Efficacy, Safety, and Tolerability Study of Oral Ubrogepant in the Acute Treatment of Migraine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Safety, and Tolerability Study of Oral Ubrogepant in the Acute Treatment of Migraine (NCT02828020), a randomized phase 3 study. The primary outcome is Percentage of Participants With Pain Freedom at 2 Hours After Initial Dose.

2. Clinical Question

3. Trial Design

This was a Phase 3, multicenter, randomized, double-blind, parallel-group, placebo-controlled study of oral ubrogepant for the acute treatment of one migraine attack. The registry lists enrollment as 1672 and the status as completed. The recorded study start was 2016-07-22, and the primary completion date was 2017-12-13. The sponsor was Allergan.

Participants were assigned to placebo, ubrogepant 50 mg, or ubrogepant 100 mg. The 50 mg group received one 50 mg ubrogepant tablet and one matching placebo tablet for initial treatment; the 100 mg group received two 50 mg ubrogepant tablets. The placebo group received two matching placebo tablets. These descriptions indicate that the initial treatment was oral and tied to a qualifying migraine attack. Each arm description also includes the option of a second dose or rescue medication 2 to 48 hours after initial treatment.

Randomization supports comparisons between assigned groups by reducing systematic differences at baseline, while double blinding is intended to limit influences of treatment knowledge on participants and study conduct. Those are general design principles; the registry record does not report the specific randomization procedure, how the blind was maintained, or any allocation ratio. It also does not report the original sample-size justification or the detailed protocol for use of rescue medication.

The posted primary endpoint focuses on pain freedom at two hours after the initial dose. The registry also lists secondary outcomes covering pain relief, sustained pain relief and freedom, and migraine-associated symptoms at two hours. The analyzed numbers vary by outcome, consistent with endpoint-specific available assessments; reasons for missing assessments are not reported in the registry record.

4. Participant Flow and Accounting

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

Treatment Period

Reasons for not completing this period:

Safety Follow-up Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intent-to-Treat (mITT) population included all randomized participants who received at least 1 dose of study drug, recorded a baseline migraine headache severity measurement, and had ≥ 1 postdose migraine headache severity or migraine-associated symptom measurement at or before the 2-hour timepoint, last observation carried forward (LOCF).

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: Intent-to-Treat (ITT) population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Pain Freedom at 2 Hours After Initial Dose, measured over Baseline (Predose) to 2 hours after initial dose.

The primary endpoint is the percentage of participants with pain freedom two hours after the initial dose. It measures whether headache severity changed from moderate or severe before treatment to no pain at the two-hour assessment. Participants recorded headache severity in an electronic diary using a scale ranging from no pain to severe pain. The endpoint description defines the analyzed number as participants with a non-missing postdose pain-severity assessment at or before two hours.

This is a binary outcome: each participant either meets the stated pain-freedom definition at the assessment or does not. Reporting the percentage makes the outcome interpretable as the observed frequency of this defined response in each group. Comparing those percentages between randomized groups describes how frequently the endpoint was recorded under each assignment. The measure does not describe the magnitude of improvement among participants who still reported pain, nor does it capture symptom experience beyond the specified assessment time.

A two-hour endpoint is used in this trial as an early assessment after acute treatment. The registry record identifies that timeframe but does not report the rationale for selecting it or any additional timing rules beyond the assessment description. The endpoint is specific to the initial dose; later options for another dose or rescue medication are part of the arm descriptions, but the primary measure is not a summary of all subsequent treatment or the entire course of a migraine attack.

The outcome is an observed trial measure, not a guarantee about an individual’s response. Its interpretation depends on the stated definition, the participants included in the analysis, and the completeness and timing of diary assessments.

7. Results Posted in the Registry

• Ubrogepant 50 mg: 19.2% (81/422) versus 11.8% (54/456) on control; risk difference 7.4 percentage points (95% CI 2.6 to 12.1), risk ratio 1.62 (1.18–2.23); unadjusted two-proportion z-test p = 0.003.
• Ubrogepant 100 mg: 21.2% (95/448) versus 11.8% (54/456) on control; risk difference 9.4 percentage points (95% CI 4.6 to 14.2), risk ratio 1.79 (1.32–2.44); 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 Relief at 2 Hours After the Initial 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:
  • Ubrogepant 50 mg: 60.7% (256/422) versus 49.1% (224/456) on control; risk difference 11.5 percentage points (95% CI 5.0 to 18.1), risk ratio 1.23 (1.09–1.39); unadjusted two-proportion z-test p = <0.001.
  • Ubrogepant 100 mg: 61.4% (275/448) versus 49.1% (224/456) on control; risk difference 12.3 percentage points (95% CI 5.8 to 18.7), risk ratio 1.25 (1.11–1.41); 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 50 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • 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 With Sustained Pain Relief From 2 to 24 Hours After Initial 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:
  • Ubrogepant 50 mg: 36.3% (150/413) versus 20.8% (93/447) on control; risk difference 15.5 percentage points (95% CI 9.5 to 21.5), risk ratio 1.75 (1.40–2.18); unadjusted two-proportion z-test p = <0.001.
  • Ubrogepant 100 mg: 38.0% (165/434) versus 20.8% (93/447) on control; risk difference 17.2 percentage points (95% CI 11.3 to 23.1), risk ratio 1.83 (1.47–2.27); 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 50 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • 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 With Sustained Pain Freedom From 2 to 24 Hours After Initial 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:
  • Ubrogepant 50 mg: 12.7% (53/418) versus 8.6% (39/452) on control; risk difference 4.1 percentage points (95% CI -0.1 to 8.2), risk ratio 1.47 (0.99–2.17); unadjusted two-proportion z-test p = 0.052.
  • Ubrogepant 100 mg: 15.4% (68/441) versus 8.6% (39/452) on control; risk difference 6.8 percentage points (95% CI 2.5 to 11.0), risk ratio 1.79 (1.23–2.59); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ubrogepant 50 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • 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 secondary outcomes cover several related aspects of a migraine attack: pain relief at two hours, sustained pain relief and sustained pain freedom between 2 and 24 hours, and absence of photophobia, phonophobia, or nausea at two hours. Taken together, the posted arm percentages generally show higher recorded response or symptom-absence percentages in the ubrogepant groups than in the placebo group. This broad pattern is directionally consistent with the primary outcome, but the secondary measures capture different experiences and time windows.

Secondary outcomes provide context about features beyond the primary definition of pain freedom. Pain relief is not the same endpoint as complete pain freedom, and sustained outcomes require a response maintained across a later interval. Symptom-absence outcomes concern migraine-associated symptoms rather than headache severity alone. Their relationship to the primary result is therefore one of related but distinct evidence, not repeated measurement of exactly the same outcome.

Unadjusted secondary results carry less weight as confirmatory evidence when the registry record does not report a multiplicity procedure. In general, the more outcomes and comparisons examined, the greater the chance that some results may appear notable through chance variation. The record lists six posted secondary outcomes, but does not report whether they were tested in a prespecified hierarchy or adjusted as a family. The sponsor’s reported analyses and any prespecified multiplicity strategy, if available, would be needed to assess formal confirmatory status.

These outcomes also have endpoint-specific analyzed numbers and different event frequencies, so their precision is not uniform. They should not be combined into a single overall measure without a prespecified method. The registry record does not report such a combined analysis. Their most defensible role is to describe the range of outcomes recorded in the trial and to show whether the overall pattern aligns with, or is less clear than, the primary comparison.

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

• Percentage of Participants With Pain Relief at 2 Hours After the Initial Dose
• Percentage of Participants With Sustained Pain Relief From 2 to 24 Hours After Initial Dose
• Percentage of Participants With Sustained Pain Freedom From 2 to 24 Hours After Initial Dose
• Percentage of Participants With the Absence of Photophobia at 2 Hours After the Initial Dose
• Percentage of Participants With the Absence of Phonophobia at 2 Hours After the Initial Dose
• Percentage of Participants With Absence of Nausea at 2 Hours After the Initial Dose

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary percentage represent?

The primary outcome is binary: participants either met the defined pain-freedom criterion at the two-hour assessment or did not. The posted percentages are the observed proportions in each arm. For example, the registry lists 11.8% for placebo, 19.2% for ubrogepant 50 mg, and 21.2% for ubrogepant 100 mg. These percentages describe the analyzed groups, not all randomized participants regardless of endpoint availability.

In general, a binary outcome can be compared using several measures. A risk difference describes the difference between the two proportions, while a risk ratio compares them as a ratio. An odds ratio compares the odds of the outcome in one group with the odds in another. These measures answer related but distinct questions and have different scales. They should not be treated as interchangeable. The sponsor’s posted primary analysis reports odds ratios from logistic regression; the simple recalculation reports unadjusted risk differences from the posted summary counts.

What does logistic regression contribute?

In general, logistic regression models the probability of a binary outcome through its odds. The registry identifies logistic regression as the method for the sponsor’s reported primary analyses. It reports an odds ratio of 1.83 for 50 mg versus placebo and 2.04 for 100 mg versus placebo. The registry record does not report which covariates, if any, were included in those models, or the model specification beyond the method and odds-ratio result. It is therefore not possible to characterize the posted estimates as adjusted for particular baseline factors.

The recalculated risk differences use the posted summary counts and are unadjusted. They are descriptive comparisons and are not replacements for the sponsor’s own model-based analysis. Because a discrepancy is flagged, the sponsor’s own analysis takes precedence. Differences between analytic approaches can arise because they estimate different measures or use different modeling details; the record does not provide enough detail to identify the specific source of the discrepancy.

How should a p-value be read?

In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it quantify the size or clinical importance of a difference. The sponsor reports p = 0.002 for the 50 mg primary comparison and p < 0.001 for the 100 mg primary comparison. The simple unadjusted recalculations report p = 0.003 and p < 0.001, respectively. The recalculated values should be understood as distinct from the sponsor’s logistic-regression results.

In general, a confidence interval gives a range of estimates compatible with the data and analysis method at the stated confidence level. It conveys uncertainty about the estimate, not a range containing a guaranteed proportion of individual outcomes. The sponsor reports 95% confidence intervals for odds ratios; the recalculations report intervals for risk differences. Their endpoints are on different scales, so numerical comparisons between the two kinds of interval are not meaningful without accounting for the measure.

Why do analysis populations matter?

The primary endpoint description identifies a modified intent-to-treat population: randomized participants who received at least one dose, recorded a baseline headache-severity measurement, and had at least one postdose headache-severity or migraine-associated symptom measurement at or before the two-hour time. The endpoint-specific analyzed number is described as participants with a non-missing postdose pain-severity assessment at or before two hours. These rules mean the primary analysis is not simply a count of everyone enrolled. The registry record does not report a full account of exclusions, missing outcome handling, or sensitivity analyses.

The posted denominators for the primary outcome are 456 for placebo, 422 for ubrogepant 50 mg, and 448 for ubrogepant 100 mg. Other outcomes have their own analyzed denominators. In general, endpoint-specific denominators can differ because participants may lack a particular assessment or fail an outcome-specific analysis criterion. The reasons for the differences are not reported in the registry record, so their causes should not be inferred from the counts alone.

What does randomization support?

In general, random assignment supports comparison of groups by helping balance participant characteristics across treatment assignments, including characteristics not measured in the trial. The study is described as randomized, double-blind, and parallel-group. Those design features support interpretation of the comparisons as between assigned groups, subject to the analysis population, missing data, adherence, and other trial conduct. The registry record does not report the randomization method, concealment procedure, or detailed blinding procedures.

Randomization does not make every statistical uncertainty disappear. Estimates remain subject to sampling variation, captured in part by confidence intervals. The outcomes are also specific to the trial’s population, treatment setting, endpoint definitions, and timeframes. The record does not provide details sufficient to extend the findings to other populations, repeated attacks, or different treatment schedules.

Why do multiple outcomes require care?

The registry lists eight outcome measures and 16 analyses, including the primary measure and posted secondary outcomes. In general, testing multiple outcomes or comparisons increases the opportunity for at least one apparently unusual result to occur by chance if each is interpreted separately. A prespecified multiplicity procedure can address that issue, but the registry record does not report whether one was planned or used. The sponsor’s reported analyses label comparisons as superiority; that label alone does not establish how multiplicity was handled.

The secondary comparisons and their recalculated p-values are therefore best read as supporting descriptive evidence, with the sponsor’s analyses and any prespecified adjustment taking priority if reported. The record does not report a complete statistical analysis plan, interim-analysis plan, or details of outcome hierarchy beyond identifying the primary outcome and listing secondary outcomes. General statistical principles explain why these details matter, but they cannot fill in what the registry record leaves unreported.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated group difference. A confidence interval expresses a range of values compatible with the observed data under the chosen method. A narrower interval indicates greater precision than a wider interval on the same scale, while an interval that includes the null value may leave greater uncertainty about the direction of the difference. This general interpretation does not make the interval a guarantee about the true value or about individual outcomes.

For the sponsor’s primary logistic-regression analysis, the 50 mg comparison has an odds ratio of 1.83 with a 95% confidence interval from 1.25 to 2.66. The 100 mg comparison has an odds ratio of 2.04 with a 95% confidence interval from 1.41 to 2.95. Both reported intervals lie above an odds ratio of 1, the null value for that measure. The sponsor’s p-values are 0.002 and < 0.001, respectively. These are the sponsor’s model-based estimates and intervals.

The unadjusted recalculated risk differences are 0.073, with a 95% confidence interval from 0.026 to 0.121, for 50 mg versus placebo, and 0.094, with a 95% confidence interval from 0.046 to 0.142, for 100 mg versus placebo. These intervals are on the risk-difference scale, not the odds-ratio scale. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence.

Confidence intervals for secondary outcomes vary in width. For example, the recalculated interval for sustained pain freedom with 50 mg versus placebo extends from -0.001 to 0.082, while the interval for 100 mg extends from 0.025 to 0.110. Such variation reflects outcome frequencies and analyzed sample sizes as well as the method used. The sponsor reports its own intervals for those outcomes, which should be kept distinct from the simple recalculations.

The registry record does not report a clinical threshold for interpreting the size of these estimates. Statistical precision alone cannot determine whether a difference is important to participants.

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 figures are planning illustrations based on the observed effect, not the trial’s original design justification. For these non-time-to-event outcomes, each figure is the number of participants per arm, not a total across arms. The assumptions listed are a 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. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the modeled participants per arm for a planning scenario with an 80% chance of detecting the stated effect under those assumptions, if that effect is present. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are conditional planning calculations, not guarantees that a future study will reach a particular result. The 50 mg primary comparison, for example, lists 380 participants per arm for 80% power and 508 participants per arm for 90% power when planning for 100% of the observed effect. For the 100 mg comparison under that same effect assumption, the listed figures are 246 and 329 participants per arm.

Rows that plan for 75% or 50% of the observed effect assume a smaller target difference than the full observed effect. Smaller effects are harder to distinguish from random variation, so the planning figures require more participants per arm. The displayed curve should be read in the same spirit: it illustrates how the assumed effect size and planned sample size relate under the stated calculation assumptions, not what was established by the completed trial. These figures are not observed power.

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 = 0.118; treatment proportion p₁ = 0.192; average p̄ = 0.155.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5121 = 1.0036.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5094 = 0.4287.
4. n = (1.0036 + 0.4287)² / (0.0735)² = 379.5, rounded up to 380 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 <- 0.118421052631579                          # control proportion
p1 <- 0.191943127962085                          # 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(2828020)
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 = 380 (80% power), 508 (90% power)
 75% of observed effect: n per arm = 643 (80% power), 860 (90% power)
 50% of observed effect: n per arm = 1,371 (80% power), 1,835 (90% power)
power.prop.test: 379.5 
Simulated power at n = 380 per arm: 0.807 (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 reported primary analyses are logistic-regression comparisons of each ubrogepant dose with placebo. The sponsor reports odds ratios of 1.83 for 50 mg and 2.04 for 100 mg, with 95% confidence intervals of 1.25 to 2.66 and 1.41 to 2.95, respectively. The reported p-values are 0.002 and < 0.001. These are the sponsor’s own model-based results.

The simple recalculations use the posted event counts and denominators to estimate unadjusted risk differences. They produce different estimates and p-values from the sponsor’s analysis, in part because the recalculated measure is a risk difference rather than an odds ratio. The record explicitly flags a discrepancy. The sponsor’s own analysis takes precedence for the trial’s reported inferential result; the recalculations serve as a separate descriptive check and should not be substituted for the registry’s reported analysis.

The registry record does not report enough detail to identify the exact reason for the discrepancy. It does not specify model covariates or all analysis procedures, and the recalculations are deliberately unadjusted. Readers should therefore keep the analyses separate: use the sponsor’s logistic-regression result as the primary reported inference, and treat recalculated risk differences as unadjusted estimates derived from the posted summaries. Neither set of figures changes the other measure’s meaning.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary outcome and lists secondary outcomes, but does not report a complete statistical analysis plan or a multiplicity adjustment strategy. It also does not report whether there was a prespecified hierarchy among secondary endpoints, whether some comparisons were exploratory, or how the overall type I error rate was managed. Without those details, the posted p-values for multiple outcomes should not all be interpreted as if each were a single, isolated confirmatory test.

In general, multiplicity arises when several hypotheses are tested. Even if each test uses the same nominal threshold, the chance of at least one false-positive result across the family can increase. Methods such as a hierarchical testing sequence or an adjustment across tests can address this, but the registry record does not say whether such methods were used. No adjustment should be assumed from the presence of sponsor-reported p-values or a superiority label.

The primary endpoint description identifies a modified intent-to-treat population. It includes randomized participants who received at least one dose, recorded baseline headache severity, and had at least one postdose headache-severity or migraine-associated symptom measurement at or before the two-hour time. It further defines the analyzed number for pain freedom using participants with a non-missing postdose pain-severity assessment at or before two hours. This clarifies the population basis of the endpoint but does not fully explain all exclusions or missing-data handling.

The registry record does not report how missing primary or secondary assessments were treated, whether imputation was used, or whether sensitivity analyses assessed alternative assumptions. It does not report a detailed accounting of missing outcomes by reason. Those omissions matter because observed percentages depend on who contributes an assessable outcome and on the assumptions used for unobserved outcomes.

The record also does not report interim analyses, stopping rules, or whether any changes were made to outcome definitions or analysis procedures. Their absence from the registry record should not be interpreted as proof that none occurred. These reporting gaps limit independent assessment of the full inferential strategy, particularly for secondary outcomes and missing data.

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: appendicitis (0.2%), abortion spontaneous (0.2%), pericardial effusion (0.2%), seizure (0.2%).

The registry reports serious adverse event counts and the number at risk for each arm. For placebo, 0 serious adverse events were reported among 485 at risk. For ubrogepant 50 mg, 3 were reported among 466 at risk; for ubrogepant 100 mg, 2 were reported among 485 at risk. The registry also reports 0 other adverse events in each group and 0 deaths in each group.

These are counts from the registry record, not estimates of comparative risk from a formal safety analysis. The groups at risk for the adverse-event summaries differ from the analyzed numbers for the primary endpoint. The record does not report exposure-adjusted event rates, a statistical comparison of these counts, event timing, or detailed criteria for seriousness. It also does not provide enough information to infer whether an event was caused by study treatment.

The registry lists appendicitis, spontaneous abortion, pericardial effusion, and seizure among the top serious-event terms, each recorded as 0.2%. The record does not identify an arm for each listed term in this summary, so those terms should not be assigned to a particular treatment group on that basis. Small event counts and limited detail make the safety figures descriptive; they do not establish the presence or absence of a treatment-related risk.

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

The primary result describes the proportion of analyzed participants who met a specific definition of pain freedom two hours after initial treatment. The posted percentages are higher in each ubrogepant arm than in the placebo arm. The sponsor’s reported logistic-regression analyses give odds ratios above 1, with the confidence intervals and p-values recorded for each dose comparison. This is evidence about group-level results within this randomized study and its stated analysis population.

The result does not mean that every participant receiving ubrogepant experienced pain freedom, or that any particular person would have the same outcome. It does not measure the severity of residual pain among those who did not meet the endpoint, and it does not summarize outcomes beyond the specified time. Although participants could take a second dose or rescue medication later, the primary endpoint concerns the two-hour assessment after the initial dose.

The trial compares each active dose with placebo. The registry does not report a direct statistical comparison between ubrogepant 50 mg and ubrogepant 100 mg, so the arm percentages alone should not be used to claim that one dose is superior to the other. A numerical ordering of observed percentages is not itself a formal head-to-head test.

The findings do not establish results for repeated migraine attacks, longer-term treatment, or populations not described by the registry record. The trial is listed as a single-attack study, and the primary endpoint is defined for a particular postdose time. The registry record does not report enough information to extend the result to other settings or treatment schedules.

Statistical significance and clinical importance are distinct. The record does not report a threshold for a clinically important difference, and a p-value does not supply one. Interpretation should consider the endpoint definition, uncertainty intervals, analysis population, multiplicity, missing-data handling, and the sponsor’s reported analysis. These results are statistical descriptions of the posted trial evidence, not individualized medical guidance.

18. Why This Trial Matters Statistically

This trial is statistically informative because it uses random allocation and a placebo comparator to frame two dose-specific comparisons for an explicitly defined binary endpoint. The primary measure is straightforward to interpret as the percentage meeting a stated pain-freedom definition at a fixed time. The registry also provides sponsor-reported logistic-regression estimates and confidence intervals, alongside arm percentages and counts that allow simple unadjusted recalculations.

The example illustrates why effect measures matter. An odds ratio and a risk difference describe a comparison on different scales. Reporting the outcome percentages helps readers understand the event frequency, while the odds ratio summarizes relative odds and the risk difference summarizes an absolute difference in proportions. Those estimates cannot be exchanged without changing the question being answered. The flagged discrepancy reinforces the importance of distinguishing the sponsor’s analysis from a summary-based recalculation.

The trial also shows why confidence intervals and p-values should be read together with endpoint definitions and analysis populations. The primary endpoint has a clear time point and response criterion, but its analyzed population is restricted by treatment, baseline-recording, and postdose-assessment requirements. Different outcomes use different analyzed numbers, and the registry record does not fully explain missing-data handling.

Finally, the presence of several secondary outcomes raises a standard issue in clinical trial interpretation: multiple comparisons need a reported analysis strategy to establish confirmatory weight. The broad consistency of the posted secondary pattern can add context, but it does not remove uncertainty about multiplicity or turn secondary results into independent replications. The record is a useful example of how design, estimand, uncertainty, analysis reporting, and endpoint multiplicity jointly shape a statistical reading.

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 does not report a complete statistical analysis plan, the original sample-size justification, or the specific randomization and allocation procedures. It identifies logistic regression for the sponsor’s analyses but does not state model covariates or provide full model specifications. The discrepancy between the sponsor’s reported results and simple unadjusted recalculations is flagged; its precise source is not reported, and the sponsor’s own analysis takes precedence.

The primary analysis uses a modified intent-to-treat population with endpoint-assessment requirements. The record does not report a full flow of participants into each analysis, reasons for missing assessments, or how missing outcomes were handled. Endpoint-specific analyzed numbers differ. Without more detail, the influence of missingness or exclusions cannot be assessed from the posted summary alone.

The trial concerns a single migraine attack and a two-hour primary assessment after initial treatment. The record does not establish whether the findings apply to repeated attacks, longer-term use, or other treatment circumstances. The arm descriptions permit later second dosing or rescue medication, but the registry record does not give detailed use patterns or explain how later treatment relates to each outcome analysis.

Several secondary outcomes and comparisons are listed, but multiplicity handling and any prespecified testing hierarchy are not reported. This limits how confidently secondary p-values can be treated as confirmatory. The safety summary provides event counts and terms, but not detailed timing, exposure-adjusted rates, causal assessments, or formal comparisons. These limitations concern the scope and reporting of the registry record and do not, by themselves, establish that the analyses or trial conduct were inadequate.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy, Safety, and Tolerability Study of Oral Ubrogepant in the Acute Treatment of Migraine — NCT02828020.
• Registry record last updated 2019-01-03; status last verified 2018-12.
• Results first posted 2019-01-03.
• 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

NCT02828020 is a completed Phase 3, multicenter, randomized, double-blind, parallel-group, placebo-controlled study of oral ubrogepant for a single migraine attack. The registry lists enrollment as 1672, a study start date of 2016-07-22, and a primary completion date of 2017-12-13. The sponsor was Allergan.

The primary endpoint was pain freedom two hours after the initial dose, defined as a change from moderate or severe headache at baseline to no pain. The posted percentages were 11.8% for placebo, 19.2% for ubrogepant 50 mg, and 21.2% for ubrogepant 100 mg. Sponsor-reported logistic-regression analyses favored each dose over placebo according to the registry’s superiority labels. A discrepancy is flagged between sponsor analyses and simple unadjusted recalculations, so the sponsor’s own analysis takes precedence.

Six secondary outcomes and safety summaries are also posted. The registry record does not report the full statistical analysis plan, multiplicity strategy, missing-data handling, or original sample-size justification.