Study of Montelukast on Gastrointestinal Tolerability in Patients With Relapsing Forms of Multiple Sclerosis Receiving Tecfidera: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Montelukast on Gastrointestinal Tolerability in Patients With Relapsing Forms of Multiple Sclerosis Receiving Tecfidera (NCT02410278), a randomized phase 4 study. The primary outcome is Percentage of Participants With a Worsening in Severity of Gastrointestinal (GI) Adverse Events (AEs) on the GSRS From Day 0 to Day 10.

2. Clinical Question

The question is about gastrointestinal symptom severity during the early period after randomized treatment began. It is not a general test of all DMF effects or of multiple sclerosis outcomes. The registry also lists secondary questions about symptom change over other timeframes, time to worsening or recovery, use of gastrointestinal symptomatic therapy, discontinuation due to gastrointestinal adverse events, and flushing after DMF. Those outcomes provide additional context, but the primary comparison is the specified Day 0 to Day 10 worsening measure.

3. Trial Design

The registry describes NCT02410278 as a completed, phase 4, multicenter, randomized, triple-masked, parallel-group study sponsored by Biogen. The study title identifies people with relapsing forms of multiple sclerosis receiving Tecfidera. Enrollment was 102. The registry records a start date of 2015-03-12 and a primary completion date of 2017-02-16. These are study-record dates and do not, by themselves, describe the duration of treatment or follow-up for each participant.

Both groups received dimethyl fumarate. One group also received montelukast and the other received matched placebo. The montelukast regimen is described as 10mg once daily according to the prevailing product label. The primary endpoint analysis used the modified intention-to-treat population rather than every randomized participant: participants had to receive DMF and study treatment and contribute at least one GSRS measurement during Day 1 to Day 10. The exact allocation sequence, concealment procedures, and roles covered by triple masking are not reported in the registry record.

The primary outcome was the percentage with worsening gastrointestinal adverse-event severity on the GSRS from Day 0 to Day 10. The registry defines Day 0 in relation to reaching a gastrointestinal threshold and starting randomized treatment; it can be the day before treatment or the first treatment day, depending on the threshold timing. Secondary outcomes extend measurement to later periods and include symptom trajectories, time-to-event outcomes, symptomatic therapy use, and discontinuation attributed to gastrointestinal adverse events. The registry lists 10 outcome measures and 17 analyses. Details of the original sample-size justification, the full statistical analysis plan, interim analyses, and the handling of all analysis populations are not reported in the registry record.

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 screened over 2 weeks. Those who met ≥1 of the following criteria were considered screen failures: a score of ≥5 on 1 question for 1 day on the Gastrointestinal Symptom Rating Scale (GSRS), ≥4 or ≥3 on 1 question for 2 or 3 consecutive days, respectively; and eDiary compliance of \<75% over 14 days prior to randomization.

Run-in Period

Reasons for not completing this period:

Study Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The MITT: All participants who were randomized, received at least 1 dose of DMF treatment, received at least 1 dose of study treatment (montelukast or placebo) on/after the first DMF dose date, and had at least 1 GSRS score measurement during the Day 1 - Day 10 period.

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: The MITT: All participants who were randomized, received at least 1 dose of DMF treatment, received at least 1 dose of study treatment (montelukast or placebo) on/after the first DMF dose date, and had at least 1 GSRS score measurement during the Day 1 - Day 10 period.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With a Worsening in Severity of Gastrointestinal (GI) Adverse Events (AEs) on the GSRS From Day 0 to Day 10, measured over Baseline (Day 0), Day 10 (10 days after Day 0).

The primary endpoint is the percentage of participants whose gastrointestinal symptom severity worsened on the Gastrointestinal Symptom Rating Scale between baseline and Day 10. The GSRS contains 15 questions and was modified from weekly recall to daily recall for this study. Each item uses a seven-point Likert scale, scored from 0 for no discomfort at all to 6 for very severe discomfort. The overall score is a mean ranging from 0, no symptoms, to 6, the worst possible symptoms.

Worsening was defined as a positive average change from baseline in the GSRS score. The registry describes average change as the sum of changes from baseline over the first 10 days divided by the number of days with a GSRS score. The endpoint therefore reduces repeated symptom measurements to a participant-level classification of whether the average change was positive. It focuses on early gastrointestinal symptom severity after randomized treatment begins, rather than on a single symptom, a diagnosis, or a later clinical event.

A binary endpoint can be communicated as the proportion meeting a defined worsening criterion in each group. It is useful for comparing how often the specified event occurred, but it does not convey the magnitude of score change among participants who worsened, or distinguish those with a small change from those with a larger one. The registry definition and analysis population should be kept in view when interpreting the reported percentages.

7. Results Posted in the Registry

• MITT-Montelukast: 33.3% (11/33) versus 16.7% (5/30) on control; risk difference 16.7 percentage points (95% CI -4.2 to 37.6), risk ratio 2.00 (0.79–5.09); unadjusted two-proportion z-test p = 0.129.

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.

Time to First Worsening From Baseline in GSRS Overall Score at Day 1 to Day 10

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • MITT-Placebo vs MITT-Montelukast: hazard ratio 1.09 (95% CI 0.55–2.16), reported p = 0.795 (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 MITT-Placebo vs MITT-Montelukast and the control. The interval gives the range of effects that remain compatible with the data.

Time to Recovery to Baseline GSRS Score From Last Occurrence of Worst GSRS Score at Day 1 to Week 8

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • MITT-Placebo vs MITT-Montelukast: hazard ratio 0.95 (95% CI 0.56–1.59), reported p = 0.833 (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 MITT-Placebo vs MITT-Montelukast and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Required GI Symptomatic Therapy During the Study

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • MITT-Montelukast: 33.3% (11/33) versus 33.3% (10/30) on control; risk difference 0.0 percentage points (95% CI -23.3 to 23.3), risk ratio 1.00 (0.50–2.01); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MITT-Montelukast and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results described in the registry span symptom worsening and recovery over time, and whether participants required gastrointestinal symptomatic therapy. Across these comparisons, the estimates do not show a clear, consistent pattern that materially resolves the uncertainty in the primary endpoint. The therapy-use proportions are equal at the displayed precision, while the time-to-event comparisons have intervals that include their null values. These results do not independently establish a benefit or harm for montelukast.

The secondary outcomes are related to the primary question because they examine gastrointestinal symptoms or their management over other timeframes. They are not interchangeable with the primary endpoint: time to first worsening and recovery concern event timing, whereas symptomatic therapy use is a binary management outcome. A result on one measure cannot automatically be treated as confirmation of a result on another. The registry lists 10 outcome measures and reports 9 secondary outcomes, but full numerical results for every secondary outcome are not described in the registry record for this analysis.

Multiplicity matters because testing many outcomes creates more opportunities for apparently notable results to arise by chance. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of the secondary outcomes. For that reason, unadjusted secondary p-values and estimates carry less weight than a single prespecified primary analysis, particularly when they are considered alongside one another. The secondary findings are best treated as contextual and hypothesis-generating, not as separate definitive tests of treatment effect.

The broad pattern should be interpreted together with the primary endpoint's wide interval and the limitations of the modified intention-to-treat population. Absence of a statistically clear secondary difference is not proof of no effect, just as an isolated secondary finding would not by itself establish an effect. The posted results describe measured outcomes during the specified periods and do not provide a complete account of all possible gastrointestinal experiences.

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

• Average Change From Baseline in GSRS Overall Score at Day 1 to Day 10
• Average Change From Baseline in GSRS Overall Score at Day 1 to Week 10
• Time to First Worsening From Baseline in GSRS Overall Score at Day 1 to Day 10
• Time to Recovery to Baseline GSRS Score From Last Occurrence of Worst GSRS Score at Day 1 to Week 8
• Average Change From Baseline in GSRS Overall Score at Day 1 to Weeks 1 to 8
• Average Change From Baseline in GSRS Overall Score at Day 0 to 72 Hours From the Initiation of Randomized Study Treatment
• Percentage of Participants Who Required GI Symptomatic Therapy During the Study
• Percentage of Participants Who Discontinued DMF Therapy Due to GI-Related Adverse Events (AEs) From Day 0 to Week 10

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant in the stated analysis population either met the registry definition of worsening or did not. A comparison of two binary outcomes can be expressed in several ways. The risk difference compares the group proportions by subtraction, while a risk ratio compares them as a ratio and an odds ratio compares the odds. These measures answer related but different questions and need not have numerically similar values. The primary recalculation is presented as an unadjusted risk difference; the sponsor's reported analysis uses weighted logistic regression and reports an odds ratio.

What does the risk difference represent?

The risk difference is the estimated difference between the proportion with worsening in the montelukast group and the proportion in the placebo group, using the stated group order. A value of zero represents equal observed risks. A positive estimate indicates a larger observed proportion in the first named group under that subtraction convention; a negative estimate indicates a smaller one. The estimate of 0.167 is an absolute contrast on the proportion scale. It is not a relative increase and it does not, on its own, establish a causal effect.

The unadjusted recalculation uses the reported event counts and analysis-population sizes. The posted results give 5 events among 30 participants in the placebo group and 11 among 33 participants in the montelukast group. These are the analysis denominators for this endpoint, not the overall enrollment count. A recalculation from summary counts is useful for making the comparison transparent, but it does not reproduce a model that accounts for weighting or other modeling choices. The recalculation is not labeled as a replacement for the sponsor's analysis.

What does the logistic-regression result add?

Logistic regression models the odds of a binary outcome. The sponsor reports a weighted logistic regression estimate as an odds ratio, with a confidence interval and p-value. An odds ratio of 1 is the no-association reference value. The reported estimate is 3.931, and its 95% confidence interval extends from 0.938 to 20.832. Because the interval includes 1, the model's uncertainty includes the null value. The interval is also broad, indicating that the estimate is not precise. The registry record does not report the details needed to reproduce the weights, the covariates, or all model diagnostics, so the sponsor model cannot be independently reconstructed from the posted summary alone.

A p-value describes how incompatible the observed data are with a specified null model, given the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The unadjusted recalculated p-value is 0.129; the sponsor analysis reports p = 0.062. The difference in p-values is not evidence of a discrepancy in the registry record, which explicitly marks no discrepancy. The analyses use different methods and measures, and the model-based estimate is the sponsor's reported analysis.

How should the confidence interval be read?

A confidence interval describes the range of effect values reasonably compatible with the data under the statistical method and its assumptions. It displays uncertainty around an estimate, rather than providing a guarantee that the true effect falls within the particular interval. For the risk difference, the interval ranges from -0.042 to 0.376. Since it crosses zero, it is compatible with no difference as well as with differences on either side. For an odds ratio, the corresponding no-association value is 1; the sponsor's interval also crosses that reference. The width of both intervals matters: a result that is not statistically distinguishable from the null can still be imprecise and compatible with potentially meaningful effects in either direction.

Time-to-event outcomes use a different form of analysis. A Cox regression estimates a hazard ratio, comparing the instantaneous event rates over follow-up under the model. The hazard ratio is not a ratio of medians and should not be read as the probability that an individual experiences an event. Interpretation depends on the event definition, censoring, follow-up, and model assumptions. The registry reports Cox regression for the two time-to-event outcomes described in the results, but further model diagnostics and assumptions are not reported in the registry record.

The secondary outcome on requiring gastrointestinal symptomatic therapy is binary. The registry reports a Chi-squared analysis with p = 1.000. A Chi-squared test assesses compatibility between categorical outcomes and the null hypothesis of no association, using its own assumptions. The observed percentages are 33.0% in both groups at the precision displayed. The test does not establish equivalence; equivalence requires a prespecified margin and an appropriate analysis, neither of which is reported in the registry record.

Why can dispersion and outcome definition matter?

For continuous or count outcomes, variability affects how precisely a group mean or rate is estimated. For count data, over-dispersion means the variation is greater than expected under a simple model; ignoring it can make uncertainty look too small. This is general statistical context, not a claim that over-dispersion was present in this trial. The primary outcome is binary, so its analysis concerns event proportions rather than an estimated mean symptom score. Its definition still compresses repeated GSRS scores into a positive-change classification and consequently loses information about the size and pattern of score changes.

For time-to-event outcomes, participants may have different amounts of observed follow-up, and some may not experience the event during observation. Censoring methods allow such follow-up to contribute information without treating participants as if they had an event at the end of observation. This is a general explanation of time-to-event methods; the censoring details for this trial are not reported in the registry record. Statistical inference also depends on the number and timing of observed events, not just the size of the enrolled groups.

Interpretation should keep the analysis population, endpoint definition, estimate, interval, and method together. No one component answers every question. A point estimate describes the direction and magnitude on its own scale, a confidence interval conveys precision, and the p-value assesses compatibility with a null hypothesis under a method's assumptions. None of these alone establishes clinical importance or causation.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.167, with a 95% confidence interval from -0.042 to 0.376. The interval crosses zero, the value representing no difference on this scale. It therefore does not exclude either a modest difference favoring the placebo group or a larger difference favoring the montelukast group, according to the stated contrast direction. The estimate itself is positive, but the interval shows why the point estimate should not be treated as a settled effect.

The sponsor's odds-ratio interval is 0.938 to 20.832 around an estimate of 3.931. For an odds ratio, 1 is the no-association value. The interval includes that value and extends over a broad range, indicating considerable uncertainty in the model-based estimate. Risk differences and odds ratios are on different scales, so their interval endpoints should not be compared as if they represented the same quantity.

Confidence intervals are not a direct measure of clinical importance. They show statistical precision conditional on the chosen model and its assumptions, while clinical importance requires judgment about the outcome and context. The registry record does not report a threshold for a clinically important change in the risk difference or the GSRS endpoint. Thus, the interval can describe statistical uncertainty but cannot classify each compatible value as clinically important or unimportant.

The analysis population is relatively limited in size compared with overall enrollment, and the primary outcome requires a qualifying GSRS measurement. The registry record defines who was included but does not report enough detail to assess the consequences of missing measurements or departures from the intended analysis. These limitations make it important to distinguish the precision of the posted estimate from the broader completeness of the evidence.

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 planning figures are illustrations based on the observed effect, not the trial's original design justification. For the binary primary endpoint, the figures are participants per arm. For the time-to-event outcomes, the figures are total events, not participants per arm. Those are different planning quantities and should not be compared as if they shared the same denominator.

The stated illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the stated fraction of the observed effect as the effect to detect. The registry record does not report the trial's own original sample-size assumptions or justification. The 80% power column represents a planning target under which the assumed design would have an 80% chance of detecting the specified effect if that effect were true and the assumptions held. The 90% power column uses a higher chance-of-detection target under those same planning assumptions.

For the primary endpoint, planning for 100% of the observed effect gives 105 participants per arm for 80% power and 140 participants per arm for 90% power. Planning for 75% of the observed effect gives 177 participants per arm for 80% power and 236 participants per arm for 90% power. Planning for 50% of the observed effect gives 372 participants per arm for 80% power and 498 participants per arm for 90% power. The pattern illustrates that smaller effects require more participants to detect under the stated assumptions.

These are planning illustrations and are not observed power. They do not show the probability that the trial's result is true, and they do not revise the trial's actual design. The time-to-event planning rows use total events; their event targets should not be mistaken for group enrollment targets.

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

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.167; treatment proportion p₁ = 0.333; average p̄ = 0.250.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6124 = 1.2002.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6009 = 0.5058.
4. n = (1.2002 + 0.5058)² / (0.1667)² = 104.8, rounded up to 105 participants per arm 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
p0 <- 0.166666666666667                          # control proportion
p1 <- 0.333333333333333                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2410278)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 105 (80% power), 140 (90% power)
 75% of observed effect: n per arm = 177 (80% power), 236 (90% power)
 50% of observed effect: n per arm = 372 (80% power), 498 (90% power)
power.prop.test: 104.8 
Simulated power at n = 105 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor reports the primary inferential analysis as a weighted logistic regression model. It estimates an odds ratio of 3.931, with a 95% confidence interval from 0.938 to 20.832 and p = 0.062. The registry record lists no discrepancy between that result and the recalculated comparison. Under the stated reporting convention, the sponsor's own analysis is the principal model-based result; the recalculation is a simple, unadjusted contrast from the posted summary counts.

The recalculation expresses the comparison as a risk difference of 0.167, with a 95% confidence interval from -0.042 to 0.376 and p = 0.129. The logistic-regression estimate is an odds ratio, so its numeric value is not directly comparable with the risk difference. The analyses also differ in method: one is a weighted model and the other uses the observed event counts without adjustment. The registry record does not report sufficient details about the weighting or model specification to reproduce the sponsor's analysis independently.

Both intervals include their respective null values. The results therefore do not give a precise basis for asserting a difference, while also not establishing that the groups are equivalent. The recalculation is helpful for transparent description of the raw group proportions; it should not be used to displace the sponsor's prespecified or official analysis. Whether the analysis was prespecified, and the details of any analysis plan, are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcome measures and analyses, including a primary endpoint and several secondary outcomes assessed over different timeframes. When many hypotheses are tested, the chance of at least one apparently unusual result can increase even if no underlying treatment difference exists. A multiplicity strategy can control or otherwise address that issue, for example by specifying a testing hierarchy or adjusting significance thresholds. Such a strategy is not reported in the registry record. It is therefore not possible to determine from the record whether secondary tests were intended as confirmatory, exploratory, or part of a formal testing sequence.

The registry describes the primary analysis population as participants who were randomized, received at least one dose of DMF, received at least one dose of montelukast or placebo on or after the first DMF dose, and had at least one GSRS score during Day 1 to Day 10. This modified intention-to-treat definition is narrower than a simple analysis of every randomized participant. It helps define exactly whose outcome data contribute to the primary comparison, but it also means that the reported endpoint estimates do not describe all randomized participants regardless of treatment exposure or measurement availability.

The reasons participants may not have contributed qualifying GSRS measurements, the amount and pattern of missing outcome data, and the method used to handle missing values are not reported in the registry record. The record also does not report whether sensitivity analyses assessed how missingness could affect the result. Missing data can affect interpretation if the probability of a missing measurement is related to symptoms or treatment experience; this is a general methodological concern, not evidence that such a pattern occurred in this trial.

The registry record does not report the original sample-size justification, a complete statistical analysis plan, interim analyses, or the full details of model covariates and weighting. Those omissions limit assessment of how the analyses were selected and whether all planned analyses are represented. They do not invalidate the posted results, but they restrict what can be concluded about prespecification, multiplicity control, and robustness to alternative analysis choices.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: microcytic anaemia (3.2%), alanine aminotransferase increased (3.2%), aspartate aminotransferase increased (3.2%), multiple sclerosis relapse (3.2%), laryngeal squamous cell carcinoma (3.0%).

The registry reports serious adverse events and other adverse events in separate safety populations. In the DMF Safety Population, 3 of 98 participants had a serious adverse event and 35 of 98 had another adverse event. In the Primary Safety Population-Placebo group, the figures were 2 of 31 for serious adverse events and 14 of 31 for other adverse events. In the Primary Safety Population-Montelukast group, the figures were 1 of 33 and 14 of 33, respectively. No deaths were reported in any of these groups.

These figures are counts within the registry's stated safety populations; they are not the same population definition as the primary endpoint analysis. Serious adverse events and other adverse events are separate summaries, and the figures do not establish that a treatment caused an event. The registry also lists several serious adverse-event terms and their reported percentages, but those terms should not be read as a complete assessment of comparative safety. The record's event counts and population sizes provide descriptive context, not a test designed to determine whether the treatments differ in safety.

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

The primary result describes the proportion meeting a defined worsening criterion on a daily-recall version of the GSRS during the period from Day 0 to Day 10. In the analyzed groups, the posted proportions were 17.0% with placebo and 33.0% with montelukast. The estimated risk difference is positive in the stated comparison direction, but its confidence interval includes no difference and extends to effects in either direction. The appropriate conclusion is that the estimate is uncertain, not that the groups have been shown to be the same or that a treatment effect has been established.

The outcome is a symptom-scale classification, not a direct measure of every aspect of gastrointestinal tolerability. A positive average change marks worsening according to the registry definition; it does not indicate how severe the symptoms were for each participant or whether an individual found the change important. The score averages 15 questions, and turning that score into a binary worsening outcome discards information about the magnitude of change. The study's secondary measures add different views of symptoms and management, but they also have their own definitions and uncertainty.

The trial compares montelukast added to DMF with placebo added to DMF. It does not estimate the effect of DMF compared with no DMF, and it does not establish effects on multiple sclerosis disease activity. The registry record also does not establish a mechanism for gastrointestinal symptoms or explain individual decisions to discontinue treatment. No medical recommendation follows from these statistical results alone.

Finally, a non-significant p-value is not proof of no effect, and a point estimate in one direction is not proof of an effect. The confidence intervals, analysis population, endpoint construction, and the distinction between sponsor modeling and unadjusted recalculation all matter. The findings are best read as a comparison with appreciable uncertainty in this completed trial and its specified measurement period.

18. Why This Trial Matters Statistically

This study illustrates why a trial result should not be reduced to a single p-value. The primary proportions and estimated risk difference provide a direct description of the observed groups, while the confidence interval shows that the data remain compatible with a range of effects. The sponsor's weighted logistic regression expresses the result on an odds scale and uses a different method. Reading the estimate, interval, analysis population, and endpoint definition together gives a more complete statistical interpretation than treating a threshold test as the entire result.

The endpoint also demonstrates a design choice with interpretive consequences. Repeated daily symptom scores were condensed into whether average change was positive. This produces an easily communicated event proportion, but it does not preserve all information about symptom magnitude or the course of scores. Secondary measures of timing, recovery, and symptom-management use provide complementary perspectives, yet multiple outcomes raise questions about multiplicity and the weight assigned to each result.

Finally, the planning illustrations show how desired precision and target effect size influence sample-size requirements under stated assumptions. They are distinct from the trial's unreported original design rationale and from retrospective notions of power. Separating planning calculations from observed evidence helps prevent an estimated effect from being mistaken for a fixed truth. The record is a useful case for considering how outcome construction, analysis choices, uncertainty, and reporting completeness jointly shape what a clinical trial can support.

19. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary result is based on the modified intention-to-treat population, which required treatment exposure and a qualifying GSRS measurement. Participants without the specified measurement do not contribute to that endpoint estimate, and the registry record does not report the number or reasons for missing measurements or the missing-data approach. This makes it difficult to assess whether missing outcome information could have influenced the comparison.

The primary endpoint is a derived binary classification from repeated symptom scores. It identifies a positive average change but does not report the size of each participant's change in the primary comparison. The registry describes the scale and the averaging rule, but a threshold for a clinically important between-group difference is not reported in the registry record. The observed event proportions should therefore not be treated as a complete description of symptom experience.

The sponsor's weighted logistic regression is reported with an odds ratio, but the weighting details, model covariates, and diagnostics are not reported in the registry record. The unadjusted recalculation is transparent from the summary counts but cannot reproduce those modeling choices. The primary and recalculated estimates also use different effect measures, so their values are not directly interchangeable.

Several outcomes and analyses are listed, while a multiplicity strategy, full statistical analysis plan, interim analyses, and original sample-size justification are not reported in the registry record. This limits evaluation of prespecification and the evidential status of secondary findings. Further, the primary observation period is early, from Day 0 to Day 10; the primary result should not be generalized to longer-term symptom effects without evidence from the relevant follow-up outcomes. The registry's completed status does not resolve these design and reporting limitations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Montelukast on Gastrointestinal Tolerability in Patients With Relapsing Forms of Multiple Sclerosis Receiving Tecfidera — NCT02410278.
• Registry record last updated 2020-03-31; status last verified 2020-03.
• Results first posted 2018-07-24.
• 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.

23. Record Summary

NCT02410278 was a completed, phase 4, multicenter, randomized, triple-masked, parallel-group study sponsored by Biogen. It enrolled 102 participants and compared DMF plus montelukast with DMF plus matched placebo in people with relapsing forms of multiple sclerosis receiving Tecfidera.

The primary endpoint was the percentage in the modified intention-to-treat population with worsening GSRS severity from Day 0 to Day 10. The posted proportions were 17.0% for placebo and 33.0% for montelukast. The unadjusted recalculated risk difference was 0.167, with a 95% confidence interval from -0.042 to 0.376; the sponsor's weighted logistic regression reported an odds ratio of 3.931, with a 95% confidence interval from 0.938 to 20.832. Both analyses leave substantial uncertainty, and the registry reports no discrepancy between them.

The registry also reports secondary symptom and safety outcomes. Missing-data handling, multiplicity procedures, original sample-size justification, and further statistical-plan details are not reported in the registry record.