Study to Evaluate Oral Ubrogepant in the Acute Treatment of Migraine During the Prodrome in Adult Participants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate Oral Ubrogepant in the Acute Treatment of Migraine During the Prodrome in Adult Participants (NCT04492020), a randomized phase 3 study. The primary outcome is Percentage of Participants Reporting Absence of Headache of Moderate/Severe Intensity Within 24 Hours Post-dose.

2. Clinical Question

This is a question about an outcome at a specified time after dosing, not about preventing every migraine or eliminating headache of any intensity. The registry also identifies secondary questions concerning absence of moderate or severe headache at 48 hours, ability to function normally over 24 hours, and absence of headache of any intensity at 24 hours. The posted results include three secondary outcomes.

The registry describes a randomized, double-blind crossover study. In this design, the treatment comparison uses observations from treatment periods assigned within the crossover sequences, rather than only a parallel comparison in which participants remain on one assigned treatment. The particular primary question is limited to the recorded endpoint, analysis population, and follow-up interval stated in the registry. The registry record does not report enough detail to infer additional eligibility rules or the exact handling of all participant-level records.

3. Trial Design

This was a Phase 3, multicenter, randomized, double-blind, placebo-controlled crossover study sponsored by AbbVie. The registry lists an enrollment of 518 and a completed status. The listed study start was 2020-08-21, and primary completion was 2022-04-19. The condition was migraine.

The interventions were oral ubrogepant 100 mg and placebo. Participants were assigned to Treatment Sequence A or Treatment Sequence B. Sequence A used placebo for the first qualifying prodrome event and ubrogepant 100 mg for the second; Sequence B used ubrogepant 100 mg for the first event and placebo for the second. Thus, the treatment order differed by randomized sequence, and both interventions were evaluated within the crossover design.

Double blinding means the registry characterizes the study as masked for participants and relevant study personnel, but the record excerpt does not state who specifically was masked or how masking was maintained. The study is described as multicenter, but the number or locations of centers are not reported in the registry record.

The primary outcome was the percentage of participants reporting absence of moderate or severe headache within 24 hours after dosing during prodrome. The primary analysis population was the modified intention-to-treat population, defined by randomization and having at least one qualifying assessment after at least one qualifying prodrome event during the double-blind treatment period. The record gives separate endpoint denominators for the posted outcome results. Those figures should be read in their endpoint context rather than treated as interchangeable counts across outcomes.

The registry does not report the original sample-size justification, the intended number of qualifying events required for every participant, detailed period or sequence model specifications, or any interim analysis plan. Those details cannot be inferred from the crossover description alone.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Modified Intent-to-Treat (mITT) population consists of all randomized participants with at least 1 assessment of headache occurrence within 24 hours after taking double-blind study intervention for at least 1 qualifying prodrome event during the double-blind treatment 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: Safety Population consists of all treated participants who take at least 1 administration of study intervention

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Reporting Absence of Headache of Moderate/Severe Intensity Within 24 Hours Post-dose, measured over 24 hours after taking double-blind study intervention during the prodrome.

The primary endpoint is the percentage of participants reporting no headache of moderate or severe intensity within 24 hours after taking the double-blind study intervention during prodrome. The registry says participants recorded headache status in an electronic diary, and that absence of moderate or severe headache was derived from the headache record and rescue use. The endpoint is therefore a binary participant-level outcome: a participant either met the recorded endpoint definition or did not.

The measure is used to assess whether a qualifying prodrome event is followed by a headache reaching moderate or severe intensity during the stated 24-hour period. It is distinct from complete absence of headache: a participant could fail to meet the primary endpoint by having a moderate or severe headache, while the secondary outcome concerning any-intensity headache applies a more inclusive threshold. It is also distinct from a measure of headache duration, pain score, or functional status.

Using a defined follow-up period makes the comparison interpretable at a specific time after dosing, while recording rescue use as part of the derivation makes that behavior relevant to endpoint classification. The registry does not provide more detail about the exact derivation rules or the treatment of incomplete diary records. Interpretation should therefore remain tied to the endpoint definition and the modified intention-to-treat population stated in the record, rather than extending to unmeasured outcomes or longer-term effects.

7. Results Posted in the Registry

• Ubrogepant 100 mg: 45.5% (190/418) versus 28.6% (121/423) on control; risk difference 16.8 percentage points (95% CI 10.4 to 23.3), risk ratio 1.59 (1.32–1.91); 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 Reporting Absence of Headache of Moderate or Severe Intensity Within 48 Hours Post-dose

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ubrogepant 100 mg: 40.7% (159/391) versus 24.6% (100/407) on control; risk difference 16.1 percentage points (95% CI 9.7 to 22.5), risk ratio 1.66 (1.34–2.04); 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 Ubrogepant 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Reporting Absence of Headache of Any Intensity Within 24 Hours Post-dose

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ubrogepant 100 mg: 23.7% (103/434) versus 13.9% (61/439) on control; risk difference 9.8 percentage points (95% CI 4.7 to 15.0), risk ratio 1.71 (1.28–2.28); 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 Ubrogepant 100 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results have a consistent overall direction: the recalculated comparisons favor a higher frequency of the recorded endpoint in the ubrogepant group across the secondary outcomes that have results posted. These outcomes address related but distinct questions, including the 48-hour status for moderate or severe headache and absence of headache of any intensity within 24 hours. Their pattern is broadly aligned with the primary result, but they do not measure precisely the same event or follow-up interval.

The registry lists a secondary outcome on improvement in the ability to function normally over 24 hours, but the posted secondary results include three outcomes, and no result for that functioning endpoint is included in the registry record. It should not be assumed to have the same result as the other secondary outcomes. Reasons for its absence from the posted results are not reported in the registry record.

Secondary findings generally carry less inferential weight when multiple outcomes are assessed and no multiplicity strategy is reported. Testing several outcomes can increase the chance of apparently strong results arising by chance, especially if outcomes are selected for emphasis after results are known. The registry record does not report the hierarchy among secondary outcomes or whether p-values were adjusted. Their unadjusted p-values should therefore be read as outcome-specific summaries, not as confirmatory evidence equivalent to a prespecified primary analysis protected by a stated multiplicity procedure.

There are also endpoint-specific denominators, so the results need not use exactly the same analytic records. Differences in event definition, follow-up window, and available assessments can affect each estimate. The overall consistency is descriptive; it does not establish that the outcomes are statistically independent or that every secondary question was answered.

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

• Percentage of Participants Reporting Absence of Headache of Moderate or Severe Intensity Within 48 Hours Post-dose
• Percentage of Participants Reporting Improvement in the Ability to Function Normally Over 24 Hours Post-dose
• Percentage of Participants Reporting Absence of Headache of Any Intensity Within 24 Hours Post-dose

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary, so a basic unadjusted comparison can describe the proportion meeting the endpoint in each treatment group and the difference between those proportions. The recalculated risk difference is an absolute contrast: it expresses how far apart the observed endpoint proportions are on the probability scale. Its confidence interval gives a range of values compatible with the data under the calculation’s assumptions. This summary is straightforward to interpret, but it does not by itself represent the full crossover model specified by the study’s analysis.

Why use a mixed model?

The sponsor reports a generalized linear mixed model (GLMM) and presents an odds ratio. Generalized linear models are used for outcomes such as binary responses by relating the probability of an event to explanatory terms through a link function. A mixed model can include both fixed-effect terms and random-effect terms. In general, random effects can represent grouping or repeated observations, and can account for dependence among observations that would not be appropriate to treat as wholly unrelated. That general property is relevant to understanding why a model-based analysis may differ from a simple arm-level recalculation in a crossover study.

The registry identifies the method as a GLMM but does not report its full specification. The exact link function, covariates, random effects, treatment-period terms, sequence terms, and any other model choices are not reported in the registry record. It would be inappropriate to infer those choices from the name of the method alone. The reported odds ratio is therefore best described as the sponsor’s model-based estimate, without attributing unreported model details to it.

Risk difference and odds ratio

A risk difference compares probabilities by subtraction, whereas an odds ratio compares odds. Odds are a transformation of probability, so the two measures are not interchangeable. An odds ratio greater than one indicates higher odds of the event in the named treatment group relative to the comparator when the event is defined as the outcome being modeled. It does not directly state the change in probability. In this study, the event is the reported absence of moderate or severe headache, so the direction needs to be read with that outcome definition in mind.

The recalculated risk difference uses posted counts without adjustment for the crossover structure. The model-based odds ratio uses the sponsor’s stated GLMM approach. Differences between their numerical values are expected because the scales and analysis methods differ; they are not a reason to convert one estimate into the other or to treat them as duplicate measures. The registry does not flag a discrepancy between the posted recalculation and sponsor analysis.

What a p-value says

A p-value describes how compatible the observed data are with a specified null model, under 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 p-value for the recalculated primary comparison is <0.001, while the sponsor’s model-based p-value is <.0001. These are reported with different precision formats and correspond to different analyses.

Unadjusted p-values for secondary outcomes do not account for the fact that several questions are assessed. When many outcomes are tested, the chance of finding at least one small p-value by chance can increase. A prespecified multiplicity procedure can address that issue, but the procedure is not reported in the registry record. Thus, secondary p-values should be interpreted with less weight than a primary result when adjustment and outcome hierarchy are not established in the record.

How the crossover structure matters

In a crossover study, treatment is assigned in sequences and participants can contribute observations under both interventions. In general, observations from the same participant can be correlated, and the order or period of treatment may matter. Analysis methods may account for this dependence and the design’s structure. The simple unadjusted comparison based on posted group counts does not model participant-level pairing or period effects. The sponsor’s mixed model is the reported model-based analysis, but the registry does not provide enough detail to determine exactly how it handled each design feature.

The primary modified intention-to-treat definition also matters: eligibility for that analysis depended on having at least one assessment after at least one qualifying prodrome event. Endpoint denominators can differ across outcomes, as shown by the posted results. Such variation means an outcome-specific count should be interpreted for that outcome and not assumed to identify a fixed set of observations used everywhere. The record does not state the full reasons for those denominator differences.

All statistical methods rely on assumptions. General considerations for binary comparisons include how observations are classified, whether the chosen model is appropriate, and how incomplete data are handled. For repeated or crossover observations, dependence and period structure may also be relevant. The registry record does not report enough detail to assess all these assumptions independently. Accordingly, the unadjusted summaries are useful descriptive recalculations, while the sponsor’s reported model result remains the stated analysis for the trial’s primary comparison.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.169, with a 95% confidence interval from 0.104 to 0.233. This interval expresses uncertainty about the unadjusted difference on the probability scale. Its lower and upper limits are both above zero, so the interval is compatible with a positive difference under this calculation. The interval is not a guarantee that the true value lies within those limits, and it does not describe the range of individual participant outcomes.

The sponsor’s GLMM estimate is an odds ratio of 2.09, with a 95% confidence interval from 1.63 to 2.69. This interval is on the odds-ratio scale, not the risk-difference scale. It should be interpreted alongside the sponsor’s model and endpoint definition, not substituted directly for the unadjusted risk-difference interval. The registry does not provide the full model specification needed to independently evaluate all sources of uncertainty in that estimate.

Confidence intervals are useful because they show both the direction and precision of an estimate, rather than reducing the result to a significance label. A narrower interval indicates greater statistical precision under the method used; a wider interval indicates greater uncertainty. Precision does not establish clinical importance, eliminate bias, or resolve uncertainty about unreported analysis choices. The posted primary interval is informative for the recalculated comparison, but it does not capture all potential uncertainties associated with endpoint measurement, missing records, multiplicity, or the crossover analysis.

The secondary recalculated intervals are also positive, but each pertains to its own outcome and denominator. They should not be compared as though they estimate one common endpoint. In particular, the primary outcome concerns moderate or severe headache within 24 hours, while secondary outcomes use a different time point or headache threshold. The sponsor’s model-based confidence intervals are separately reported for the primary and posted secondary outcomes. Interpretation should preserve those distinctions.

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 express the requested enrollment as participants per arm, not total events. They are based on an assumed two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These are planning assumptions for the illustration; the registry record does not report the trial’s own original design assumptions.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the assumed effect under those assumptions, if that effect and analysis framework applied. The 90% power column gives the corresponding participants per arm for a 90% chance. These are design-planning quantities, not probabilities that the completed study’s result is correct or evidence that the study had a particular probability of success.

The displayed scenarios scale the observed effect to 100%, 75%, or 50%. As the assumed effect becomes smaller, more participants are needed to distinguish it from no difference at the stated power and significance level. The planning values therefore should be read as illustrations of how sample-size requirements change with effect size, not as observed participant counts or a reconstruction of the study’s planning process. This is not observed power.

The curve represents the same planning relationship across effect assumptions: smaller target effects generally require a larger sample for a fixed power target. The registry does not report whether the original trial used these assumptions, whether it planned for an effect of this size, or whether its crossover structure was included in the original sample-size calculation. Those matters are not reported in the registry record.

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 = 0.286; treatment proportion p₁ = 0.455; average p̄ = 0.370.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6829 = 1.3385.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6724 = 0.5659.
4. n = (1.3385 + 0.5659)² / (0.1685)² = 127.7, rounded up to 128 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 <- 0.286052009456265                          # control proportion
p1 <- 0.454545454545455                          # 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(4492020)
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 = 128 (80% power), 171 (90% power)
 75% of observed effect: n per arm = 223 (80% power), 297 (90% power)
 50% of observed effect: n per arm = 487 (80% power), 651 (90% power)
power.prop.test: 127.7 
Simulated power at n = 128 per arm: 0.799 (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’s primary analysis is a generalized linear mixed model reporting an odds ratio of 2.09, with a 95% confidence interval from 1.63 to 2.69 and p <.0001. This is the model-based result reported in the registry. The recalculated comparison uses the posted arm counts and reports an unadjusted risk difference of 0.169, with a 95% confidence interval from 0.104 to 0.233 and p <0.001.

The estimates are not competing values for the same scale: one is an odds ratio from a mixed model and the other is an unadjusted difference in observed proportions. Their intervals and p-values likewise arise from different analyses. Both describe a higher frequency of the defined primary endpoint in the ubrogepant group, but the recalculation should not be presented as a replacement for the sponsor’s model.

The registry record does not flag a discrepancy. The complete GLMM specification is not reported in the registry record, so the precise model terms and assumptions cannot be independently reconstructed from the posted summary. The sponsor’s result should therefore be identified as the reported model analysis, while the recalculation is useful as a transparent, unadjusted summary of the posted counts.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and lists secondary outcomes, but the multiplicity procedure is not reported in the registry record. In general, multiplicity arises when several hypotheses are tested: without an adjustment or prespecified testing hierarchy, interpreting each p-value as if it were the only test can overstate the strength of the total evidence. The posted unadjusted secondary results should consequently be treated as supportive descriptions rather than automatically as independent confirmatory findings.

The number of analyses reported in the record is four, while the listed secondary results include three outcomes in addition to the primary outcome. The record does not explain whether these represent all planned analyses, whether an outcome was not reported, or whether other analyses were performed. It does not report a complete statistical analysis plan or a prespecified ordering for interpreting primary and secondary outcomes.

The primary analysis population is defined as randomized participants with at least one assessment of headache occurrence within 24 hours after taking the intervention for at least one qualifying prodrome event during the double-blind treatment period. This definition provides an important boundary for interpreting the primary result. The registry does not report a detailed missing-data method, the extent or reasons for missing assessments, or sensitivity analyses for missingness. Therefore, the effect of incomplete diary records on the posted estimates cannot be assessed from the registry record.

Endpoint denominators differ across the posted results. The record does not give enough information to determine all reasons for those differences or how observations outside each outcome’s denominator were handled. The outcome counts should be interpreted as specific to the endpoint in question, not as a complete account of follow-up or missingness.

Although this is a crossover trial, detailed methods for period effects, sequence effects, within-participant correlation, or treatment carryover are not reported in the registry record. This is not evidence that such issues were ignored; it means the available record does not describe how they were addressed. The sponsor’s GLMM result is reported, but its full specification is also absent. These reporting gaps limit independent assessment of model assumptions and the robustness of the analysis.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: rhabdomyolysis (0.2%).

The registry reports serious adverse event counts among 462 participants at risk in the placebo group and 456 at risk in the ubrogepant 100 mg group. One serious adverse event was reported in the placebo group and zero in the ubrogepant group. Deaths were reported as zero in each group. These are counts for the stated at-risk groups and should not be confused with the efficacy endpoint denominators.

The record identifies rhabdomyolysis at 0.2% among the top serious adverse event terms. That listed term is a registry safety summary; the record excerpt does not provide its group-specific allocation or additional clinical details. No causal conclusion can be made from these counts alone.

Other adverse events were reported in 35 of 462 participants at risk in the placebo group and 50 of 456 at risk in the ubrogepant group. The registry distinguishes these other events from serious adverse events. Counts do not by themselves establish whether events were related to treatment, how severe they were, or whether exposure time differed. The record does not provide enough detail to assess those questions, nor do these figures support an individual medical recommendation.

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

The posted results show that the recorded primary endpoint—absence of moderate or severe headache within 24 hours after dosing during prodrome—occurred more often in the ubrogepant 100 mg group than in the placebo group in the reported counts. The unadjusted risk-difference interval is above zero, and the sponsor’s reported mixed-model odds ratio is also above one. These are statistical descriptions of the registry’s primary comparison under the stated endpoint and analysis population.

The result does not mean every participant avoided headache, and it does not address every aspect of migraine experience. The primary endpoint is not absence of headache of any intensity, long-term prevention, symptom duration, or functioning. The registry lists related secondary questions, but the posted results do not include the functioning outcome. Results for one defined endpoint should not be generalized automatically to these other outcomes.

The crossover design, outcome definitions, endpoint-specific denominators, and analysis methods all shape what the estimates mean. The unadjusted recalculation is not equivalent to the sponsor’s GLMM analysis. Details of the model specification, missing-data handling, multiplicity procedure, and original design assumptions are not reported in the registry record, which limits assessment of how those choices might affect interpretation.

Statistical evidence is not the same as clinical importance. The estimates and intervals quantify comparisons under particular methods; they do not establish how participants value the outcome or whether the difference is meaningful for an individual. Nor do the reported counts by themselves establish safety for every person or settle questions beyond the outcomes measured in the trial. The record should be read as evidence about the specified trial comparison, not as medical advice or a universal prediction.

18. Why This Trial Matters Statistically

This trial is statistically notable as a randomized, double-blind crossover comparison of treatment given during migraine prodrome. The sequence design means that treatment order is part of the study structure, and the same participant could be evaluated under both interventions. This makes the analysis method important: an arm-level recalculation provides an accessible summary, while a model-based analysis can address repeated or grouped observations if the model is specified appropriately.

The primary result illustrates why reporting both an absolute measure and a model-based relative measure can be helpful. The recalculated risk difference describes separation in the observed endpoint proportions, while the sponsor’s odds ratio comes from a generalized linear mixed model. They provide different views and should not be collapsed into one number. The confidence intervals also make uncertainty visible instead of relying only on p-values.

The registry’s clear endpoint definition and modified intention-to-treat population allow readers to identify what the primary result concerns. At the same time, incomplete reporting of the model specification, missing-data methods, and multiplicity strategy limits independent scrutiny of the analysis. This is a general lesson in interpreting clinical trial records: a numerical estimate is most useful when its population, outcome, time window, and analysis method are all understood.

The secondary outcomes add context because they address related thresholds and follow-up periods, but their unadjusted status matters. The planning illustrations also show how sample-size needs depend on the assumed effect size, while not revealing the trial’s original planning rationale. Keeping observed results, model-based inference, and planning scenarios distinct prevents overinterpretation.

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.

Several trial-specific reporting limitations affect interpretation. The registry gives the sponsor’s GLMM method and odds ratio but not the full model specification. The exact fixed and random effects, handling of treatment period and sequence, and other modeling choices are not reported in the registry record. That makes it difficult to reproduce or fully audit the sponsor’s model-based estimate from the posted summary alone.

The registry defines the modified intention-to-treat population, but does not report a complete account of missing diary assessments, reasons for endpoint-specific denominator differences, or methods used to handle missing data. It also does not report sensitivity analyses that would show how assumptions about incomplete records might affect the results.

The record lists secondary outcomes but does not report a multiplicity adjustment or confirmatory hierarchy. It includes three posted secondary results, while the listed functioning outcome does not have a posted result in the record described. The reason for that gap is not reported in the registry record. Secondary conclusions therefore require caution.

The original sample-size justification, trial-specific planning assumptions, and interim analysis plan are not reported. The planning illustrations use the observed effect under stated assumptions and should not be taken as a record of the study’s original design process. Further, the arm-level recalculations are unadjusted and do not reproduce the crossover model. These limitations do not negate the posted findings, but they define what can and cannot be independently concluded from the registry summary.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate Oral Ubrogepant in the Acute Treatment of Migraine During the Prodrome in Adult Participants — NCT04492020.
• Registry record last updated 2023-05-31; status last verified 2023-05.
• Results first posted 2023-05-31.
• 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 Phase 3, multicenter, randomized, double-blind, placebo-controlled crossover study sponsored by AbbVie, with an enrollment of 518. It evaluated oral ubrogepant 100 mg and placebo during qualifying migraine prodrome events, assigned in opposite treatment sequences.

The primary outcome was absence of moderate or severe headache within 24 hours after dosing, assessed in a modified intention-to-treat population. The posted counts and unadjusted recalculation favor a higher frequency of that endpoint under ubrogepant; the sponsor also reports a GLMM odds ratio above one. Three secondary outcomes have posted results, with a generally similar direction, while the registry lists one further secondary outcome without a posted result.

The registry reports serious adverse event counts and deaths by group. It does not report the full model specification, detailed missing-data handling, multiplicity procedure, original sample-size rationale, or interim analysis plan. Those gaps limit independent assessment of the analysis beyond the posted summaries.