Safety and Efficacy of Two Types of Botulinum Toxin Type A For the Treatment of Glabellar Lines: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Two Types of Botulinum Toxin Type A For the Treatment of Glabellar Lines (NCT01271452), a randomized phase 4 study. The primary outcome is Number of Subjects With a Treatment Response at Day 28 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the Facial Wrinkle Scale (FWS).

2. Clinical Question

The study description identifies the purpose as evaluating the safety and efficacy of two types of botulinum toxin type A for glabellar frown lines. The primary outcome focuses on the injector’s assessment of wrinkle severity at maximum contraction. A response is a change from each subject’s Day 0 score, rather than simply having a particular score at the follow-up visit.

The registry record also lists secondary questions about injector assessments at later visits and subject assessments at several visits. Those outcomes broaden the questions beyond the primary Day 28 injector assessment, but the registry record does not report numerical results for every listed secondary outcome. The central comparison is between the named products; no placebo or untreated comparison is described.

3. Trial Design

The registry identifies this as a phase 4, randomized, quadruple-masked, parallel-group study. The planned enrollment was 224. The two arms were Vistabel® and Bocouture®, both described as botulinum toxin type A. The registry record marks the study as completed.

The listed study start was 2010-09 and the primary completion date was 2011-01. These dates describe the registry record and do not provide details about the timing of each participant’s treatment or follow-up. The record does not describe the randomization procedure, how masking was maintained, or which roles were included in the term “quadruple.” Those details are not reported in the registry record.

The primary outcome population is the intent-to-treat population, defined as all randomized subjects. Each arm’s primary outcome count is reported with 112 subjects. The primary outcome is a binary response: a subject either met the stated response definition at Day 28 or did not. The registry also lists seven secondary outcomes, including injector assessments at later visits and subject assessments. Numerical secondary results are posted for injector-assessed outcomes at Day 84, Day 98, and Day 112.

The registry record does not report the trial’s original sample-size justification, a statistical analysis plan, the details of allocation concealment, or procedures for handling missing outcome data. It also does not provide information on adherence, withdrawals, or participant flow. The design labels and reported counts therefore describe the structure and posted results, but do not fill in those methodological details.

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

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT): all randomized subjects.

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 Number of Subjects With a Treatment Response at Day 28 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the Facial Wrinkle Scale (FWS), measured over Day 28.

The primary endpoint is the number of subjects with a treatment response at Day 28, based on the injector’s assessment of glabellar-line severity at maximum contraction using the Facial Wrinkle Scale (FWS). The FWS runs from 0, meaning no wrinkles, to 3, meaning severe wrinkles. A treatment response was defined as a reduction of at least 1 point from the subject’s Day 0 FWS score at maximum contraction.

This endpoint turns a change in an ordinal wrinkle-severity score into a binary outcome: the subject meets the response definition or does not. Counting responders makes the result interpretable as the frequency of meeting a prespecified threshold, rather than as an average score change. It also makes clear that a response requires improvement relative to that subject’s starting score, not merely a low score at follow-up.

In general, a threshold-based endpoint can be useful when a study seeks to describe how often participants achieve a defined degree of change. It also discards information: subjects just below and well below the threshold are both classified as nonresponders, while differing amounts of improvement above the threshold are grouped as responses. The registry record does not report a justification for choosing this threshold or additional details about how the FWS was administered.

7. Results Posted in the Registry

• Bocouture®: 94.6% (106/112) versus 96.4% (108/112) on control; risk difference -1.8 percentage points (95% CI -7.2 to 3.6), risk ratio 0.98 (0.93–1.04); unadjusted two-proportion z-test p = 0.518.

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 Subjects With a Treatment Response at Day 84 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS

• 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:
  • Bocouture®: 71.4% (80/112) versus 80.4% (90/112) on control; risk difference -8.9 percentage points (95% CI -20.1 to 2.2), risk ratio 0.89 (0.77–1.03); unadjusted two-proportion z-test p = 0.118.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bocouture® and the control. The interval gives the range of effects that remain compatible with the data.

Number of Subjects With a Treatment Response at Day 98 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS

• 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:
  • Bocouture®: 62.5% (70/112) versus 67.9% (76/112) on control; risk difference -5.4 percentage points (95% CI -17.8 to 7.1), risk ratio 0.92 (0.76–1.12); unadjusted two-proportion z-test p = 0.400.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bocouture® and the control. The interval gives the range of effects that remain compatible with the data.

Number of Subjects With a Treatment Response at Day 112 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS

• 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:
  • Bocouture®: 50.0% (56/112) versus 54.5% (61/112) on control; risk difference -4.5 percentage points (95% CI -17.5 to 8.6), risk ratio 0.92 (0.71–1.18); unadjusted two-proportion z-test p = 0.504.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bocouture® and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question beyond Day 28 and include both injector and subject assessments. Numerical posted results are available for the injector-assessed response outcomes at later visits. Across those follow-up comparisons, the observed risk-difference estimates are below zero for Bocouture® relative to Vistabel®, while the confidence intervals include zero. This is a directional pattern in the posted estimates, not a definitive demonstration of a difference.

That pattern is broadly consistent with the primary point estimate, which is also below zero, but it does not change the primary result’s uncertainty. Later measurements address response at different times, and they should not be treated as independent replications of the primary endpoint without knowing the analysis plan and the relationship between repeated assessments. They also do not establish that the products differ in a way that is clinically important.

The registry lists subject-assessed response outcomes at Day 28, Day 84, Day 98, and Day 112, but numerical results for those outcomes are not reported in the registry record. Their direction and precision therefore cannot be evaluated from the posted numeric results. The listed outcomes should not be mistaken for findings when their counts and comparisons are absent.

Secondary results generally carry less weight than a prespecified primary result because there may be multiple opportunities to find an apparently notable result, especially when outcomes, timepoints, and assessors vary. Unadjusted secondary p-values, where available, do not account for that multiplicity. The registry record does not report a multiplicity strategy, so the secondary findings are best read as supportive descriptive evidence rather than as stand-alone confirmatory conclusions.

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

• Number of Subjects With a Treatment Response at Day 84 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS
• Number of Subjects With a Treatment Response at Day 98 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS
• Number of Subjects With a Treatment Response at Day 112 Based on the Injector's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS
• Number of Subjects With a Treatment Response at Day 28 Based on the Subject's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS
• Number of Subjects With a Treatment Response at Day 84 Based on the Subject's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS
• Number of Subjects With a Treatment Response at Day 98 Based on the Subject's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS
• Number of Subjects With a Treatment Response at Day 112 Based on the Subject's Assessment of the Severity of Glabellar Lines at Maximum Contraction Using the FWS

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference express?

For a binary outcome, a risk difference compares the proportion with the outcome in one group with the proportion in the other. Here, the comparison is Bocouture® relative to Vistabel®. A value below zero indicates a lower observed response proportion in the Bocouture® group; a value above zero indicates a higher observed response proportion. A value of zero represents no difference in the observed proportions.

The primary estimate is -0.018. This is a difference on the proportion scale, not a difference in the raw number of subjects. The comparison is based on the posted responder counts and denominators. In general, a risk difference is often useful because it describes an absolute contrast between groups. It remains specific to the outcome definition and follow-up time used in the comparison.

How should the confidence interval be understood?

A confidence interval expresses uncertainty around an estimate. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. The primary interval runs from -0.072 to 0.036. Because it includes zero, the posted data do not distinguish clearly between a negative contrast, no contrast, and a positive contrast at the confidence level represented by the interval.

The interval is not a range in which the true effect is guaranteed to fall, and it does not give the probability that the true effect equals a particular value. It is a way to show how much uncertainty remains under the statistical method used. The registry record does not describe the method used to construct the interval, so its technical assumptions cannot be checked from the record.

What does the unadjusted p-value say?

The primary unadjusted p-value is 0.518. In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. “Unadjusted” means the value is not reported as corrected for multiple comparisons.

The registry record does not report a statistical analysis plan or the details of the test underlying the p-value. The p-value should therefore be read alongside the estimated risk difference, the confidence interval, the responder counts, and the limits of the registry’s analytic reporting. A p-value alone cannot establish sameness, equivalence, or the absence of a meaningful difference.

Why do binary outcomes lose information?

The endpoint converts a change on the FWS into a responder or nonresponder classification using a reduction of at least 1 point. In general, this can make a result easier to communicate as a count, but it does not preserve every detail of score change. The endpoint does not distinguish between different amounts of improvement among responders, and it groups all subjects who do not meet the threshold together. The registry record does not post the underlying score distributions, so those changes cannot be assessed from the responder counts.

Why can over-dispersion matter in other outcome types?

Over-dispersion is a general issue for count outcomes when observed variability exceeds what a simple statistical model expects. It can make standard errors too small if the extra variability is ignored. The primary endpoint is a binary responder outcome, not a count of repeated events per subject, and the record does not report a dispersion estimate or over-dispersion adjustment. The concept is relevant to statistical methods generally, but the registry record does not indicate that over-dispersion was part of this trial’s primary analysis.

What analysis details remain unknown?

The registry record does not report the exact statistical test, covariate adjustment, handling of missing outcomes, or a multiplicity strategy. It also does not report whether an interim analysis was planned or conducted. Those items should not be inferred from the randomized design or from the posted p-value. The posted comparison is unadjusted, and no reported analysis entries give further detail about the sponsor’s analysis methods.

11. Confidence Intervals and Precision

The primary risk difference is -0.018 for Bocouture® relative to Vistabel®, with a 95% confidence interval from -0.072 to 0.036. This interval crosses zero. It therefore includes values consistent with a lower response proportion in the Bocouture® arm, no difference, and a higher response proportion. The range is broad enough that the point estimate alone should not be treated as a precise description of the underlying contrast.

At the observed group sizes, the primary counts were 108 of 112 responders for Vistabel® and 106 of 112 for Bocouture®. The closeness of the counts does not remove sampling uncertainty. A confidence interval is useful because it places the estimate in context: it shows that the posted results are compatible with a range of possible contrasts, rather than identifying one exact effect.

Precision is not the same as whether a result crosses a conventional significance threshold, and it is not a measure of clinical importance. No threshold for a clinically important risk difference is reported in the registry record. The interval also does not establish equivalence: that would require an appropriate design and a prespecified margin, neither of which is reported.

For the later injector-assessed outcomes, the posted confidence intervals also include zero. Those results are less conclusive about the direction and size of the group contrast. The registry record does not post confidence intervals for every listed secondary outcome, including the subject-assessed outcomes, so their precision cannot be judged from the available numerical results.

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 stated as participants per arm, not as a total across the two arms and not as total events. The illustration assumes a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. It uses the observed effect as its reference and shows planning for 100%, 75%, or 50% of that observed effect.

The 80% power column describes the number of participants per arm that a hypothetical study would require, under those assumptions, to have an 80% chance of detecting the stated effect if that effect were the true one. The 90% power column uses the same idea with a higher chance of detection, which generally requires more participants per arm. These values are planning illustrations, not reconstructions of the trial’s original design. The original design assumptions and sample-size justification are not reported in the registry record.

As the effect to be detected becomes smaller, more participants are needed to distinguish it from random variation under the stated assumptions. For example, the planning row for 50% of the observed effect requires more participants per arm than planning for the full observed effect. This is not observed power: it does not describe the probability that the completed trial detected an effect, and it should not be used to reinterpret the trial’s result as having succeeded or failed.

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 = 0.964; treatment proportion p₁ = 0.946; average p̄ = 0.955.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2921 = 0.5724.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2918 = 0.2456.
4. n = (0.5724 + 0.2456)² / (-0.0179)² = 2,098.4, rounded up to 2,099 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 <- 0.964285714285714                          # control proportion
p1 <- 0.946428571428571                          # 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(1271452)
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 = 2,099 (80% power), 2,809 (90% power)
 75% of observed effect: n per arm = 3,554 (80% power), 4,757 (90% power)
 50% of observed effect: n per arm = 7,593 (80% power), 10,164 (90% power)
power.prop.test: 2098.4 
Simulated power at n = 2,099 per arm: 0.808 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and seven secondary outcomes. The secondary outcomes cover multiple follow-up times and include assessments by both the injector and the subject. Considering multiple outcomes raises a general statistical concern: the more comparisons examined, the greater the chance that some will appear notable by chance, even if there is no underlying group difference for those outcomes.

The registry record does not report a plan for controlling multiplicity, such as prioritizing secondary outcomes, adjusting significance thresholds, or treating secondary results as exploratory. The posted primary p-value is identified as unadjusted, and the secondary comparison results are also presented as unadjusted. Without a reported plan, the strength of evidence from the collection of comparisons is difficult to assess. A pattern across related outcomes may be informative, but it does not remove the uncertainty created by multiple testing.

The record defines the primary outcome population as intent-to-treat, meaning all randomized subjects. That definition is important because it identifies the intended population for the primary endpoint. However, the registry record does not report how missing Day 28 assessments were handled, whether all randomized subjects had outcome data, or whether any imputation or sensitivity analyses were used. It also does not explain the handling of missing secondary assessments.

The registry record does not report an analysis plan, analysis entries, interim analyses, or details of the statistical tests. It is therefore not possible to determine from the record whether the posted analyses follow a prespecified hierarchy, whether adjustments were made outside the displayed unadjusted comparisons, or whether the reported outcomes were selected from a broader set. These are reporting gaps, not evidence that a particular method was or was not used.

15. 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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse event figures of 0 for Vistabel® among 112 at risk and 0 for Bocouture® among 111 at risk. These entries indicate that no serious adverse events are recorded in either group in the posted safety summary. They do not establish that the risk of a serious event is zero, particularly because adverse-event counts from a trial are estimates based on the observed participants and follow-up.

The posted figures for other adverse events are 6 for Vistabel® among 112 at risk and 2 for Bocouture® among 111 at risk. The registry record does not provide further event descriptions in the listed serious-event terms, nor does it report deaths for either group. Death information is not reported in the registry record.

These figures are descriptive. The record does not provide a comparative safety analysis, confidence intervals, severity details for other adverse events, or information about how long each participant was followed for safety. The counts should not be interpreted as establishing a safety advantage for either product.

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

The primary result describes the Day 28 frequency of meeting a defined injector-assessed response threshold in two randomized groups. The observed counts were close, and the estimated risk difference was -0.018 for Bocouture® relative to Vistabel®. The 95% confidence interval, from -0.072 to 0.036, includes zero and allows for contrasts in either direction. The posted result is therefore uncertain about the size and direction of the underlying difference.

This does not show that the products are identical. A failure to distinguish a difference in a particular comparison is not the same as evidence of equivalence. The registry record does not report an equivalence or non-inferiority margin, and the interval is not assessed against such a margin. It also does not establish that either product is effective or ineffective in every setting; the posted outcome is limited to the trial’s definition, assessment method, and follow-up.

The endpoint is a threshold-based response on the FWS at maximum contraction. It does not capture every possible change in wrinkle severity, patient experience, duration of response, or other clinical outcome. The registry lists subject-assessed outcomes, but their numerical results are not reported in the registry record. The posted primary result should not be generalized to those unreported outcomes.

The safety summary records no serious adverse events in either group and reports other adverse-event figures, but it does not provide a detailed comparative safety analysis. These entries cannot establish that an event cannot occur or that one product has a safer profile. The record also lacks details about missing data, the statistical analysis plan, and the handling of multiple outcomes. Those gaps constrain how far the findings can be interpreted beyond the specific posted comparisons.

In general, statistical evidence is one part of evaluating a clinical question. The registry results describe observed data and uncertainty; they do not provide medical advice or determine an individual treatment choice.

17. Why This Trial Matters Statistically

This trial offers a randomized head-to-head comparison of two named botulinum toxin type A products, rather than a comparison with no treatment. Randomization can support a fairer group comparison by reducing systematic differences at allocation, although the registry record does not describe the randomization method or how it was implemented. The parallel-group and quadruple-masked labels provide useful design context, while leaving some procedural details unreported.

The primary endpoint is clearly framed as a responder count at a specified visit and uses a stated threshold based on change from Day 0. That clarity helps readers understand what the result represents. At the same time, the risk difference and its confidence interval show why an observed comparison should not be reduced to a single point estimate or p-value: the estimate is uncertain, and the interval includes values on both sides of no difference.

The record also illustrates the difference between a primary endpoint and a wider collection of secondary questions. Later visits and another assessor can add context, but multiple unadjusted comparisons require caution. The absence of a reported analysis plan, multiplicity strategy, and missing-data procedures makes it harder to judge how firmly the full set of results supports any conclusion.

Finally, the planning illustration shows how sample-size requirements depend on the effect a future study aims to detect. Those figures are not evidence about the probability that this completed trial found an effect. Keeping planning calculations separate from observed results is important when interpreting modest group contrasts and their uncertainty.

18. 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 registry record gives limited methodological detail beyond the randomized, quadruple-masked, parallel design. It does not report the randomization procedure, masking procedures, allocation concealment, statistical analysis plan, or the trial’s original sample-size justification. These omissions make it difficult to evaluate design and analysis decisions in detail.

The primary result is a binary response measure based on a reduction of at least 1 point on the FWS. The registry record does not report the baseline score distribution, the full score changes, or a justification for the response threshold. As a result, the posted responder counts cannot show how much subjects improved or how scores were distributed within each response category.

Although the primary population is defined as all randomized subjects, missing outcome handling and participant flow are not reported. Numerical results are also absent for the listed subject-assessed secondary outcomes. The record lists outcome timepoints through Day 112 but does not provide longer-term outcome information in the posted results. A multiplicity strategy is not reported, and the comparisons are unadjusted.

The safety summary provides event figures but not detailed event descriptions, severity information for other adverse events, comparative estimates, or deaths. The record does not report deaths, so no conclusion about the death count can be made. These limitations are specific to the information available in the registry record and should be kept separate from conclusions that might be supported by additional reports.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of Two Types of Botulinum Toxin Type A For the Treatment of Glabellar Lines — NCT01271452.
• Registry record last updated 2019-01-29; status last verified 2019-01.
• Results first posted 2012-01-16.
• 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.

22. Record Summary

The registry record describes a completed randomized phase 4 parallel-group comparison of Vistabel® and Bocouture® for glabellar lines. It lists quadruple masking and planned enrollment of 224, with a study start of 2010-09 and primary completion of 2011-01.

The primary outcome is the number of subjects with an injector-assessed response at Day 28, defined as a reduction of at least 1 point from Day 0 on the FWS at maximum contraction. The posted counts were 108 of 112 for Vistabel® and 106 of 112 for Bocouture®. The risk difference for Bocouture® relative to Vistabel® was -0.018, with a 95% confidence interval from -0.072 to 0.036.

The record lists seven secondary outcomes, with numerical results posted for three later injector-assessed outcomes. It does not report the statistical analysis plan, multiplicity strategy, or missing-data methods. Safety figures record no serious adverse events in either group; the available safety summary is descriptive.