide outcome set can add important dimensions, but it also complicates interpretation. Clinical relapse, MRI measures, cognitive function, safety, and pharmacokinetics are not interchangeable. Their results need to be considered according to their measurement, uncertainty, and place in the testing plan. The registry record does not report whether multiplicity was controlled.

Finally, the sample-size illustrations distinguish planning from inference after a trial. They show how required event totals change with the effect size and desired power under stated assumptions, but they do not reveal the original design rationale or the probability that this completed trial detected its true effect. Keeping those distinctions clear prevents planning quantities from being mistaken for trial results.

20. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification, planned interim analyses, or a complete statistical analysis plan. It also does not identify the stratification factors used for the primary log-rank test. These omissions limit independent assessment of how the primary analysis was planned and how the full set of outcomes was handled.

Details on missing data, incomplete follow-up, censoring beyond the stated Week 96 relapse-free rule, and sensitivity analyses are not reported in the registry record. The primary analysis is described as intent-to-treat, but the summary does not give further detail on adherence, analysis-set exclusions, or the amount of outcome information available for each participant.

The primary endpoint is specific: time to first confirmed clinical relapse up to Week 96, using the registry’s definition and independent adjudication. It does not capture all forms of disease activity or progression. The listed MRI and other secondary outcomes address additional questions, but the registry summary does not report an overall multiplicity approach for interpreting those results.

The open-label extension has different treatment sequences from the blinded period, so its comparison has a different design context and should not be treated as another placebo-controlled randomized comparison. The safety summaries also span multiple periods and groups. The listed counts are useful descriptions, but the record does not provide exposure-adjusted comparisons or enough detail to establish causation for individual adverse events.

Finally, the enrolled population was children and adolescents 10 to 17 years of age with relapsing forms of multiple sclerosis. The registry information does not establish how well these results apply beyond that population or beyond the conditions and follow-up described for this trial.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Efficacy, Safety and Pharmacokinetics of Teriflunomide in Pediatric Patients With Relapsing Forms of Multiple Sclerosis — NCT02201108.
• Registry record last updated 2025-02-06; status last verified 2025-01.
• Results first posted 2020-11-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

This completed Phase 3 study randomized 166 participants with relapsing forms of multiple sclerosis to oral teriflunomide or matching placebo during a quadruple-masked, parallel-group period, followed by an open-label extension. The primary endpoint was time to first confirmed clinical relapse through Week 96, analysed in the intent-to-treat population.

The registry reports median times of 39.14 weeks for placebo and 75.29 weeks for teriflunomide. The sponsor’s stratified log-rank analysis reports a hazard ratio of 0.657, with a 95% confidence interval from 0.388 to 1.113 and p = 0.295. The interval includes the no-difference reference, so the primary result does not establish a clear between-group difference.

Secondary outcomes address relapse, MRI measures, and other study objectives. The registry record does not report the full multiplicity, missing-data, or original design assumptions needed for a complete independent statistical assessment.