Comparative Study of Oral Atogepant Versus Oral Topiramate to Assess Adverse Events in Adult Participants With Migraine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparative Study of Oral Atogepant Versus Oral Topiramate to Assess Adverse Events in Adult Participants With Migraine (NCT05748483), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Discontinued Treatment Due to Treatment-Emergent Adverse Events (TEAEs).

2. Clinical Question

3. Trial Design

TEMPLE, registered as NCT05748483, is a completed phase 3 randomized, quadruple-masked, parallel-group, active-controlled trial sponsored by AbbVie. It compares oral atogepant with oral topiramate for migraine prevention. The registry lists the study start as 2023-10-07 and primary completion as 2025-04-28. The brief summary describes approximately 85 sites across the world and an intended enrollment of approximately 520 participants aged 18 and older; the registry enrollment field lists 545.

The study had a double-blind treatment period followed by an open-label safety extension. During the double-blind period, participants were randomly assigned to atogepant or topiramate, with matching placebo treatments described in the brief summary. The assigned treatments were given for 24 weeks. From Week 25, eligible participants in either group could receive atogepant in the open-label period, which continued for 52 weeks. Safety monitoring continued for 4 weeks after a participant’s last study treatment, according to the brief summary.

The primary endpoint is assessed at Week 24, so the central randomized comparison concerns the double-blind period. The open-label period offers later safety follow-up but, because the groups could both receive atogepant, it is not a continuing blinded comparison of atogepant against topiramate. The registry record does not report the original sample-size justification or the assumptions used in the trial’s design. Those design details should not be inferred from the separate planning illustrations based on the observed results.

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.

Double Blind (DB) Period

Reasons for not completing this period:

Open Label (OL) Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Safety Population 1 - All participants who received at least 1 dose of study treatment during the DB treatment period. Here, 'Overall Number of Participants Analyzed' is the number of participants evaluable for this Endpoint.

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: ITT - Intent-to-Treat Population includes all randomized subjects.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Discontinued Treatment Due to Treatment-Emergent Adverse Events (TEAEs), measured over Week 24.

The primary endpoint is the percentage of participants who discontinued treatment because of treatment-emergent adverse events by Week 24. The registry defines an adverse event as an untoward medical occurrence in a participant administered a pharmaceutical product; the event does not necessarily have a causal relationship to treatment. The investigator assesses the relationship to study drug. A treatment-emergent event is defined by its timing in relation to double-blind dosing, including the registry’s stated window after the last dose and before open-label dosing when applicable.

This endpoint is used to describe a specific aspect of tolerability: stopping assigned treatment when an event is considered a reason for discontinuation. It is distinct from the occurrence of any adverse event, the occurrence of a serious adverse event, and an investigator’s assessment of causality. Participants can experience an event without discontinuing, and discontinuation can reflect decisions or circumstances not captured by an event count alone.

The registry identifies the analysis population as participants who received at least 1 dose during the double-blind period and says the overall number analyzed is the number evaluable for this endpoint. The posted percentages are 29.6% for topiramate and 12.1% for atogepant. These figures describe the analyzed groups at Week 24; they do not alone describe the full safety profile or the longer open-label period.

7. Results Posted in the Registry

• Atogepant: 12.1% (33/273) versus 29.6% (79/267) on control; risk difference -17.5 percentage points (95% CI -24.2 to -10.8), risk ratio 0.41 (0.28–0.59); 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 Achieving ≥ 50% Improvement (Reduction) in Mean Monthly Migraine Days (MMD) During Months 4 to 6 (DB Period)

• 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:
  • Atogepant: 64.1% (173/270) versus 39.3% (101/257) on control; risk difference 24.8 percentage points (95% CI 16.5 to 33.0), risk ratio 1.63 (1.37–1.94); 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 Atogepant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Mean Monthly Migraine Days During Months 4 to 6 (DB Period)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Atogepant: mean -6.27 versus -4.49 on control; difference -1.78 (95% CI -2.52 to -1.04), standardized effect d = -0.43; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Atogepant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Total 6-Item Headache Impact Test (HIT-6) Score at Week 24

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Atogepant: mean -11.70 versus -7.40 on control; difference -4.30 (95% CI -5.89 to -2.71), standardized effect d = -0.50; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Atogepant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes extend the primary tolerability question to migraine burden and participant-reported impact. Their overall pattern favors atogepant on the reported double-blind measures: the responder proportion was higher, and the model-based changes in mean monthly migraine days and HIT-6 score were more negative. These outcomes address different dimensions from discontinuation due to treatment-emergent adverse events, so they add context rather than serving as alternative measures of the primary endpoint.

The registry record lists additional secondary measures, including migraine-specific quality of life, patient global impression of change, and cognitive-function reporting. Numerical results for all listed secondary measures are not included in the posted results used for these comparisons. The available results should not be generalized to unreported measures or to outcomes for which no numerical estimates are posted.

The sponsor reports statistical analyses for the posted responder and continuous outcomes, and the record also contains unadjusted recalculations. Each result is outcome-specific. A favorable direction across several measures can be informative about consistency, but it does not by itself establish that every outcome was statistically significant under a prespecified multiplicity strategy or that all measures show the same treatment effect.

Unadjusted secondary results carry less weight because multiple outcomes create more opportunities for apparently notable results, and the registry record does not report whether or how multiplicity was controlled. The record also does not report a complete analysis plan, so it is not possible to establish from these results which secondary tests were confirmatory, how missing observations were treated for each measure, or whether outcome hierarchies were prespecified. These findings are best read as supporting context for the primary randomized comparison, not as a substitute for it.

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

• Percentage of Participants Achieving ≥ 50% Improvement (Reduction) in Mean Monthly Migraine Days (MMD) During Months 4 to 6 (DB Period)
• Change From Baseline in Mean Monthly Migraine Days During Months 4 to 6 (DB Period)
• Change From Baseline in the Total 6-Item Headache Impact Test (HIT-6) Score at Week 24
• Change From Baseline in Migraine-Specific Quality of Life Questionnaire Version 2.1 (MSQ v2.1) Role Function - Restrictive (RFR) Domain Score At Week 24
• Percentage of Participants Achieving a Rating of "Much Better" or "Very Much Better" Assessed by the Patient Global Impression of Change (PGIC)
• Change From Baseline in Patient-Reported Outcomes Measurement Information System (PROMIS) Cognitive Function - Abilities Subset - Short Form 6a Version 2.0 Score

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical summaries are used because the outcomes have different forms. The primary endpoint and the responder endpoint are percentages of participants with an event or response. The migraine-day and HIT-6 outcomes are reported as model-based mean changes. A percentage comparison, a mean difference, and a relative risk answer related but not identical questions, so their numerical scales should not be conflated.

What does a risk difference describe?

A risk difference subtracts the comparator group’s event proportion from the intervention group’s event proportion. A negative value for the primary endpoint means the observed proportion discontinuing due to treatment-emergent adverse events was lower in the atogepant group. The posted recalculated estimate is -0.175, with a 95% confidence interval from -0.242 to -0.108. The estimate is an unadjusted re-calculation from the posted summary statistics, rather than the sponsor’s model-based result.

How does a relative risk differ?

A relative risk compares the proportions as a ratio rather than a subtraction. The sponsor reported a relative risk of 0.41 for the primary endpoint, with a 95% confidence interval from 0.28 to 0.59, using the Miettinen and Nurminen method. A value below 1 indicates a lower observed event proportion in the atogepant group relative to topiramate. The relative-risk scale does not state the absolute percentage-point difference, and the two measures should not be treated as interchangeable.

The sponsor also used the Miettinen and Nurminen method for the secondary responder comparison. For continuous outcomes, the reported analysis used a Mixed-effect Model Repeated Measurement method and presented least-squares mean differences. These model-based estimates account for repeated outcome measurements according to the fitted model. The registry record does not report the full model specification, covariates, covariance structure, or detailed missing-data assumptions, so those elements cannot be reconstructed from the posted summaries.

What does a confidence interval communicate?

A confidence interval describes the range of estimates compatible with the observed data under the method’s assumptions and repeated-sampling interpretation. It communicates uncertainty around an estimated group contrast, not the range of individual participant outcomes. The interval’s width reflects precision: a narrower interval indicates greater precision for that estimate, while a wider interval leaves more uncertainty. A confidence interval does not correct for bias, unreported design choices, or multiple testing.

The reported p-values evaluate compatibility between the observed data and a null comparison under the stated analysis. The sponsor’s primary p-value is < 0.001, and the recalculated unadjusted p-value is <0.001. These values are not probabilities that the null hypothesis is true, nor are they measures of effect size. The registry record does not report whether the reported analyses were adjusted for multiplicity. That matters particularly when interpreting multiple secondary outcomes.

What is the role of the recalculation?

The posted recalculated risk difference is a simple, unadjusted comparison based on group-level summary statistics. It does not reproduce the sponsor’s Miettinen and Nurminen analysis, which estimates relative risk. Similarly, the continuous-outcome planning illustrations use summary-statistic-based approximations; they do not replace the sponsor’s repeated-measures model. The discrepancy indicator is false, but the sponsor’s own analysis remains the primary reported analysis where available. Recalculations provide a complementary check of the direction and scale of a comparison, not a substitute for the trial’s analysis.

For continuous outcomes, the group results are least-squares mean changes with standard errors. The sponsor-reported contrasts are least-squares mean differences, confidence intervals, and p-values. The registry record also includes approximate pooled standard deviations for planning illustrations, derived from the posted standard errors. Such approximations are useful for the stated planning exercise but do not supply a complete account of the model or the distribution of participant-level outcomes.

The trial’s primary analysis population is described as a safety population: participants receiving at least 1 dose during the double-blind period, with the endpoint denominator defined by evaluability. The analysis counts differ across posted outcomes, and the registry record does not state all reasons for those differences. It is therefore important not to assume that every endpoint uses the same participants or missing-data rules.

11. Confidence Intervals and Precision

The sponsor-reported relative-risk estimate for the primary endpoint is 0.41, with a 95% confidence interval from 0.28 to 0.59. The interval lies below 1, the value corresponding to equal event proportions on a relative-risk scale. The recalculated risk difference is -0.175, with a 95% confidence interval from -0.242 to -0.108; that interval lies below 0, the value corresponding to no difference on a difference scale. These intervals indicate that the posted estimates are not centered near a null comparison, while still allowing a range of effect sizes.

A confidence interval is a measure of statistical precision under the method and assumptions used. It does not mean that there is a 95% probability that the fixed treatment effect lies within the particular interval. Nor does it cover uncertainty from possible bias, selection, measurement, unreported analysis decisions, or multiplicity. The interval concerns a group-level estimate, not the range of responses expected among individual participants.

The sponsor’s interval and the recalculated interval differ in scale and method. The sponsor reports a relative risk using the Miettinen and Nurminen method; the recalculation reports an unadjusted risk difference. Their endpoints should therefore be read as separate summaries, not as competing versions of the same numerical quantity. The registry reports the sponsor’s result as primary and the discrepancy indicator is false.

Secondary confidence intervals are also reported for the responder outcome and model-based mean differences. They describe precision for those particular contrasts, but they do not resolve the concerns arising from multiple outcomes or unreported missing-data details. The registry record does not report a multiplicity adjustment, so nominal confidence levels and p-values should not be read as if they necessarily control uncertainty across the full set of outcomes.

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 effects, not the trial’s original design assumptions. For these binary and continuous outcomes, the figures are participants per arm. The record’s planning assumptions 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 trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm associated with an 80% chance of detecting the stated effect under those planning assumptions, if that effect and assumptions were correct. The 90% power column describes the corresponding illustration for a 90% chance. These are design calculations, not guarantees about the result of a future study. The figures are not observed power.

Rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect explore progressively smaller target effects. Smaller effects generally require more participants to detect with the same planning assumptions, which is why the displayed participant requirements increase as the target effect is reduced. These rows are scenarios, not estimates of what a future trial will observe.

The figures should be interpreted as planning aids rather than as evidence that the completed trial was designed to those exact assumptions. They do not account for design features or analysis choices that are not included in the stated illustration, and they do not establish that any particular sample size is adequate for all endpoints. The registry record does not report the trial’s original power calculation or its design rationale.

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 = 0.296; treatment proportion p₁ = 0.121; average p̄ = 0.208.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5744 = 1.1258.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5609 = 0.4721.
4. n = (1.1258 + 0.4721)² / (-0.1750)² = 83.4, rounded up to 84 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 <- 0.295880149812734                          # control proportion
p1 <- 0.120879120879121                          # 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(5748483)
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 = 84 (80% power), 112 (90% power)
 75% of observed effect: n per arm = 161 (80% power), 215 (90% power)
 50% of observed effect: n per arm = 386 (80% power), 516 (90% power)
power.prop.test: 83.4 
Simulated power at n = 84 per arm: 0.819 (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

For the primary endpoint, the sponsor reported a relative risk of 0.41 with a 95% confidence interval from 0.28 to 0.59 and p < 0.001, using the Miettinen and Nurminen method. The sponsor’s analysis takes precedence over the simple recalculation when describing the trial’s own reported result. Its relative-risk scale compares the event proportions as a ratio.

The recalculated estimate is an unadjusted risk difference of -0.175, with a 95% confidence interval from -0.242 to -0.108 and p < 0.001. It is derived from posted group summary statistics and uses a different measure from the sponsor’s relative risk. The negative direction agrees with the sponsor’s result: the observed discontinuation proportion is lower in the atogepant group. The numerical estimates are not directly comparable because one is a difference and the other a ratio.

The registry record marks the discrepancy indicator as false. The sponsor-reported result is still the authoritative trial analysis, while the recalculation serves as an unadjusted supplementary check. For secondary outcomes, the sponsor reports Miettinen and Nurminen analyses for the binary responder measure and repeated-measures model analyses for continuous outcomes. Recalculated summary-statistic comparisons do not reproduce those model-based analyses or their assumptions.

15. Multiplicity, Missing Data and Analysis Populations

The trial reports a primary endpoint and multiple secondary outcomes. When many outcomes are examined, the chance of obtaining at least one apparently unusual result under null effects can increase. Statistical approaches can address this multiplicity, for example by adjusting significance thresholds or defining a testing hierarchy. The registry record does not report whether a multiplicity procedure was used, which outcomes were included in any procedure, or whether secondary analyses were confirmatory. Accordingly, nominal p-values and confidence intervals for secondary measures should be interpreted cautiously and not treated as though family-wise error control has been established.

The record does not report enough detail to reconstruct missing-data handling across outcomes. It identifies the primary population as participants who received at least 1 dose during the double-blind period and describes the endpoint denominator as participants evaluable for that endpoint. The analysis counts differ across outcomes. Reasons for those differences, the handling of missing visits or discontinuation, and sensitivity analyses for missing observations are not reported in the registry record.

For continuous outcomes, the sponsor reports a Mixed-effect Model Repeated Measurement analysis. The registry record does not specify the full model, its covariates, covariance assumptions, or missing-data assumptions. These details affect how model-based estimates should be interpreted, particularly if outcome data are missing for reasons related to treatment or health status. No specific missing-data mechanism should be assumed from the analysis label alone.

The registry identifies a safety population for the primary outcome, but it does not provide a complete account of analysis populations for every endpoint. It also does not report the original statistical analysis plan or any interim-analysis procedures. These omissions limit independent assessment of prespecification, multiplicity control, and the robustness of the posted estimates. They do not change the numerical results reported, but they narrow what can be concluded about their inferential status.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cartilage injury (0.4%), back pain (0.4%), migraine (0.4%), bradycardia (0.4%), dyspepsia (0.4%).

The registry posts serious adverse event counts separately for the double-blind groups and the open-label atogepant group. In the double-blind period, serious adverse events affected 3 of 272 participants at risk in the topiramate group and 7 of 273 participants at risk in the atogepant group. In the open-label period, 8 of 457 participants at risk in the atogepant group were affected. The record reports 0 deaths in each of these groups.

These are descriptive counts, not a randomized comparison across all periods. The open-label group differs in treatment exposure and study period from the double-blind groups, so its figures should not be treated as a direct comparison with topiramate. Serious adverse event counts also do not establish causality, severity patterns beyond the serious classification, or the overall benefit-risk profile. The registry lists serious event terms with reported percentages, but those terms should not be interpreted as proof that the study drug caused them.

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

The primary result describes a lower observed percentage of treatment discontinuations attributed to treatment-emergent adverse events in the atogepant group than in the topiramate group during the double-blind period through Week 24. The sponsor’s relative-risk estimate and the unadjusted risk-difference recalculation both point in that direction, with confidence intervals that exclude their respective null values. The result is evidence about this defined endpoint in the analyzed trial populations.

It does not show that atogepant prevents all adverse events, that every participant tolerates it, or that every observed event was caused by treatment. The endpoint combines event emergence, investigator assessment, and a decision to discontinue. It is not equivalent to all adverse-event incidence or to serious adverse event incidence. The separately posted serious-event counts provide safety context but do not settle causal questions.

The trial also reports secondary outcomes concerning migraine days and patient-reported impact. Their group-level pattern is relevant context, but the registry record does not report whether multiplicity was controlled or provide all numerical results for every listed secondary measure. They therefore should not be used to claim a comprehensive or definitive effect across all outcomes.

The randomized, masked, active-controlled design supports interpreting the double-blind comparison as a group comparison under the trial conditions. The open-label extension is different: eligible participants in both original groups could receive atogepant, so later observations do not maintain the original randomized treatment contrast. The registry record does not report the trial’s original sample-size rationale, complete missing-data methods, or full statistical analysis plan. Those limitations constrain how far the posted estimates can be generalized or independently evaluated.

These results describe a completed clinical trial, not individualized treatment choices. They do not establish how the treatments compare in populations or settings not represented by the registry record, and they do not replace clinical judgment. The central statistical interpretation remains specific: a difference between analyzed groups for a prespecified tolerability-related endpoint during the double-blind period, with uncertainty represented by the reported confidence intervals.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares an active migraine-prevention treatment with atogepant in a randomized, masked design, while making treatment discontinuation due to treatment-emergent adverse events the primary endpoint. The outcome focuses on a clinically relevant aspect of tolerability, but its narrow definition also makes clear why it should not be mistaken for a complete safety summary.

The reported sponsor analysis and the unadjusted recalculation express the same group contrast on different scales. Reading both requires distinguishing relative and absolute measures rather than relying on a p-value alone. The confidence intervals add information about precision, while the secondary measures provide a broader view of migraine burden and patient-reported outcomes. Together, these features illustrate why statistical interpretation depends on outcome definition, estimand, analysis method, and uncertainty.

The two-period design also matters. The double-blind period supports the randomized comparison, whereas the open-label extension addresses later exposure without the same between-group contrast. Combining those periods as if they were one continuous randomized comparison would obscure the design. Finally, the registry’s lack of reported detail about multiplicity, missing-data handling, and original sample-size justification shows why numerical results should be considered alongside transparency about analysis choices.

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 the original sample-size justification or the design assumptions behind enrollment. The stated planning illustrations are based on observed effects and should not be taken as evidence about the trial’s original design. The record also does not include a complete statistical analysis plan, so prespecification and analysis hierarchy cannot be fully evaluated from the posted results.

Multiplicity handling is not reported, limiting the confirmatory interpretation of multiple secondary outcomes. Missing-data methods, sensitivity analyses, and reasons for different endpoint analysis counts are also not reported. These gaps are particularly relevant for model-based repeated-measures outcomes and for endpoint populations defined by evaluability.

The registry’s enrollment figure is 545, while the brief summary describes approximately 520 participants. The record does not explain the relationship between those figures. The primary analysis uses outcome-specific evaluable populations rather than the enrollment figure, so the denominators should be read directly with each outcome rather than assumed to match enrollment.

The open-label extension differs from the randomized double-blind comparison because eligible participants in both groups could receive atogepant after Week 24. Extension safety counts are descriptive and do not preserve the original active-comparator contrast. The posted summary also does not provide numerical results for every secondary outcome listed in the registry record. These limitations restrict conclusions about longer-term comparative safety, unreported outcomes, and generalizability beyond the studied setting.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparative Study of Oral Atogepant Versus Oral Topiramate to Assess Adverse Events in Adult Participants With Migraine — NCT05748483.
• Registry record last updated 2026-07-02; status last verified 2026-06.
• Results first posted 2026-07-02.
• 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

NCT05748483, TEMPLE, is a completed phase 3 randomized, quadruple-masked, parallel-group trial sponsored by AbbVie. It compared atogepant with topiramate during a 24-week double-blind period, followed by an open-label atogepant extension for eligible participants. The primary endpoint was discontinuation due to treatment-emergent adverse events at Week 24.

The posted primary result shows a lower discontinuation percentage in the atogepant group. The sponsor reported a relative risk of 0.41, with a 95% confidence interval from 0.28 to 0.59 and p < 0.001. Secondary results address migraine days and patient-reported outcomes. Interpretation is limited by unreported details on multiplicity, missing-data handling, and the original design assumptions.