Efficacy and Safety Study of BOTOX® Compared to Topiramate for the Prevention of Chronic Migraine in Adults: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of BOTOX® Compared to Topiramate for the Prevention of Chronic Migraine in Adults (NCT02191579), a randomized phase 4 study. The primary outcome is Percentage of Participants With a ≥ 50% Decrease From Baseline in the Frequency of Headache Days.

2. Clinical Question

The central question is whether the proportion of adults with chronic migraine who achieve a reduction of at least 50% in headache days differs between the BOTOX® and topiramate groups. The registry record reports a randomized, open-label, parallel-group study comparing these preventive treatment approaches. The primary outcome was assessed from baseline through the last 28-day period ending with Week 32.

This question concerns the proportion crossing a prespecified response threshold, rather than the average change in headache days for everyone in a group. The result therefore describes the frequency of this particular level of reduction in the registry’s analysis population; it does not describe every participant’s experience or all possible dimensions of migraine burden.

3. Trial Design

The registry describes a multicenter, prospective, randomized, open-label, parallel-group Phase 4 study. It lists 282 participants enrolled and a completed study. The recorded start date is 2014-08-05, and the primary completion date is 2017-05-09. No masking was used, so participants and study personnel were not blinded to the assigned treatment according to the registry design entry.

The two groups followed different treatment schedules. BOTOX® was given as 155U of onabotulinumtoxinA per treatment by intramuscular injection every 12 weeks for up to 3 treatments. Topiramate began at 25 mg/day by mouth and was titrated up to a maximum of 100 mg/day for 36 weeks. The record notes that participants who discontinued topiramate were eligible to receive BOTOX®. It does not report how many participants used that option.

The primary endpoint used the ITT Set, which the record defines as all randomized participants. The posted primary arm counts were 140 for BOTOX® and 142 for topiramate. A randomized design supports a comparison between assigned groups, while open-label conduct can affect expectations, treatment decisions, and participant reporting. Those are general considerations, not evidence that any particular influence occurred in this trial.

The registry record does not report the trial’s original sample-size justification, detailed randomization procedures, allocation concealment, interim analyses, or a full statistical analysis plan. Those details should not be inferred from the sample-size planning illustrations or from the analyses posted for the outcomes.

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 1

Reasons for not completing this period:

Treatment 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Set included all randomized participants.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Intent-to-treat (ITT) Set included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With a ≥ 50% Decrease From Baseline in the Frequency of Headache Days, measured over Baseline (First 28 days from Screening) to the last 28-day period ending with Week 32.

The primary endpoint was the percentage of participants with at least a 50% decrease from baseline in the frequency of headache days. Baseline was the first 28 days from screening, and the outcome period was the last 28-day period ending with Week 32. Participants recorded headaches in a daily e-diary. A headache day was defined as a calendar day with at least 4 hours of headache, or headache of any duration with use of migraine-specific acute headache medication. The number of headache days was counted over each 28-day period.

This endpoint is a responder measure: each participant is classified according to whether the decrease reaches the stated threshold, and the group result is the percentage meeting that criterion. Such measures can make a treatment comparison easier to interpret as the proportion reaching a particular degree of change. As a general statistical trade-off, converting a continuous change into a yes-or-no response discards information about the size of change within each response category. The endpoint does not show the full distribution of individual changes, and it does not by itself capture other aspects of headache burden.

The measure is relevant to the study’s stated prevention question because it compares change in headache-day frequency from baseline over a defined follow-up period. The registry record does not report a separate justification for selecting the 50% threshold.

7. Results Posted in the Registry

• Topiramate: 12.0% (17/142) versus 40.0% (56/140) on control; risk difference -28.0 percentage points (95% CI -37.7 to -18.3), risk ratio 0.30 (0.18–0.49); 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.

Change From Baseline in the Frequency of Headache Days Per 28-day 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 deviations.
• Result:
  • Topiramate: mean -2.10 versus -8.30 on control; difference 6.20 (95% CI 4.46 to 7.94), standardized effect d = 0.84; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Topiramate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Headache Impact Test (HIT-6) Total Score

• 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 deviations.
• Result:
  • Topiramate: mean -1.30 versus -5.60 on control; difference 4.30 (95% CI 2.78 to 5.82), standardized effect d = 0.75; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Topiramate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With a ≥ 70% Decrease From Baseline in the Frequency of Headache Days

• 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:
  • Topiramate: 8.5% (12/142) versus 27.1% (38/140) on control; risk difference -18.7 percentage points (95% CI -27.4 to -10.0), risk ratio 0.31 (0.17–0.57); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Topiramate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the three posted secondary outcomes, the registry reports contrasts favoring the BOTOX® group in the direction of greater reduction in headache-day frequency, greater reduction in HIT-6 score, and a higher proportion meeting the more stringent headache-day reduction threshold. The posted sponsor analyses report p < 0.001 for each of these outcomes. This overall pattern is directionally consistent with the primary responder result, but secondary results do not replace the primary endpoint or establish effects on outcomes that were not measured.

The secondary endpoints address related but distinct aspects of the study question. One measures change in headache days as a continuous outcome, another measures change in headache impact, and the third counts participants meeting a more stringent response definition. Agreement in direction across different measures can add context, while differences in scales, analysis populations, and follow-up periods complicate direct comparison. The registry record does not report a single combined analysis across these endpoints.

Unadjusted secondary results generally carry less inferential weight when multiple outcomes are tested. As a general statistical concern, considering several comparisons increases the chance of at least one apparently unusual result if no multiplicity adjustment is used. The registry record lists four outcome measures, including the primary measure, and posts three secondary outcomes. It does not report whether the secondary analyses were prespecified in a detailed analysis plan or whether any adjustment for multiple testing was applied. Their p-values should therefore be read as reported results, not as a complete account of uncertainty across the family of outcomes.

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

• Change From Baseline in the Frequency of Headache Days Per 28-day Period
• Change From Baseline in Headache Impact Test (HIT-6) Total Score
• Percentage of Participants With a ≥ 70% Decrease From Baseline in the Frequency of Headache Days

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met the threshold of at least a 50% decrease in headache days or did not. The registry reports the percentage meeting that threshold in each group and also reports a logistic regression odds ratio. The unadjusted recalculation gives a risk difference from the posted counts and denominators. These methods answer related but distinct questions, so the numerical estimates use different scales.

What does the risk difference describe?

As a general statistical concept, a risk difference subtracts the event proportion in one group from the event proportion in another. Here, the recalculated contrast is defined as topiramate minus BOTOX®. Its negative estimate describes a lower observed response proportion in the topiramate arm. A risk difference is expressed on the proportion scale and is often easier to connect to the observed event percentages than an odds ratio. The interval around the estimate represents uncertainty in the group contrast, subject to the assumptions of the calculation.

What does the logistic regression odds ratio describe?

The registry reports logistic regression with an odds ratio of 4.94 for the BOTOX® and topiramate groups. In general, logistic regression models the log odds of a binary outcome, and the odds ratio compares the odds between groups. Odds and probabilities are related but are not interchangeable. An odds ratio is not a risk difference and should not be read as a direct change in the percentage of responders. The registry also reports a 95% confidence interval and p < 0.001 for this analysis.

The registry’s reported logistic regression analysis is the sponsor-reported model-based result. The recalculated risk difference is a simple unadjusted comparison based on posted group summaries. Because the scales and methods differ, the estimates should be interpreted according to their definitions rather than treated as duplicate versions of the same number.

How should the continuous secondary outcomes be read?

For headache-day frequency and HIT-6 score, the registry posts group means and standard deviations, while the sponsor-reported analyses use ANCOVA. General explanation: ANCOVA estimates a group contrast while accounting for covariates included in the model. The registry record does not identify the covariates used, so the adjustment cannot be reconstructed from the posted information. The recalculated mean differences are unadjusted comparisons from the posted summary statistics and do not reproduce an ANCOVA model.

A standard deviation describes the spread of individual observations around a group mean; it is not the standard error of the mean or a confidence interval. A mean change below zero indicates a decrease from baseline on the measure as coded. For the HIT-6 outcome, the registry’s reported analysis is labeled a median difference, whereas the posted group summaries are means and standard deviations. Those are different summaries, and the registry record does not provide enough detail to reproduce the reported model estimate from the group summaries alone.

Why does over-dispersion matter in some analyses?

General explanation: a statistical model can be over-dispersed when the observed variability exceeds what the model’s assumed distribution allows. If that extra variability is not accounted for, standard errors can be too small and confidence intervals too narrow. This primary outcome is a binary responder measure, and the registry reports logistic regression. The record does not report a dispersion assessment or a special over-dispersion adjustment, so no claim can be made about whether either was used.

For continuous outcomes, variability is represented in the posted group summaries by standard deviations. For binary outcomes, event counts and proportions describe the observed data, while the model produces an odds ratio and its interval. The assumptions and adjustment details for the sponsor’s models are not fully reported in the registry record.

What can a p-value establish?

General explanation: a p-value measures how incompatible the observed data are with a specified null model, assuming that model and its assumptions are correct. It is not the probability that the null hypothesis is true, nor is it a measure of the probability that the result will replicate. The reported p < 0.001 indicates that the analysis produced a small p-value under its model; it does not quantify the magnitude of the contrast. Effect estimates and confidence intervals are needed to describe magnitude and precision.

The posted analyses identify the primary population as all randomized participants. They do not report a detailed missing-data method, a sensitivity analysis, model diagnostics, or the complete covariate specification. These absences limit independent assessment of the analyses and should not be filled in by assumptions about common practice.

11. Confidence Intervals and Precision

The primary unadjusted risk difference is -0.280, with a 95% confidence interval from -0.377 to -0.183, for topiramate relative to BOTOX®. The entire reported interval is below zero, consistent with a lower observed response proportion for topiramate in this contrast. The interval gives a range of values compatible with the data and the calculation’s assumptions; it is not a range containing 95% of individual participant outcomes.

The registry’s logistic regression estimate is an odds ratio of 4.94, with a 95% confidence interval from 2.681 to 9.085. This interval is on the odds-ratio scale, so it cannot be compared numerically with the risk-difference interval as if the measures had the same units. Both intervals communicate uncertainty, but each applies to a different effect measure and analysis.

As a general statistical concept, a confidence interval reflects both the observed data and the method’s assumptions. A narrower interval indicates greater precision for that estimate on its scale, while a wider interval indicates more uncertainty. Confidence intervals do not account automatically for every limitation, such as possible bias from open-label conduct, missing outcomes, or selective reporting. The registry record does not provide enough information to assess all such sources of uncertainty.

The sponsor-reported logistic regression interval and the unadjusted recalculation are not interchangeable: they use different methods and effect measures. The reported interval should be read with its model estimate, and the recalculated interval with the unadjusted risk difference. Neither interval alone establishes clinical importance.

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 original trial’s documented design calculation. The figures for these outcomes are participants per arm, not total event counts. The registry’s original sample-size justification and assumptions are not reported in the registry record.

The 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 set at the stated fraction of the observed effect. The displayed scenarios include planning for 100%, 75%, and 50% of the observed effect. For time-to-event outcomes, the planning display would give total events using the Schoenfeld approach; these posted outcomes are not time-to-event outcomes.

The 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect is the true effect. The 90% power column gives the corresponding per-arm planning number for a 90% chance. These are design calculations, not probabilities that the observed trial result is true or that a treatment is beneficial. This is not observed power.

Smaller effects require more participants to achieve the same planned power under the stated assumptions. The planning values are illustrations using the observed effect as a starting point; they do not establish what the study team assumed when designing the trial or whether the original trial was adequately sized for every outcome.

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 = 0.400; treatment proportion p₁ = 0.120; average p̄ = 0.260.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6202 = 1.2156.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5877 = 0.4946.
4. n = (1.2156 + 0.4946)² / (-0.2803)² = 37.2, rounded up to 38 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 <- 0.4                          # control proportion
p1 <- 0.119718309859155                          # 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(2191579)
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 = 38 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 73 (80% power), 97 (90% power)
 50% of observed effect: n per arm = 176 (80% power), 235 (90% power)
power.prop.test: 37.2 
Simulated power at n = 38 per arm: 0.821 (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 logistic regression analysis gives an odds ratio of 4.94, with a 95% confidence interval from 2.681 to 9.085 and p < 0.001. The unadjusted recalculation instead reports a risk difference of -0.280, with a 95% confidence interval from -0.377 to -0.183, for topiramate relative to BOTOX®. The registry record does not flag a discrepancy. These estimates point in a consistent direction but use different effect scales and methods.

The reported analysis should be read as the registry’s model-based result, and the recalculation as a simple unadjusted contrast from the posted summaries. The odds ratio compares odds; the risk difference compares proportions. Their numerical values therefore should not be compared directly. The recalculation does not replace the sponsor’s model or provide a reconstruction of its covariate adjustments.

For the continuous secondary outcomes, the reported analyses are ANCOVA results, while the recalculations use unadjusted summary statistics. The registry describes the HIT-6 sponsor result as a median difference, while the arm summaries are means. These differences in method and summary measure matter when placing the results side by side. The registry record does not report sufficient model detail to recreate the sponsor analyses independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and three secondary outcomes. It reports analyses for the primary endpoint and each of the posted secondary endpoints, but the registry record does not report a multiplicity-adjustment procedure. Without that information, the extent to which the reported p-values account for testing several outcomes is not known. As a general statistical principle, multiple testing can raise the chance of false-positive findings across a set of comparisons; this consideration is especially relevant to secondary results.

The primary outcome population is identified as the ITT Set, defined as all randomized participants. The primary arm counts are 140 for BOTOX® and 142 for topiramate. The posted HIT-6 arm counts are 110 and 115, respectively, while the other posted outcome counts differ by outcome as recorded. The registry record does not explain the differences in analysis counts, report a participant flow accounting, or state how missing outcome data were handled. No assumption should be made about why counts vary.

The record does not report whether analyses used imputation, a complete-case approach, a missing-at-random assumption, or sensitivity analyses for missing data. It also does not report interim analyses, stopping rules, or a full statistical analysis plan. These details are important for evaluating how analysis decisions were made and how robust the findings may be to missing observations or multiple comparisons.

The randomized design and the stated ITT population provide useful context for the primary comparison, but they do not resolve the unreported details. The registry record also does not provide enough information to assess whether every outcome analysis followed an analysis plan fixed before data were examined. These are reporting limitations, not evidence that a particular method was or was not used.

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: concussion (0.7%), chronic obstructive pulmonary disease (0.7%), deep vein thrombosis (0.7%), dehydration (0.7%), nephrolithiasis (0.7%).

The posted serious adverse event figures give the number of participants at risk and the number affected: for BOTOX®, 4 of 220 participants at risk; for topiramate, 6 of 142. The record reports zero deaths in each group. These counts describe the recorded safety populations and should not be treated as if their denominators were the primary endpoint counts. The registry record does not explain why the BOTOX® safety denominator differs from its randomized arm count.

For other adverse events, the record reports 27 affected participants among 220 at risk in the BOTOX® group and 89 among 142 at risk in the topiramate group. These are participant counts, not estimates of event severity or causal attribution. The record lists concussion, chronic obstructive pulmonary disease, deep vein thrombosis, dehydration, nephrolithiasis, and peripheral arterial occlusive disease among the top serious adverse event terms, each at 0.7%.

Adverse-event comparisons require caution because the registry record does not provide a detailed account of exposure time, event ascertainment, seriousness criteria, or causal assessment. The figures describe what was posted and do not by themselves establish comparative safety.

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

The primary result describes the percentage of randomized participants who met a defined reduction threshold during the reported follow-up period. In the posted data, the response proportion was higher in the BOTOX® group than in the topiramate group, and the reported unadjusted risk-difference interval was entirely below zero when the contrast is expressed as topiramate minus BOTOX®. The sponsor-reported logistic regression analysis is also statistically significant as reported in the registry.

This finding does not mean that every participant in one group had a better outcome than every participant in the other. It does not describe how much each responder improved beyond the threshold, the number of headache days for every individual, or outcomes outside the measured period. A group-level contrast cannot determine an individual’s likely response.

The result also does not establish the comparative effect on every aspect of headache burden, quality of life, long-term outcomes, or outcomes not included in the registry. The secondary outcomes add context but require caution because multiplicity handling is not reported. The open-label design is another consideration, particularly for outcomes based on participant recording and reporting; the registry does not establish that any reporting effect occurred.

Finally, the record describes a treatment strategy in which participants who discontinued topiramate were eligible to receive BOTOX®. It does not report how many participants used that option. The posted results should therefore be interpreted in the context of the assigned groups and the treatment arrangements described, without assuming details about actual treatment after discontinuation. These data are statistical evidence about the recorded study outcomes, not medical advice or a complete basis for an individual treatment decision.

18. Why This Trial Matters Statistically

This study is statistically informative because it compares two preventive treatment approaches using randomized parallel groups and reports a primary responder outcome with both group proportions and a model-based analysis. The primary endpoint translates change in headache-day frequency into the proportion of participants meeting a defined threshold. Reporting an effect estimate with a confidence interval, alongside the arm results, helps readers consider both direction and precision rather than relying on a p-value alone.

The trial also illustrates why the effect measure matters. The unadjusted recalculation is a risk difference, whereas the registry’s primary analysis is a logistic regression odds ratio. Both describe the same binary endpoint but on different scales. For continuous secondary outcomes, the recalculations from group summaries differ methodologically from the sponsor-reported ANCOVA results. Recognizing these distinctions prevents unlike estimates from being treated as if they were directly interchangeable.

The study further demonstrates the value of examining analysis populations, outcome definitions, and denominators. The primary outcome is defined using daily e-diary records and a specific headache-day rule, while safety counts use different recorded denominators. Without full reporting of missing-data handling, multiplicity adjustment, and model details, readers cannot fully assess robustness. Those omissions are important for statistical interpretation even when the reported results are clear.

Finally, planning illustrations based on observed effects are not a substitute for a trial’s original sample-size justification. Separating design assumptions from results helps prevent retrospective planning calculations from being mistaken for evidence of the study’s initial power or intent.

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 study was open-label, with no masking recorded. Because the primary outcome depends on headache recording in a daily e-diary, awareness of assigned treatment is a relevant design consideration. This does not establish that reporting was biased, but the registry record does not report methods to evaluate or mitigate that possibility.

The topiramate arm allowed participants who discontinued topiramate to receive BOTOX®. The number who discontinued or received BOTOX® under this provision is not reported in the registry record. The details of treatment exposure and any effect of this option on the assigned-group contrast therefore cannot be assessed from the posted information.

Analysis counts vary across outcomes. The primary population is defined as all randomized participants, but the registry record does not report a full participant flow, reasons for missing observations, or the missing-data methods used. The HIT-6 outcome has fewer posted participants than the primary endpoint, and the reason is not reported in the registry record.

The record does not report the original sample-size justification, the complete statistical analysis plan, the covariates used in the sponsor’s models, or whether multiplicity adjustments were made. The posted recalculations are unadjusted and cannot reproduce the sponsor’s analyses. The open-label design, incomplete details on missing data, and unreported analysis-plan elements limit independent assessment of bias and robustness. The results also apply to the reported outcomes and follow-up periods; the registry record does not establish effects beyond them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of BOTOX® Compared to Topiramate for the Prevention of Chronic Migraine in Adults — NCT02191579.
• Registry record last updated 2018-06-07; status last verified 2018-04.
• Results first posted 2018-06-07.
• 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, multicenter, prospective, randomized, open-label, parallel-group Phase 4 study of BOTOX® and topiramate in adults with chronic migraine. It lists 282 participants enrolled and identifies the primary analysis population as all randomized participants.

The primary outcome was the percentage of participants with at least a 50% decrease in headache days from baseline through the 28-day period ending with Week 32. The posted response proportions were 40.0% for BOTOX® and 12.0% for topiramate. The registry reports a logistic regression odds ratio of 4.94, with a 95% confidence interval from 2.681 to 9.085 and p < 0.001.

Three secondary outcomes and safety results are also posted. The record does not report the original sample-size justification, detailed missing-data methods, multiplicity adjustment, full model specifications, or interim analyses. These gaps limit assessment of some design and analysis details.