Safety and Efficacy Study in Adult Subjects With Acute Migraines: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study in Adult Subjects With Acute Migraines (NCT03235479), a randomized phase 3 study. The primary outcome is Percentage of Participants With Freedom From Pain at 2 Hours Post-dose.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, triple-masked, parallel-group, placebo-controlled trial of rimegepant for acute migraine. The registry record identifies Pfizer as the sponsor and reports enrollment of 1485 participants with migraine, with or without aura. The study began on 2017-07-18, reached primary completion on 2018-01-21, and is listed as completed.

Participants were assigned to rimegepant 75 mg or matching placebo. The treatment was a single oral dose taken when a migraine reached moderate or severe intensity, up to 45 days after randomization. The intervention descriptions specify the same dosing occasion and time window for both groups. The registry record does not report the allocation ratio or further details of the randomization procedure.

Triple masking indicates that the registry record classifies the study as masked across three roles, but the identities of those roles are not reported in the registry record. The record also does not describe the practical steps used to maintain masking or whether masking was assessed.

The primary endpoint was the percentage of participants free from pain at two hours after dosing. The registry record says that pain was assessed using an electronic diary and a four-point scale. Its stated definition of pain freedom was a pain level of none. The primary analysis population was modified intent to treat. Arm-specific outcome counts were 543 for rimegepant and 541 for placebo, which are the denominators associated with the posted primary outcome results. The registry record does not explain the difference between those analysis counts and total enrollment.

The study also assessed other symptoms, pain relief, rescue medication use, sustained pain outcomes, and safety. Further detail about the protocol, original sample-size justification, planned interim analyses, and full statistical analysis plan is 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: A total of 1485 participants were enrolled, of which 1162 participants were randomized to BHV-3000 (rimegepant) 75 milligram (mg) or placebo. A total of 323 participants failed screening mainly due to failure to meet eligibility criteria.The randomization was stratified in a 1:1 ratio based on use of prophylactic migraine medications (yes or no).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis was performed on modified intent to treat (mITT) participants.

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 analysis was performed on modified intent to treat (mITT) participants, defined as those who were randomized only once, took study medication, had moderate to severe pain level at migraine onset, and who provided at least 1 post-dose efficacy measurement (i.e., after taking study medication).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Freedom From Pain at 2 Hours Post-dose, measured over 2 hours post-dose.

The primary endpoint was the percentage of participants with freedom from pain two hours after dosing. Pain was assessed through an electronic diary using four response levels: none, mild, moderate, and severe. The endpoint counted a participant as pain-free only when the recorded level was none. It is a binary outcome at a specified post-dose time: each participant either met the stated pain-freedom definition or did not.

This endpoint captures a specific, patient-reported state at a defined time, rather than a change in average pain score or the duration of symptoms. It is used to distinguish complete absence of pain from partial improvement. That distinction matters when interpreting the result: the registry record’s separate pain-relief outcome is not interchangeable with pain freedom. A participant may experience pain relief without reaching the endpoint’s stricter definition of no pain.

The percentage is the proportion of participants in the relevant analysis group who met the endpoint definition. The primary analysis was conducted in the modified intent-to-treat population. The registry record does not report the detailed eligibility rules for that population, the handling of missing diary entries, or the exact approach to repeated or unusable assessments. Those details affect how a binary endpoint is operationalized and cannot be inferred from the endpoint description alone.

The two-hour time point provides a common point for comparing groups after the single dose. It does not by itself describe pain status at other times or establish whether a participant’s experience was sustained. Other registered outcomes addressed later or related outcomes, including pain relief and sustained pain freedom, but those are distinct measures.

7. Results Posted in the Registry

• Rimegepant 75 mg: 19.2% (104/543) versus 14.2% (77/541) on control; risk difference 4.9 percentage points (95% CI 0.5 to 9.3), risk ratio 1.35 (1.03–1.76); unadjusted two-proportion z-test p = 0.030.

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 Freedom From Photophobia at 2 Hours Post-dose

• 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:
  • Rimegepant 75 mg: 34.9% (164/470) versus 24.8% (120/483) on control; risk difference 10.0 percentage points (95% CI 4.3 to 15.8), risk ratio 1.40 (1.15–1.71); 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 Rimegepant 75 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Freedom From Phonophobia at 2 Hours Post-dose

• 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:
  • Rimegepant 75 mg: 38.6% (133/345) versus 30.9% (113/366) on control; risk difference 7.7 percentage points (95% CI 0.7 to 14.7), risk ratio 1.25 (1.02–1.53); unadjusted two-proportion z-test p = 0.032.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Rimegepant 75 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Pain Relief at 2 Hours Post-dose

• 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:
  • Rimegepant 75 mg: 56.0% (304/543) versus 45.7% (247/541) on control; risk difference 10.3 percentage points (95% CI 4.4 to 16.2), risk ratio 1.23 (1.09–1.38); 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 Rimegepant 75 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results cover different aspects of the migraine episode, including freedom from photophobia, freedom from phonophobia, and pain relief at two hours. Across the secondary outcomes with numerical results posted, the observed percentages were higher in the rimegepant group than in the placebo group. This broad direction is consistent with the primary result, but each outcome represents a separate endpoint and has its own analysis population and uncertainty.

The registry also lists outcomes involving nausea, rescue medication, and sustained pain freedom or relief. Numerical results for these outcomes are not reported in the registry record in the available outcome details. The registry reports 11 secondary outcomes as posted, but only some have detailed group estimates and comparisons in the record. Absence of a posted estimate should not be interpreted as evidence of no difference.

Secondary outcomes help show whether the primary result sits alongside other measures of symptoms and pain, but they should not be treated as independent confirmations without considering how many outcomes were tested and whether testing was planned hierarchically. When many endpoints are examined, the chance of at least one apparently notable result can rise. In general, multiplicity procedures are used to control or otherwise manage that issue; the registry record does not report whether any such adjustment was used.

The secondary p-values are identified as unadjusted in the recalculated comparisons. They therefore carry less confirmatory weight than a result assessed under a clearly reported multiplicity plan. The secondary estimates can be read as descriptive evidence about the measured outcomes, with their confidence intervals and analysis populations, but they should not be used to claim a broad pattern of established effects across all symptoms. The registry record does not provide enough information to determine how the sponsor planned or interpreted the full family of secondary tests.

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

• Percentage of Participants With Freedom From Photophobia at 2 Hours Post-dose
• Percentage of Participants With Freedom From Phonophobia at 2 Hours Post-dose
• Percentage of Participants With Pain Relief at 2 Hours Post-dose
• Percentage of Participants With Freedom From Nausea at 2 Hours Post-dose
• Percentage of Participants With Rescue Medication Use Within 24 Hours Post-dose
• Percentage of Participants With Sustained Pain Freedom From 2 to 24 Hours Post-dose
• Percentage of Participants With Sustained Pain Relief From 2 to 24 Hours Post-dose
• Percentage of Participants With Sustained Pain Freedom From 2 to 48 Hours Post-dose

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a Cochran-Mantel-Haenszel analysis for the primary risk difference and gives a 95% confidence interval and p-value. The posted recalculation is an unadjusted comparison of the binary event proportions using the summary counts. These methods answer related but not identical statistical questions, so their estimates and uncertainty intervals can differ.

What does a risk difference express?

A risk difference compares the percentage meeting an outcome in one group with the percentage in the other group. For this endpoint, the outcome is pain freedom at two hours. A positive risk difference for rimegepant means the observed percentage meeting that definition was higher in the rimegepant group than in the placebo group. The sponsor-reported risk difference is 4.9 percentage points. This is an absolute contrast, expressed in percentage points, rather than a relative comparison such as a risk ratio.

Absolute contrasts are often useful because they describe how far apart the observed group percentages are on the outcome’s original scale. Relative measures can describe the same data from another perspective, but they are not interchangeable with an absolute difference. The registry’s primary reported analysis is the risk difference; interpretation should keep that scale in view rather than substituting another measure.

What does the Cochran-Mantel-Haenszel method do?

In general, the Cochran-Mantel-Haenszel method can estimate and test an association across strata, combining information while accounting for the stratification used in an analysis. The registry record names this method for the sponsor-reported risk difference. It does not report the stratification factors or enough detail to establish precisely how they were used. Therefore, the method name alone does not justify assumptions about the analysis structure.

The recalculated comparison is described as unadjusted because it uses the posted aggregate group counts without the sponsor’s analysis procedure. An unadjusted calculation is useful as a transparent check on the broad contrast in the observed proportions. It does not replace the prespecified or sponsor-reported analysis, and it may not reproduce adjustments, stratification, or other elements of the trial’s full analysis plan.

How should the p-value be read?

In general, a p-value measures how unusual data at least as incompatible with a null hypothesis as the observed data would be, assuming that null model and the statistical assumptions hold. A smaller p-value indicates greater incompatibility with that null model; it is not the probability that the null hypothesis is true. It also does not measure the size or clinical importance of the group difference. For the primary outcome, the registry reports p = 0.030 for its Cochran-Mantel-Haenszel analysis, while the unadjusted recalculation gives p = 0.03.

A p-value should be read alongside the effect estimate and its confidence interval. The estimate describes the observed contrast, while the interval conveys uncertainty about its magnitude under the method’s assumptions. Neither the p-value nor the confidence interval resolves questions about missing observations, outcome measurement, or unreported analysis choices.

Why can analysis methods produce different estimates?

Different statistical methods may use the same underlying trial but handle the data differently. A stratified analysis can account for grouping factors, while an unadjusted calculation works directly from pooled counts. Differences can also result from definitions of the analysis population or handling of missing outcomes. The registry record does not report enough information to attribute any method-specific variation to a particular factor. Here, the sponsor analysis and recalculation are both available, and the sponsor’s analysis is the registry-reported trial analysis.

Why do these methods not settle every question?

The endpoint is binary, so the analysis reduces each participant’s recorded pain status at the target time to whether the pain-freedom definition was met. That is appropriate to the stated endpoint, but it discards distinctions among the other pain categories. It also does not describe within-person changes over time. The registry lists separate endpoints for pain relief and sustained outcomes, which address different aspects of the clinical course.

For binary outcomes, the observed proportion is only one part of interpretation. The precision of the estimate depends on the amount of information in the analyzed groups and on the event frequency. In general, limited information or sparse events can make estimates less precise. The primary outcome has more observed events than some of the listed serious adverse event categories, so its precision and the safety counts should not be interpreted as equivalent. The registry does not provide a full statistical analysis plan, interim-analysis information, or missing-data methods; those omissions restrict independent evaluation of the assumptions behind the reported inference.

11. Confidence Intervals and Precision

The primary outcome estimates have 95% confidence intervals: 15.8 to 22.5% for rimegepant and 11.3 to 17.2% for placebo. The sponsor-reported risk difference is 4.9 percentage points, with a 95% confidence interval from 0.5 to 9.3. The unadjusted recalculation gives a risk difference of 0.049, with a 95% confidence interval of 0.005 to 0.093. These intervals convey uncertainty in the estimated group results under their respective analysis methods.

In general, a confidence interval is a range generated by a procedure that, under its assumptions and repeated use, would cover the underlying parameter at the stated rate. It is not a range containing a fixed proportion of individual participant outcomes, and it does not mean there is a 95% probability that the fixed parameter lies inside this particular calculated interval. The interval’s width communicates precision: narrower intervals generally indicate more precise estimation, while wider intervals indicate greater uncertainty.

The interval for the sponsor-reported risk difference extends from a small positive contrast to a larger positive contrast. The data are therefore compatible with a range of effect magnitudes, not only the point estimate. Precision should be judged from the interval rather than from the p-value alone. A p-value addresses compatibility with a null model; it does not show how tightly the effect magnitude has been estimated.

The primary outcome confidence intervals are based on the analyzed groups and the reported methods. They do not account for uncertainty from unreported choices such as missing-data handling or undisclosed analysis-plan details. The registry record does not report those details. The difference in analysis method between the sponsor result and the unadjusted recalculation is also relevant: the confidence intervals should be read in the context of the method attached to each estimate.

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 illustrations translate an assumed target effect into the number of participants per arm that would be needed under stated planning assumptions. The primary outcome values correspond to planning for 100%, 75%, and 50% of the observed effect. For example, the primary-outcome illustration lists 901 participants per arm for 80% power when planning for 100% of the observed effect, and 1,206 participants per arm for 90% power under that same effect assumption. These are planning illustrations rather than observed trial results.

The assumptions listed 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. The listed figures are participants per arm, not total participants or total events. The time-to-event tables, if applicable, use total events, but the primary endpoint is not a time-to-event outcome.

The 80% power column describes a planned chance of detecting the assumed effect under the specified statistical model if that effect is real and the planning assumptions hold. The 90% power column describes a higher target chance under the same type of assumptions, which generally requires more participants. Smaller assumed effects need more participants because they are harder to distinguish from random variation.

The registry record does not report the trial’s original sample-size justification or the assumptions used when designing the trial. The illustrations therefore should not be read as a reconstruction of the sponsor’s original design. This is not observed power; it is a forward-looking planning calculation based on the observed effect and stated 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

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 = 0.142; treatment proportion p₁ = 0.192; average p̄ = 0.167.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5274 = 1.0336.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5262 = 0.4429.
4. n = (1.0336 + 0.4429)² / (0.0492)² = 900.7, rounded up to 901 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 <- 0.142329020332717                          # control proportion
p1 <- 0.191528545119705                          # 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(3235479)
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 = 901 (80% power), 1,206 (90% power)
 75% of observed effect: n per arm = 1,555 (80% power), 2,081 (90% power)
 50% of observed effect: n per arm = 3,390 (80% power), 4,538 (90% power)
power.prop.test: 900.7 
Simulated power at n = 901 per arm: 0.802 (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’s primary result is the sponsor-reported Cochran-Mantel-Haenszel analysis. It gives a risk difference of 4.9 percentage points, a 95% confidence interval from 0.5 to 9.3, and p = 0.030. This is the analysis identified in the record as the superiority analysis for the primary endpoint.

The posted recalculation uses an unadjusted comparison of the event counts and gives a risk difference of 0.049, a 95% confidence interval of 0.005 to 0.093, and p = 0.03. It provides a simple check based on the aggregate numbers, but it is not the same procedure as the sponsor’s Cochran-Mantel-Haenszel analysis. The sponsor result should be treated as the trial’s reported analysis; the recalculation is supplemental and should not be substituted for it.

The record does not flag a discrepancy between the reported analysis and the recalculation. Their estimates and uncertainty intervals are similar, but the method distinction remains important. The registry does not state which strata or other analysis details were used for the sponsor result, nor does it provide the full analysis plan. Therefore, the recalculation cannot establish whether every feature of the sponsor’s procedure has been reproduced.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and multiple secondary outcomes. The primary endpoint is pain freedom at two hours; the secondary outcomes address other symptoms, pain relief, rescue medication use, and sustained outcomes. Testing multiple endpoints creates a multiplicity question because each test can produce evidence against its own null hypothesis, and considering many tests together can increase the chance of at least one apparently positive finding.

In general, a prespecified testing hierarchy, adjustment procedure, or other multiplicity strategy can clarify which results are intended to support confirmatory conclusions. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a plan for interpreting the secondary p-values. The posted recalculated secondary comparisons are unadjusted. Their p-values should therefore be read as individual comparisons rather than as evidence that a family-wide error rate was controlled.

The primary analysis population is described as modified intent to treat. The registry record does not provide the exact membership rules for that population, the number excluded from it, or the reasons for exclusion. The primary outcome counts are 543 in the rimegepant group and 541 in the placebo group. Total enrollment is 1485. The record does not explain the relationship between those numbers, so no specific account of exclusions or missing outcomes can be inferred.

The endpoint description says pain was recorded in an electronic diary, but the registry record does not report how missing diary entries were handled, whether any imputation was used, or how participants without an evaluable two-hour assessment were treated. Such choices can affect a binary percentage, particularly if missingness differs between groups or is related to outcome status. The record also does not report sensitivity analyses for missing data.

The record names the Cochran-Mantel-Haenszel method for the sponsor’s primary analysis but does not report the full statistical analysis plan, analysis strata, interim analyses, or other implementation details. These omissions limit independent evaluation of the analysis strategy and the relation between primary and secondary testing. They do not invalidate the posted result, but they constrain how completely its assumptions and confirmatory status can be assessed.

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

Serious events with the highest arm-level rate: acute respiratory failure (0.2%), pulmonary embolism (0.2%), colitis (0.2%).

The registry reports serious adverse events for 2 participants among 546 at risk in the rimegepant group and 1 participant among 549 at risk in the placebo group. Other serious events are reported for 0 participants in each group, and deaths are reported for 0 participants in each group. The serious-adverse-event denominators differ from the primary efficacy analysis counts, so they describe a separate safety population.

The registry lists Acute Respiratory Failure, Pulmonary Embolism, and Colitis among the top serious-event terms, each reported as 0.2%. These terms are event categories in the record; their listing does not establish a causal relationship to treatment. The registry record does not provide enough detail to assess event timing, participant-level overlap, clinical adjudication, or the basis for attributing an event to study treatment.

Serious adverse event counts are sparse. In general, sparse event data yield limited precision for comparing groups, and counts alone do not establish whether risks differ. These figures should be read as the reported events and denominators, not as a comprehensive assessment of all possible safety outcomes or as a basis for treatment advice.

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

The posted primary data show that pain freedom at two hours was reported by 19.2% of participants in the rimegepant group and 14.2% in the placebo group. The sponsor-reported risk difference was 4.9 percentage points, with a 95% confidence interval from 0.5 to 9.3. This describes the group-level contrast for a specific outcome, at a specified time, in the modified intent-to-treat population.

The result does not mean that every participant receiving rimegepant became pain-free, or that every participant receiving placebo remained in pain. The percentages represent proportions, so outcomes varied among participants. Nor does the primary endpoint capture all dimensions of migraine or later status. Pain freedom is distinct from pain relief, freedom from associated symptoms, use of rescue medication, and sustained pain outcomes.

The confidence interval indicates that the estimated group difference has uncertainty. It is compatible with a range of possible magnitudes under the reported analysis, and the point estimate should not be mistaken for an exact or universal effect. The p-value is not the probability that the observed result occurred by chance, nor the probability that the treatment effect is zero. It is a measure tied to a null model and statistical assumptions.

The registry record reports some secondary outcomes and serious adverse event counts, but these do not settle the full balance of outcomes. The secondary comparisons are unadjusted in the recalculations, and the record does not report the multiplicity strategy. The serious-event counts are sparse and do not establish causality. Missing-data handling, the exact modified intent-to-treat definition, and the full statistical analysis plan are not reported in the registry record.

Accordingly, the result is evidence about a defined trial comparison and endpoint, not a guarantee of an individual outcome or a complete account of every potential benefit and harm. It does not establish how results generalize to people or settings beyond those represented by the trial, because the registry record does not provide sufficient detail to assess that question fully. No treatment decision should be based on these statistics alone.

18. Why This Trial Matters Statistically

This trial illustrates why the outcome definition and its time point matter. Pain freedom at two hours is a specific binary endpoint, defined as a pain rating of none on an electronic diary. It is not equivalent to a reduction in pain or a favorable result on another symptom. The separate secondary endpoints make clear that a study can ask several clinically related but statistically distinct questions.

The primary contrast is reported as a risk difference, which expresses an absolute difference between group percentages. Pairing that estimate with its confidence interval gives more information than a p-value alone: the estimate conveys the observed magnitude, while the interval communicates uncertainty about that magnitude. The sponsor’s reported analysis and the simple unadjusted recalculation also illustrate why the statistical method should accompany an estimate. Similar aggregate results do not make different methods interchangeable.

The study also demonstrates the importance of distinguishing enrollment from the analysis population. The registry reports enrollment of 1485, while the primary outcome is analyzed among 543 and 541 participants in the respective groups. The record identifies a modified intent-to-treat analysis but does not explain the population rules or missing-data handling. Those details are essential for assessing how the analyzed group relates to randomization.

Finally, the record includes multiple secondary outcomes and sparse serious adverse event counts. Those results require different interpretive cautions: multiplicity affects the strength of conclusions across endpoints, while sparse safety counts limit precision. The registry record does not report a multiplicity strategy or the complete statistical analysis plan. Reading the effect estimate, uncertainty, analysis population, and reporting limitations together is therefore more informative than focusing on a single significance test.

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 registry record leaves several trial-specific questions unresolved. It identifies a modified intent-to-treat population but does not define its membership or explain how the primary outcome analysis population relates to total enrollment. The primary outcome denominators are smaller than enrollment, but the record does not report the reasons for that difference. Missing-data methods for the electronic diary outcome are also not reported in the registry record, so the influence of unavailable or incomplete assessments cannot be evaluated from the posted details.

The record names a Cochran-Mantel-Haenszel method for the primary sponsor analysis but does not describe the stratification factors, the complete statistical analysis plan, or whether interim analyses were conducted. It also does not report the original sample-size justification. The planning illustrations based on observed effects are not a substitute for the trial’s design rationale.

Multiplicity is another limitation of interpretation. Several secondary endpoints are listed, and the recalculated secondary p-values are unadjusted. The registry record does not report a testing hierarchy or adjustment plan. As a result, the secondary findings should not be treated as if they were all independently confirmatory.

The safety summary reports a small number of serious events and no deaths in either group, but the posted counts alone do not provide detailed event timing, attribution, or participant-level context. The record does not report further information needed to assess those aspects. The primary endpoint is limited to pain status at two hours, and it cannot answer questions about all later or sustained outcomes. Finally, the registry record does not provide enough detail to evaluate how representative the analyzed participants are of populations outside the trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy Study in Adult Subjects With Acute Migraines — NCT03235479.
• Registry record last updated 2023-02-16; status last verified 2023-02.
• Results first posted 2020-12-23.
• 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

The registry record describes a completed, randomized, triple-masked, parallel-group, placebo-controlled phase 3 study of rimegepant for acute migraine. Enrollment was 1485; the sponsor was Pfizer. Participants received a single oral dose of rimegepant 75 mg or matching placebo when migraine reached moderate or severe intensity, up to 45 days after randomization.

The primary endpoint was pain freedom two hours after dosing, analyzed in a modified intent-to-treat population. The reported percentages were 19.2% for rimegepant and 14.2% for placebo. The sponsor-reported risk difference was 4.9 percentage points, with a 95% confidence interval from 0.5 to 9.3 and p = 0.030.

Some secondary outcomes and serious adverse event counts are also posted. The registry record does not report the full analysis plan, missing-data methods, multiplicity strategy, or original sample-size justification. These gaps limit assessment of analysis details and the strength of conclusions across outcomes.