Efficacy and Tolerability of Rimegepant for the Acute Treatment of Migraine in Adults Unsuitable for Triptan Use: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Tolerability of Rimegepant for the Acute Treatment of Migraine in Adults Unsuitable for Triptan Use (NCT05509400), a randomized phase 4 study. The primary outcome is Percentage of Participants With Pain Relief at 2 Hours Post-Dose: DBT Phase.

2. Clinical Question

3. Trial Design

NCT05509400 is a completed phase 4 randomized trial of rimegepant for acute migraine treatment in adults considered unsuitable for triptan medications. The registry lists an enrollment of 813. The stated reasons for triptan unsuitability include previous intolerance, lack of efficacy, or a contraindication, including a history of clinically relevant cardiovascular disease. The trial began on 2022-10-18, and the primary completion date is 2025-03-10.

The double-blind phase compared one dose of rimegepant 75 mg oral disintegrating tablet with a matching placebo. The registry describes the study as quadruple masked and randomized, with a sequential model. It does not give further detail in the record about how the masking was implemented or what the sequential model means operationally, so those details are not reported in the registry record.

The trial also had an open-label extension. In that phase, participants could receive one dose of rimegepant 75 mg oral disintegrating tablet as needed for a qualifying acute migraine. The primary efficacy comparison, however, is explicitly labelled as being from the double-blind treatment phase. The open-label extension therefore should not be conflated with the randomized placebo comparison used for the primary endpoint.

The primary efficacy analysis set was narrower than the enrollment count. It included participants in the full analysis set who were randomized only once, took double-blind study drug, had a qualifying migraine attack at dosing, and had post-dose efficacy data. For the primary outcome, the posted groups comprise 286 participants in the rimegepant arm and 284 in the placebo arm. The registry record does not report the original sample-size justification, detailed allocation procedures, or the planned statistical analysis in sufficient detail to reconstruct those features.

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.

DBT Phase

Reasons for not completing this period:

OLE Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: DBT efficacy analysis set included participants in the full analysis set (FAS) who met all the following criteria: 1) randomized only once; 2) took DB study drug; 3) had qualifying migraine attack at the time of DB study drug dosing and 4) had DB post-dose efficacy data. FAS: participants who signed an informed consent form and were assigned a participant identification number and who received a randomization treatment assignment.

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: Safety analysis set (SAS) included participants in the enrolled analysis set who took \>= 1 dose of study drug. Enrolled analysis set included participants who signed an informed consent form and were assigned a participant identification number, i.e., non-missing informed consent date.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Pain Relief at 2 Hours Post-Dose: DBT Phase, measured over At 2 hours post-dose.

The primary endpoint is the percentage of participants with pain relief at 2 hours after dose during the double-blind treatment phase. Participants recorded headache pain intensity on a four-point numeric rating scale: 0 for none, 1 for mild, 2 for moderate, and 3 for severe. For this endpoint, pain relief means a rating of none or mild at the stated time point. It is not the same outcome as complete pain freedom, which is listed separately as a secondary endpoint.

A percentage endpoint is useful when the clinical question is whether participants meet a defined response at a particular time, rather than how far an individual’s score changes on average. The comparison describes the proportion meeting that definition in each group and the difference between those proportions. It does not describe the duration of relief beyond the assessment time, nor does it by itself capture every dimension of a migraine attack or its treatment.

The analysis was restricted to the double-blind efficacy analysis set described in the registry record. This matters because the primary result applies to participants meeting the stated analysis-set criteria, including having post-dose efficacy data. The registry record does not report further details about how missing pain-intensity observations were handled, or whether any additional rules were applied when determining endpoint status.

At 2 hours post-dose, the posted estimate was 55.9% in the rimegepant group and 32.7% in the placebo group. The reported difference in percentages was 23.2 percentage points, with a 95% confidence interval from 15.3 to 31.1 percentage points. These estimates describe the endpoint as defined; they should not be interpreted as a measure of all possible benefits, harms, or longer-term outcomes.

7. Results Posted in the Registry

• DB Rimegepant: 55.9% (160/286) versus 32.7% (93/284) on control; risk difference 23.2 percentage points (95% CI 15.3 to 31.1), risk ratio 1.71 (1.40–2.08); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Participants With Pain Freedom at 2 Hours Post-Dose: DBT Phase

• 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:
  • DB Rimegepant: 22.7% (65/286) versus 7.4% (21/284) on control; risk difference 15.3 percentage points (95% CI 9.6 to 21.1), risk ratio 3.07 (1.93–4.89); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DB Rimegepant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Used Rescue Medications Within 24 Hours Post-Dose: DBT Phase

• 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:
  • DB Rimegepant: 18.0% (51/283) versus 46.2% (129/279) on control; risk difference -28.2 percentage points (95% CI -35.6 to -20.8), risk ratio 0.39 (0.29–0.52); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for DB Rimegepant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Return to Normal Function at 2 Hours Post-Dose: DBT Phase

• 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:
  • DB Rimegepant: 28.9% (67/232) versus 12.7% (30/237) on control; risk difference 16.2 percentage points (95% CI 9.0 to 23.4), risk ratio 2.28 (1.54–3.37); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DB Rimegepant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes broadly address several related dimensions of the acute migraine episode: complete pain freedom at 2 hours, use of rescue medication within 24 hours, return to normal function at 2 hours, and sustained pain or functional outcomes over later time windows. For the three secondary outcomes with numerical results in the record, the group contrasts are directionally consistent with the primary result: the rimegepant group had a higher percentage for pain freedom and return to normal function, and a lower percentage for rescue medication use. These outcomes complement the primary endpoint because they concern related but distinct responses.

The secondary outcomes should not be treated as interchangeable with the primary endpoint. Pain relief allows a rating of mild pain, whereas pain freedom requires no pain. Rescue medication use records a subsequent action within a defined period, and normal function concerns a separate functional status. Sustained outcomes add duration requirements. Each endpoint therefore has its own definition, eligible observations, and interpretation.

The registry lists 23 outcome measures and 22 posted secondary outcomes, while the posted analysis count is 16. Numerical results are not present in the record for every listed secondary outcome. Where results are not given, they are not reported in the registry record; no direction or magnitude should be inferred from the outcome title alone.

Unadjusted secondary results carry less weight than a prespecified primary result because evaluating many outcomes increases the chance of finding at least one apparently notable result by chance. General statistical explanation: multiplicity procedures can control this risk, but they may also affect how uncertainty and significance are assessed. The registry record does not report whether multiplicity adjustments were planned or applied to these secondary comparisons. Their p-values and confidence intervals should therefore be interpreted as endpoint-specific, without assuming that they provide confirmatory evidence across the full outcome set.

Taken together, the available secondary results are supportive in direction of the primary endpoint, but they do not independently settle questions about the robustness of the full outcome family, longer-term effects, or clinical importance. They add context rather than replacing the primary comparison.

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

• Percentage of Participants With Pain Freedom at 2 Hours Post-Dose: DBT Phase
• Percentage of Participants Who Used Rescue Medications Within 24 Hours Post-Dose: DBT Phase
• Percentage of Participants With Return to Normal Function at 2 Hours Post-Dose: DBT Phase
• Percentage of Participants With Sustained Return to Normal Function From 2 to 24 Hours Post-Dose: DBT Phase
• Percentage of Participants With Sustained Return to Normal Function From 2 to 48 Hours Post-Dose: DBT Phase
• Percentage of Participants With Sustained Pain Relief From 2 to 24 Hours Post-Dose: DBT Phase
• Percentage of Participants With Sustained Pain Relief From 2 to 48 Hours Post-Dose: DBT Phase
• Percentage of Participants With Sustained Freedom From Pain From 2 to 24 Hours Post-Dose: DBT Phase

9. Statistical Interpretation

10. Statistical Methods Explained

The main comparison is between a binary outcome in two randomized groups. For each participant in the endpoint analysis set, the outcome is classified according to whether pain relief was present at 2 hours. The group percentages estimate the proportion meeting that definition in each arm. The primary effect measure is the difference in those percentages, expressed in percentage points. The registry labels its analysis method “Crude risk estimation” and its parameter “Difference in percentages.”

What does the difference in percentages express?

The absolute difference compares the two group proportions directly. A positive value in this comparison means the recorded outcome percentage is higher in the rimegepant group than in the placebo group; a negative value would mean it is lower. For the primary endpoint, the registry reports a difference of 23.2 percentage points. This is not a percentage increase and should not be confused with a risk ratio or odds ratio, which describe relative rather than absolute contrasts.

The posted recalculation uses the event counts and denominators recorded for the endpoint: 160 of 286 participants in the rimegepant group and 93 of 284 in the placebo group. The registry’s reported crude difference is 23.2 percentage points, with confidence limits from 15.3 to 31.1 and p < 0.001. These are unadjusted group comparisons; the record does not report a covariate-adjusted model for this endpoint. Because discrepancy is not flagged, the sponsor’s reported analysis and the recalculated estimate agree at the displayed precision.

What does a confidence interval add?

A confidence interval communicates uncertainty around an estimated effect. In general, a 95% confidence interval is generated by a procedure that, over repeated comparable studies under its assumptions, would cover the underlying effect in 95% of those studies. It is not a statement that there is a 95% probability that this particular interval contains the true effect. The interval for the primary difference ranges from 15.3 to 31.1 percentage points. Its width reflects the precision of the estimate; narrower intervals generally indicate greater precision, while wider intervals indicate more uncertainty.

How should the p-value be read?

The reported p-value, p < 0.001, is a test statistic expressed as a tail probability under a null hypothesis of no difference and the analysis assumptions. It describes how incompatible the observed data are with that null model, not the probability that the treatment has no effect. It does not measure clinical importance, prove that the analysis assumptions are correct, or account automatically for testing multiple endpoints. The registry record does not report whether a multiplicity adjustment was planned for the full set of outcomes.

Why might binary outcomes need careful analysis?

General statistical explanation: binary outcomes reduce each participant’s status at a time point to one of two categories. That makes the result easy to interpret as a proportion, but it also means information about the degree of change within each category is not represented in the percentage. The cutoff defining a response is important. Here, the primary cutoff is pain intensity of none or mild at 2 hours; complete pain freedom is a distinct outcome.

General statistical explanation: group percentages can vary with the mix of participants and with the number of observed outcomes. Confidence intervals account for sampling variability under a method’s assumptions, but they do not correct for bias arising from missing data, protocol deviations, or differences in how outcomes are recorded. The registry record’s stated analysis set requires post-dose efficacy data, while the handling of missing observations is not reported in the registry record.

What does the analysis set imply?

The primary efficacy set includes participants in the full analysis set who were randomized only once, took double-blind study drug, had a qualifying migraine attack at dosing, and had double-blind post-dose efficacy data. This defines the population to which the posted primary estimate directly applies. The registry record does not give the complete definition of the full analysis set in the available description. It also does not report details of imputation, sensitivity analyses, or other procedures that might address missing outcomes.

The sample-size calculations associated with the observed result are planning illustrations, not the trial’s original design calculation. They use the observed effect and stated planning assumptions. Such calculations answer a hypothetical planning question about how many participants might be needed for a future comparison under those assumptions; they do not change the uncertainty of this completed trial or establish what its investigators planned. The original sample-size assumptions and justification are not reported in the registry record.

Finally, the posted analysis is an unadjusted comparison of the randomized groups for a defined binary endpoint. Randomization supports a group comparison by design, but it does not eliminate uncertainty or resolve every issue concerning analysis population, missing data, measurement, or multiplicity. Those details should be considered alongside the effect estimate rather than inferred from the p-value alone.

11. Confidence Intervals and Precision

The primary estimate is a difference of 23.2 percentage points between the rimegepant and placebo groups. Its 95% confidence interval extends from 15.3 to 31.1 percentage points. The interval is entirely above zero, indicating that the data are compatible with a positive difference under the reported analysis. It also shows that the point estimate is not known with exact precision: a range of effect sizes remains compatible with the data.

In general, a confidence interval combines the estimated effect with its sampling uncertainty. It is not a range containing a fixed percentage of individual participant outcomes, and it does not say where the effect for a particular participant lies. A 95% confidence interval refers to the long-run performance of the method under its assumptions, rather than a 95% probability statement about the specific interval after the data have been observed.

The width of an interval depends on factors including the amount of information in the analysis and the variability of the estimate. It does not capture every possible source of uncertainty. For example, it does not automatically account for bias from missing data, outcome measurement, or selective reporting. The registry record does not report enough detail to assess all such possibilities or to establish how missing endpoint data were handled.

The group percentages also have their own 95% confidence intervals: 50.2 to 61.7 for rimegepant and 27.3 to 38.2 for placebo. These intervals describe uncertainty in each group percentage, while the interval for the difference directly addresses the between-group contrast. The difference interval is the most direct interval for the primary comparative question.

Precision is not synonymous with clinical importance. The registry record does not report a threshold for a clinically meaningful difference. The observed separation and its confidence interval therefore describe the statistical result, while judgments about clinical importance require a threshold and context not established by these estimates alone.

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 illustrations are expressed as participants per arm for the binary outcomes in this trial. They are not total event counts. For the primary endpoint, the illustration based on 100% of the observed effect gives 71 participants per arm for 80% power and 95 participants per arm for 90% power. Planning for 75% of the observed effect gives 125 participants per arm for 80% power and 167 participants per arm for 90% power. Planning for 50% of the observed effect gives 276 participants per arm for 80% power and 368 participants per arm for 90% power.

The assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. These assumptions describe the illustrations, not the trial’s original design: the registry record does not report the original sample-size justification or design assumptions.

In plain terms, 80% power is the probability of detecting an effect of the specified size at the stated significance level under the planning assumptions, if that effect is truly present. The 90% power column represents a higher target probability of detecting that specified effect. Reaching the higher target generally requires more participants under otherwise comparable assumptions. Likewise, smaller effects are harder to distinguish from random variation and require more participants than larger effects.

These are hypothetical planning quantities derived from the observed effect and are not observed power. They should not be read as an assessment of the probability that the completed trial’s result is correct, or as proof that the original trial was adequately or inadequately sized. The observed result and its confidence interval remain the direct evidence from the trial.

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 = 0.327; treatment proportion p₁ = 0.559; average p̄ = 0.443.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7026 = 1.3770.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6832 = 0.5750.
4. n = (1.3770 + 0.5750)² / (0.2320)² = 70.8, rounded up to 71 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 <- 0.327464788732394                          # control proportion
p1 <- 0.559440559440559                          # 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(5509400)
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 = 71 (80% power), 95 (90% power)
 75% of observed effect: n per arm = 125 (80% power), 167 (90% power)
 50% of observed effect: n per arm = 276 (80% power), 368 (90% power)
power.prop.test: 70.8 
Simulated power at n = 71 per arm: 0.809 (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 registry reports the sponsor’s primary analysis as crude risk estimation, with the difference in percentages reported as 23.2, a 95% confidence interval from 15.3 to 31.1, and p < 0.001. The unadjusted recalculation from the posted group counts gives a risk difference of 0.232, with the corresponding percentage-point estimate and confidence limits displayed as 23.2, 15.3, and 31.1. The figures agree at the displayed precision, and the registry record does not flag a discrepancy.

The sponsor’s analysis is the trial’s reported analysis and should be distinguished from a simple recalculation based on posted summary counts. A recalculation can check whether the summary statistics are consistent with an unadjusted comparison, but it cannot reproduce undisclosed details of the sponsor’s analysis or establish that both use every element of the same analysis procedure. Here, the reported method is crude risk estimation, and the displayed result aligns with the recalculation.

The p-values are recorded at different displayed thresholds: the sponsor reports p < 0.001, while the recalculation reports p < 0.001. Both indicate a small p-value, but they should not be substituted for one another or presented as identical precision. The sponsor’s reported p-value remains the trial’s own analysis result.

Neither the agreement of the estimates nor the small p-value resolves questions not addressed in the registry record, such as the full missing-data procedure, adjustment for other variables, or multiplicity handling. The effect estimate, confidence interval, analysis population, and these limitations should be read together.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcomes, including a primary endpoint and numerous secondary measures. Testing multiple endpoints creates a multiplicity issue: even when there is no true effect for any of several outcomes, repeated testing can make at least one result appear statistically notable by chance. General statistical explanation: a prespecified hierarchy or multiplicity adjustment can help manage that risk and clarify which results are confirmatory. The registry record does not report whether such a plan was used, how endpoints were ordered for testing, or whether the reported secondary p-values were adjusted.

The primary endpoint has a clearly stated definition and a reported sponsor analysis. The registry identifies the analysis set as participants in the full analysis set who were randomized only once, took double-blind study drug, had a qualifying attack at dosing, and had post-dose efficacy data. This means the estimate is directly about the defined efficacy analysis set. The full analysis set definition is incomplete in the record, and further details about exclusions or analysis conventions are not reported in the registry record.

Missing-data handling is another important uncertainty. The endpoint population requires post-dose efficacy data, but the registry record does not describe the extent or pattern of missing data, how missing endpoint observations were treated, or whether sensitivity analyses tested alternative assumptions. General statistical explanation: estimates can be affected if outcome availability is related to response or treatment group; a confidence interval based on observed outcomes alone does not resolve that concern.

The record also does not report whether the primary analysis included covariate adjustment, how protocol deviations were handled, or the detailed statistical analysis plan. The posted comparison is labelled crude risk estimation, which describes an unadjusted group contrast in the reported results. No additional model or missing-data method should be assumed.

These reporting gaps do not negate the posted result, but they limit how fully readers can evaluate the planned analysis, the control of false-positive risk across outcomes, and the sensitivity of conclusions to missing observations. The primary comparison can be described as reported, while the unreported procedures remain unknown.

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: abdominal pain upper (0.4%), abortion spontaneous (0.4%), suicidal ideation (0.4%).

During the double-blind treatment phase, the registry reports serious adverse events in 0 of 295 participants at risk in the rimegepant group and 0 of 290 participants at risk in the placebo group. No deaths are reported for either double-blind group. These are event counts for the safety population listed for that phase, not the efficacy analysis denominators used for the primary endpoint.

Other adverse events are reported in 116 of 295 participants at risk in the double-blind rimegepant group and 20 of 290 participants at risk in the double-blind placebo group. The registry’s serious-event listings include “Abdominal pain upper,” “Abortion spontaneous,” and “Suicidal Ideation,” each shown as 0.4%. The record also lists serious-event and other-event counts for the post-double-blind, open-label extension, and follow-up phases. Those phases involve different exposure histories and should not be combined with the double-blind comparison as if they were one randomized contrast.

A zero serious-event count in these groups means no serious events were recorded in the listed at-risk groups during the specified phase; it does not establish that a risk is absent. The registry figures alone do not describe event timing, causal attribution, severity beyond the serious classification, or a comparative safety analysis. The record’s counts should be read as descriptive safety reporting rather than proof of safety or a complete assessment of risk.

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

The primary result means that, in the double-blind efficacy analysis set, a higher percentage of participants assigned to rimegepant met the registry’s definition of pain relief at 2 hours than participants assigned to placebo. The reported percentages were 55.9% and 32.7%, and the reported difference was 23.2 percentage points, with a 95% confidence interval from 15.3 to 31.1. The interval is compatible with a positive difference under the reported analysis.

This result does not mean that every participant experienced relief, that all participants became pain-free, or that relief necessarily continued after the 2-hour assessment. The endpoint counts none or mild pain as relief; complete pain freedom is a separate outcome. Nor does the result describe every symptom, functional consequence, or subsequent course of a migraine attack.

The comparison also does not establish the result for every adult with migraine. The trial concerns adults considered unsuitable for triptan medications because of previous intolerance, lack of efficacy, or a contraindication. The directly analyzed population was further defined by the double-blind efficacy-set criteria. Applicability to people outside that population cannot be determined from the primary estimate alone.

A statistically small p-value does not by itself establish clinical importance. The registry record does not report a threshold for a clinically meaningful difference, and a treatment decision involves considerations beyond this endpoint, including adverse events and individual circumstances. The descriptive safety figures do not establish the absence of risk, while the efficacy estimate does not provide a full benefit-harm assessment.

Finally, the primary result is a comparison from the randomized, double-blind phase, not a conclusion based on the open-label extension. The extension provides a different treatment context and is not the randomized placebo-controlled primary contrast. The posted result is evidence about a specific outcome, time point, analysis population, and comparison; it should not be stretched into a broader claim than those data support.

18. Why This Trial Matters Statistically

This trial is statistically informative because its primary endpoint is defined in a concrete way: pain intensity of none or mild at 2 hours after dosing. That definition makes the outcome interpretable as a percentage meeting a stated response threshold, while also making clear that pain relief is not identical to complete pain freedom. The separate endpoint definitions matter when comparing results or considering what the primary estimate does and does not capture.

The randomized, double-blind placebo comparison provides a direct contrast during the treatment phase. The posted percentages and absolute difference allow readers to assess both the group outcomes and their separation, while the confidence interval conveys uncertainty around that separation. Reporting an absolute difference is especially useful for understanding the scale of a binary-outcome contrast without relying solely on a relative measure or a p-value.

The trial also illustrates why analysis populations must be read alongside enrollment. The registry records enrollment of 813, but the primary endpoint uses a narrower efficacy analysis set, with 286 participants in the rimegepant group and 284 in the placebo group. The estimate therefore pertains to the specified endpoint population and not automatically to everyone enrolled.

At the same time, the available record highlights reporting questions that affect statistical interpretation: the original sample-size justification, missing-data procedures, and multiplicity approach are not reported in the registry record. These omissions do not change the numerical comparison, but they constrain evaluation of the planned analysis and the full set of outcomes. The posted result is best understood through the combination of endpoint definition, effect size, interval, analysis set, and reporting limitations rather than through significance alone.

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.

Several limitations are specific to interpreting this trial from the registry record. The primary result applies to the double-blind efficacy analysis set, which required a qualifying attack at dosing and post-dose efficacy data. It may not represent all enrolled participants, and the record does not provide a complete account of the full analysis set or all reasons participants were excluded from the endpoint analysis.

The registry does not report the missing-data method, the amount or pattern of missing endpoint observations, or sensitivity analyses. Because post-dose efficacy data are part of the analysis-set criteria, the effect of missingness on the result cannot be evaluated from the record alone. Detailed protocol-deviation handling and any covariate adjustment are also not reported.

The original sample-size justification and design assumptions are not reported in the registry record. The displayed planning illustrations use the observed effect under stated assumptions and should not be mistaken for the trial’s original planning calculation. The record also does not report whether an interim analysis occurred or provide details of any monitoring plan.

The record includes multiple secondary outcomes, but does not report a multiplicity strategy. This limits the confirmatory interpretation of secondary results, particularly where many outcomes may be tested. Numerical results are not posted for every listed secondary outcome, and conclusions cannot be inferred for those without results.

Safety reporting is organized across the double-blind phase, transition periods, open-label extension, and follow-up. Those descriptive counts do not by themselves provide a fully adjusted comparative safety assessment, and phase-specific counts should not be treated as equivalent randomized comparisons. Finally, the primary endpoint is one pain assessment at 2 hours; it does not fully characterize duration, recurrence, all symptoms, function, or longer-term outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Tolerability of Rimegepant for the Acute Treatment of Migraine in Adults Unsuitable for Triptan Use — NCT05509400.
• Registry record last updated 2026-04-21; status last verified 2026-04.
• Results first posted 2026-04-21.
• 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

NCT05509400 is a completed phase 4 randomized, quadruple-masked, placebo-controlled trial of rimegepant for acute migraine treatment in adults unsuitable for triptan use. The registry lists an enrollment of 813 and a double-blind phase comparing one dose of rimegepant 75 mg oral disintegrating tablet with matching placebo, followed by an open-label extension.

The primary endpoint was pain relief at 2 hours, defined as none or mild pain. The posted percentages were 55.9% for rimegepant and 32.7% for placebo. The sponsor reported a difference of 23.2 percentage points, with a 95% confidence interval from 15.3 to 31.1 and p < 0.001; the unadjusted recalculation agrees at the displayed precision.

The interpretation is specific to the double-blind efficacy analysis set and the stated endpoint. The registry record does not report the original sample-size justification, detailed missing-data procedures, or multiplicity strategy. Secondary outcomes and safety counts provide additional context but do not replace the primary randomized comparison or establish a complete assessment of clinical importance and risk.