Investigation of Efficacy and Safety of Botulinum Toxin A (Botox-Allergan Inc) in Migraine Headaches: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Investigation of Efficacy and Safety of Botulinum Toxin A (Botox-Allergan Inc) in Migraine Headaches (NCT00660192), a randomized phase 2, phase 3 study. The primary outcome is Mean Number of Days of Decrease in Pain Level Using VAS.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-masked, parallel-group study of botulinum toxin A and placebo. It lists the trial as Phase 2 and Phase 3, with Yale University as sponsor. The condition is refractory migraine, and the registry status is completed. The recorded study start is 2008-01 and the primary completion is 2012-07. The total enrollment is listed as 25.

One arm received active Botox, described as onabotulinumtoxinA, and the other received inactive saline. The record says participants were randomized and that treatment was double-blinded. It describes the saline volume as comparable with the active solution volume. The active-arm description specifies 200-300 units of toxin in 2cc-3cc of solution. Further details about allocation concealment, the masking procedures, treatment visits, or follow-up beyond the reported outcome timeframe are not reported in the registry record.

The primary outcome results list 10 participants for placebo and 10 for botulinum toxin. These outcome counts do not match the registry’s total enrollment, and the reason is not reported in the registry record. The safety record uses different at-risk counts: 12 for saline and 13 for Botox. The record does not explain the difference among these counts or state which analysis population was used for each result.

The primary outcome timeframe was 4 weeks. A secondary outcome, satisfaction with treatment, also has a 4-week timeframe. The registry lists two outcome measures and two analyses in total, with one secondary outcome posted. Other trial design details, including the original sample-size justification and the full statistical analysis plan, 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.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Mean Number of Days of Decrease in Pain Level Using VAS, measured over 4 weeks.

The primary endpoint is the mean number of days with decreased pain level during 4 weeks. A day qualifies when pain decreases by 2 grades or more on the Visual Analog Scale, which the registry describes as ranging from 0-10, with 0 meaning no pain and 10 the worst pain. The endpoint therefore counts days meeting a defined change criterion; it is not a measure of average pain intensity across the whole period.

Counting qualifying days can represent how often a participant experiences a meaningful reduction in pain, while the threshold helps distinguish a defined change from smaller movements on the scale. The registry summary frames the study around migraine intensity and frequency, but the posted primary endpoint specifically counts days of decreased pain. It should not be read as a direct count of migraine attacks unless the registry explicitly defines it that way; it does not.

The endpoint is reported as a mean with standard deviation for each arm. A mean describes the average number of qualifying days, while the standard deviation describes how spread out participant values are around that average. In the posted results, the group means are based on 10 participants per arm. The registry does not report individual participant data, a distribution of endpoint values, or additional detail on how daily pain assessments were collected.

7. Results Posted in the Registry

• Botullinum Toxin: mean 8.67 versus 1.20 on control; difference 7.47 (95% CI 1.32 to 13.62), standardized effect d = 1.06; z-test p = 0.017.

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.

Number of Participants Satisfied With Treatment

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Botullinum Toxin: 30.0% (3/10) versus 90.0% (9/10) on control; risk difference -60.0 percentage points (95% CI -93.9 to -26.1), risk ratio 0.33 (0.13–0.88); unadjusted two-proportion z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Botullinum Toxin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcome contributes a different perspective from the primary endpoint. Its overall pattern does not align with the primary mean comparison: the posted satisfaction results favor the placebo arm, whereas the primary outcome mean is higher in the botulinum-toxin arm. This divergence makes it important to consider the outcomes together rather than treating the primary finding as a complete account of participants’ experience.

Satisfaction is not interchangeable with the number of days meeting the pain-decrease criterion. It may reflect aspects of treatment experience or expectations that the primary endpoint does not capture, but the registry record does not describe what influenced satisfaction or how it was assessed. The two outcomes therefore address related but distinct questions, and one cannot be used as a direct validation of the other.

The secondary result should be interpreted cautiously. The registry posts one secondary outcome, and the method listed is Fisher Exact. The original hierarchy of outcomes and any planned adjustment for multiple comparisons are not reported in the registry record. When multiple outcomes or tests are considered, unadjusted results can overstate the strength of evidence because they do not account for the number of opportunities to observe an apparently notable finding.

The contrast between the endpoints does not by itself explain why participants’ reported satisfaction differed from the primary outcome pattern. Nor does it establish that one outcome is more reliable. The secondary analysis is best treated as additional, exploratory context, with less inferential weight than a clearly prespecified and multiplicity-controlled confirmatory endpoint.

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

• Number of Participants Satisfied With Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a count of days summarized as a mean. A comparison of two independent group means asks whether the average outcome differs between the randomized arms. The registry reports a two-sided t-test. A two-sided test considers departures in either direction rather than testing only whether one arm has a larger mean. The registry does not report further details of the t-test implementation, such as whether equal variances were assumed.

What does the mean difference express?

The mean difference is calculated as the botulinum-toxin mean minus the placebo mean. A positive value therefore means the posted average number of decreased-pain days is higher in the active arm. The estimated mean difference is 7.47 days. This is an absolute difference in the endpoint’s units, not a percentage change, and it does not describe the experience of every participant.

Each arm’s standard deviation describes the variability of participant outcomes within that arm. The reported standard deviations, 5.63 for placebo and 8.18 for botulinum toxin, are sizeable relative to their corresponding means. This indicates that outcomes were not tightly clustered around the group averages. In small samples, variation and the influence of individual observations can make estimates unstable.

How should the p-value be read?

A p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The recalculated unadjusted p-value is 0.017. The registry reports a two-sided t-test result with a different, larger p-value. Neither result resolves questions about measurement, missing outcomes, analysis populations, or whether the finding would be reproduced.

The recalculated comparison uses posted group summaries rather than individual participant records. It is a simple unadjusted re-calculation, so it cannot account for covariates or analysis procedures that are not represented in those summaries. The registry does not report an adjusted primary analysis. The fact that no discrepancy is flagged does not mean that the two p-values are identical; the reported result and the recalculated result should remain distinguishable.

Why can over-dispersion matter?

As a general statistical concept, over-dispersion means that observed variability is greater than a model expects. Greater variability makes estimates less precise and can affect standard errors and tests if a method assumes less variation than the data contain. For a continuous mean outcome, the standard deviations provide a direct description of spread, although the registry record does not label the outcome as over-dispersed. Here, the reported variability and small arm counts are reasons to avoid treating the point estimate as highly precise.

For a binary outcome, a risk difference expresses the difference between the proportions meeting an outcome in two groups. The secondary satisfaction comparison is binary, with the registry reporting Fisher Exact as its test. Fisher’s exact test is often used for small samples because it calculates significance using the discrete possible allocations under the null model rather than relying on a large-sample approximation. The registry does not report a multiplicity adjustment for this secondary comparison.

What does a confidence interval add?

As a general statistical concept, a confidence interval gives a range of values compatible with the data and the assumptions used to calculate it. Its width conveys precision: a wider interval leaves more uncertainty about the size of the underlying difference. A 95% confidence interval is not a probability statement that the true value lies in this particular interval. It describes the behavior of the method over repeated samples under its assumptions. The primary interval spans 1.315 to 13.62 days, reflecting substantial uncertainty about the magnitude even though the interval lies above zero.

The registry’s original statistical plan, including any planned covariate adjustment, missing-data procedures, interim analyses, or multiplicity control, is not reported in the registry record. Those details should not be inferred from the tests listed for the posted results.

11. Confidence Intervals and Precision

The primary mean difference is 7.47 days, with a 95% confidence interval from 1.315 to 13.62 days. The interval’s endpoints are both above zero, so the range of values compatible with this unadjusted calculation favors a higher mean number of decreased-pain days in the botulinum-toxin arm. The interval is nevertheless wide: it allows for a comparatively modest difference as well as a much larger one. It does not identify a single precise effect size.

A confidence interval combines the estimated difference with uncertainty arising from sampling variability, under the calculation’s assumptions. It is not a range containing every participant’s outcome, and it does not mean there is a 95% probability that the true difference falls between the endpoints. In repeated use, a 95% interval procedure would cover the target value in 95% of intervals if its assumptions held.

Precision is limited by the small primary-outcome counts: 10 participants are listed in each arm. The standard deviations are 5.63 and 8.18, indicating substantial variation in individual outcomes. Both features contribute to uncertainty around the mean difference. The posted summary does not provide individual values or enough information to examine the influence of particular observations.

The interval is an unadjusted re-calculation from posted summary statistics. The registry record gives no confidence interval for its own reported t-test. The recalculated interval should therefore be read as a transparent summary-statistic estimate, not as confirmation of an undocumented analysis plan. It also does not account for uncertainty arising from unreported features such as missing-data handling or outcome selection.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrative calculations based on the observed effect, not the trial’s original design. For the continuous primary outcome, the figures are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The original trial’s design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting the selected effect under those assumptions. The 90% power column gives the corresponding estimate for a 90% chance. These are planning targets under a model, not guarantees for a future study. For the primary outcome, the illustrations range from 14 participants per arm when planning for 100% of the observed effect to 56 per arm when planning for 50% of it for 80% power. The corresponding 90% figures range from 19 to 75 participants per arm.

The same planning approach is also shown for the binary satisfaction outcome, where the figures are participants per arm rather than total events. Smaller effects need more participants to detect, all else equal. The sample-size illustrations are not observed power; they do not tell how likely this completed trial was to detect an effect after its results were known. They should be read as planning illustrations tied to the observed estimates, which may themselves be unstable in a small trial.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 7.470; pooled standard deviation σ = 7.022.
2. n = 2 × (1.96 + 0.842)² × 7.022² / 7.470² = 13.9, rounded up to 14 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
delta <- 7.47                      # observed difference in means
sigma <- 7.02172699554746                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(660192)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 14 (80% power), 19 (90% power)
 75% of observed effect: n per arm = 25 (80% power), 34 (90% power)
 50% of observed effect: n per arm = 56 (80% power), 75 (90% power)
power.t.test: 14.9 
Simulated power at n = 14 per arm: 0.776 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 reports a two-sided t-test for the primary comparison. Its p-value is larger than the unadjusted p-value recalculated from the posted arm summaries, but both calculations indicate the same direction for the mean difference. The registry does not give the test statistic, confidence interval, or explanation for the difference between the two p-values.

The recalculation uses only the posted means, standard deviations, and arm counts. It is a simple unadjusted analysis and may not reproduce details of the sponsor’s analysis that are not described in the record. No discrepancy is flagged in the registry data. Even so, the sponsor’s reported analysis remains the trial’s own analysis; a summary-statistic recalculation is best understood as a separate check, not a replacement for a documented analysis of participant-level data.

For the secondary satisfaction outcome, the registry reports Fisher Exact. That reported test also differs from the unadjusted recalculation, and the registry does not provide a confidence interval for its analysis. The analysis methods and p-values should be interpreted alongside the missing information about analysis populations, missing data, and multiplicity rather than treated as complete evidence of a prespecified statistical plan.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and one secondary outcome, but the planned approach to testing multiple outcomes is not reported in the registry record. It is therefore unknown whether the trial specified a hierarchy, adjusted significance thresholds, or another multiplicity procedure. Unadjusted p-values for separate outcomes do not account for the possibility of chance findings arising across multiple tests. This limits how strongly the secondary result can be interpreted and is relevant to the overall pattern of evidence.

The record also does not report how missing primary or secondary outcome data were handled. It does not state whether all randomized participants were included in the analyses, whether any outcomes were imputed, or whether analyses followed an intention-to-treat principle. The primary outcome counts are 10 per arm, while the total enrollment is 25 and the safety at-risk counts are 12 and 13. The reasons for these differences are not reported in the registry record; the counts alone do not establish whether data were missing or how participants were analyzed.

Analysis populations are not described in enough detail to determine whether the reported outcome sets represent all randomized participants, participants who completed follow-up, or another defined group. The registry also does not describe exclusions after randomization or the handling of protocol deviations. These omissions matter because analysis choices can affect estimated treatment differences, particularly when the study is small.

Interim analyses, stopping rules, covariate adjustment, and the full prespecified statistical analysis plan are not reported in the registry record. Their absence from the record should not be interpreted as evidence that such procedures were or were not used. Without those details, the posted analyses can be described, but their relationship to the original plan cannot be fully assessed.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The safety record lists serious adverse events for 12 participants at risk in the saline group and 13 in the Botox group. It records zero participants affected by a serious adverse event in each group. No serious adverse-event terms are listed. The record does not provide a death count; deaths are not reported in the registry record.

These figures describe what the registry reports for the listed at-risk groups. They do not prove that serious harms are impossible or that the groups have equivalent safety. With a small number of participants, uncommon events may not appear in the observed record, and estimates of event frequency would be imprecise. The safety denominators also differ from the primary outcome denominators, and the reason is not reported in the registry record.

For other adverse events, the registry records zero affected participants among 12 at risk for saline and one among 13 at risk for Botox. These are descriptive counts, not a comprehensive assessment of all possible harms. The registry record does not provide further detail on event severity or timing.

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

The posted primary results show a higher mean number of days with decreased pain in the botulinum-toxin arm than in the placebo arm during the 4-week timeframe. The estimated difference is 7.47 days, with a 95% confidence interval from 1.315 to 13.62 days. The uncertainty interval and small arm counts are central to interpretation: the data support a range of possible effect sizes, not a precise prediction for an individual or a future trial.

The result does not establish that the observed difference is clinically important. The registry does not state a threshold for a clinically meaningful difference, and the endpoint is not the same as a direct count of migraine attacks. The record’s summary mentions a 50% reduction as the study hypothesis, but the posted endpoint results do not establish that the hypothesis was achieved in a prespecified way.

The secondary satisfaction pattern differs from the primary outcome pattern. That contrast, together with unreported multiplicity and analysis details, argues against relying on a single statistic as a complete account of the trial. The sponsor’s two-sided t-test is the reported trial analysis; a separate unadjusted recalculation gives a different p-value and should not be mistaken for a replacement analysis.

The safety record reports no serious adverse events in the listed groups, but the participant counts are small and do not rule out uncommon events. The registry record does not report enough detail to establish how all enrolled participants contributed to the efficacy and safety analyses.

These results describe one completed trial in participants with refractory migraine. They do not, by themselves, establish a general treatment effect, resolve uncertainty about replication, or support medical advice. Broader conclusions would require consideration of the study’s full methods and other relevant evidence, which are not described in this record.

18. Why This Trial Matters Statistically

This trial illustrates why a difference in group means and the precision of that difference should be read together. The primary estimate is 7.47 days, but its 95% confidence interval extends from 1.315 to 13.62 days. The interval communicates uncertainty about magnitude that a point estimate alone conceals. The standard deviations and the 10 participants per arm listed for the primary outcome further show why a large-looking estimate should not be treated as exact.

It also illustrates the distinction between a trial’s reported analysis and a transparent recalculation from summary statistics. The registry reports a two-sided t-test, while the unadjusted recalculation produces a different p-value. Keeping these results distinct helps readers assess what the registry actually reports and what can be reconstructed from group summaries without implying that the reconstruction reproduces every feature of the original analysis.

The secondary outcome adds an important interpretive check because its overall direction is not consistent with the primary endpoint. Multiple outcomes can illuminate different aspects of a study, but unadjusted testing and an unreported analysis plan limit the strength of conclusions drawn from secondary results. This is a statistical interpretation issue, not a reason to select whichever outcome appears most persuasive.

Finally, the record shows why enrollment, outcome counts, and safety denominators should not be treated as interchangeable. Their differences are visible, but the reasons and analysis populations are not documented. Such gaps are important when evaluating precision, missing-data risk, and the reach of trial conclusions.

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.

The primary comparison is based on 10 participants in each arm, despite total enrollment of 25. The registry does not explain the difference. Safety denominators are 12 and 13, and the reason those differ from the primary outcome counts is also not reported in the registry record. Without an account of participant flow and analysis populations, it is not possible to establish how the reported results relate to all enrolled or randomized participants.

The primary endpoint counts days meeting a threshold for decreased pain, but the record does not describe the assessment schedule, data collection procedures, or handling of incomplete daily measurements. The outcome is reported as a mean and standard deviation; individual-level distributions are not available in the registry record. The relatively small arm counts and substantial standard deviations limit precision and make the summaries sensitive to individual observations.

The registry does not report the original sample-size justification, full statistical analysis plan, multiplicity approach, missing-data procedures, interim analyses, or details of allocation concealment and masking. It also does not report a primary confidence interval from the sponsor’s analysis. These omissions prevent a full assessment of prespecification and robustness.

The study concerns refractory migraine and reports a 4-week primary outcome timeframe. The registry record does not provide participant characteristics beyond the condition that would help assess applicability to other groups, nor does it report longer-term outcome results. The safety record has small at-risk groups, no serious events recorded, and no reported death count. It cannot exclude uncommon harms.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Investigation of Efficacy and Safety of Botulinum Toxin A (Botox-Allergan Inc) in Migraine Headaches — NCT00660192.
• Registry record last updated 2016-03-14; status last verified 2016-02.
• Results first posted 2016-03-14.
• 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

NCT00660192 is a completed randomized, double-masked, parallel-group Phase 2 and Phase 3 study sponsored by Yale University. It enrolled 25 participants with refractory migraine and compared Botox, described as onabotulinumtoxinA, with inactive saline.

The primary endpoint was the mean number of days with decreased pain over 4 weeks, defined as a decrease of 2 grades or more on the Visual Analog Scale. The posted primary outcome lists 10 participants per arm. Its unadjusted mean difference is 7.47 days, with a 95% confidence interval from 1.315 to 13.62 days and an unadjusted p-value of 0.017. The registry reports a two-sided t-test with a different p-value.

One secondary outcome concerns satisfaction with treatment. The safety record lists zero serious adverse events in both groups. Important details about missing data, analysis populations, multiplicity, and the original sample-size justification are not reported in the registry record.