Efficacy and Safety of Clostridium Botulinum Toxin Type A to Improve Appearance of Moderate to Severe Glabellar Lines: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Clostridium Botulinum Toxin Type A to Improve Appearance of Moderate to Severe Glabellar Lines (NCT02353871), a randomized phase 3 study. The primary outcome is The Proportion of Responders at Day 29 in the ILA of Glabellar Lines at Maximum Frown..

2. Clinical Question

The clinical question is about a defined assessment and time point, not about every possible change in facial appearance or the duration of any change. The study also lists secondary assessments, including assessments at rest, participant self-assessment, satisfaction, and time to response. Their presence broadens the questions considered, but does not change the definition of the primary endpoint.

3. Trial Design

The registry record describes a phase III, randomized, double-blind, parallel-group, placebo-controlled study. It was sponsored by Ipsen and is marked completed. The stated enrollment was 185. The registry record lists a study start of 2015-01 and a primary completion of 2015-04.

The study compared a single treatment of BTX-A-HAC Next Generation with placebo. Both were administered as intramuscular injections at five predefined sites across the glabellar region. The active treatment is described as a 50 U solution in a total volume of 0.25 mL; the placebo volume was also 0.25 mL. The registry record does not report further details about how randomization was generated, how allocation was concealed, or how blinding was maintained.

The primary endpoint was assessed on Day 29. The main reported analysis used adjusted responder percentages for the modified intent-to-treat population. That population is described as randomized participants who received at least one injection into an injection site and had baseline and at least one postbaseline value for the investigator’s assessment at maximum frown. The population description in the registry record is incomplete, so additional handling rules are not reported in the registry record.

The primary efficacy groups are listed with 124 participants for BTX-A-HAC Next Generation and 58 for placebo. The adverse-event groups use different at-risk counts, which are reported separately with the safety information. These analysis counts should not be treated as interchangeable: the record gives specific populations for different outcomes. The original sample-size justification and design assumptions are not reported in the registry record. The planning illustrations associated with the posted summary statistics are not a substitute for those original design 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.

Before assignment: Overall, 190 subjects were screened, five of whom were screening failures. A total of 185 subjects were randomised to receive treatment. One of the subjects who was randomised to placebo did not receive study treatment due to violation of inclusion criterion 3.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat (mITT) population included all randomised subjects who received at least one injection of study treatment into one injection site and who had both Baseline and at least one postbaseline value for the ILA of glabellar lines at maximum frown. Subjects who did not have available data at Day 29 were excluded from the analysis.

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: Randomised population.

6. Primary Endpoint

The registry lists the primary outcome as The Proportion of Responders at Day 29 in the ILA of Glabellar Lines at Maximum Frown., measured over Day 29.

The primary endpoint is the proportion of responders at Day 29 on the investigator’s assessment of glabellar lines at maximum frown. The assessment uses a 4-point photographic scale: none, Grade 0; mild, Grade 1; moderate, Grade 2; and severe, Grade 3. A responder had a severity grade of none or mild at maximum frown on Day 29, while having a moderate or severe grade at baseline.

This definition requires both a post-treatment status and a baseline status. It therefore does not simply count everyone whose Day 29 appearance was rated none or mild; the baseline grade is part of the responder rule. The endpoint turns an ordinal assessment into a binary outcome: each participant either meets the specified responder definition or does not. The reported group result is an adjusted percentage of responders.

As a general statistical point, a binary responder endpoint can be easy to communicate because it describes the proportion meeting a prespecified threshold. It also compresses information: two people with different degrees of improvement may both count as responders, while a person just outside the threshold counts as a nonresponder. The endpoint is useful for answering the particular threshold-based question chosen for the study, but it does not capture every feature of the underlying severity scale.

The registry record says the adjusted proportions were estimated using a multivariate logistic regression model. The covariates and other details of that model are not reported in the registry record. The endpoint should consequently be read as a result for this assessment, responder definition, analysis population, and time point rather than as a general measure of all outcomes.

7. Results Posted in the Registry

• BTX-A-HAC NG Solution (50 U): 87.9% (109/124) versus 1.7% (1/58) on control; risk difference 86.2 percentage points (95% CI 79.5 to 92.8), risk ratio 50.98 (7.30–356.24); 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.

The Time to Onset of Treatment Response Based on the Subject's Diary Card.

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Cox proportional hazard model); it was not recalculated.
• Result:
  • BTX-A-HAC NG Solution (50 U) vs Placebo: hazard ratio 6.56, reported p < 0.001 (as reported in the registry).
• Interpretation:
  • The posted data give a point estimate for BTX-A-HAC NG Solution (50 U) vs Placebo but no confidence interval, so the precision of the comparison cannot be judged.

The registry identifies secondary questions covering responder status at other visits, persistence of response, assessments at rest, changes of two or more severity grades, participant self-assessment, satisfaction, and time to onset. These outcomes are related to the primary Day 29 investigator assessment, but they measure different dimensions or use different time points and instruments. They can add context about the breadth and timing of outcomes considered.

The detailed secondary results available in the registry record concern time to onset based on the participant’s diary card. The remaining secondary outcome results are not reported in the registry record. As a result, the record does not establish a consistent pattern across the full set of secondary measures, and the primary finding cannot be assumed to apply to each one.

Secondary outcomes are often interpreted with more caution when many outcomes or repeated assessments are examined. As a general statistical point, testing multiple outcomes increases the chance that at least one result will appear statistically notable by chance if no adjustment is made. The registry record does not report a multiplicity adjustment for the secondary analyses, so their p-values should not be read as if they necessarily controlled the overall false-positive risk across all secondary questions.

The secondary measures are useful for describing questions beyond the primary endpoint, but they do not replace it. The primary endpoint was defined in advance in the record as the Day 29 responder proportion at maximum frown. Missing results for other secondary measures limit assessment of whether findings were consistent across visits, assessment settings, and participant-reported outcomes. The registry record does not report enough information to resolve that limitation.

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

• The Proportion of Responders at Each Post-treatment Visit to the Study Centre (Except Day 29) as Measured by the ILA at Maximum Frown.
• The Proportion of Responders on Day 29 Who Remained Responders on Days 57, 85, 113, 148 and 183 as Measured by the ILA at Maximum Frown.
• The Proportion of Responders at Each Post-treatment Visit to the Study Centre as Measured by the ILA at Rest.
• The Proportion of Subjects With a Reduction of Two or More Grades in the Severity of Glabellar Lines at Each Post-treatment Visit to the Study Centre as Measured by the ILA at Maximum Frown.
• The Proportion of Responders at Each Post-treatment Visit to the Study Centre as Measured by the Subject's Self-assessment (SSA) at Maximum Frown.
• The Proportion of Responders at Each Post-treatment Visit to the Study Centre as Measured by the Subject's Level of Satisfaction With the Appearance of Their Glabellar Lines.
• The Time to Onset of Treatment Response Based on the Subject's Diary Card.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: participants are classified as responders or nonresponders according to the Day 29 and baseline grades. The registry reports adjusted responder percentages from a multivariate logistic regression model. The posted summary also includes a recalculated unadjusted comparison using the group counts and sizes. These are related descriptions of the outcome, but they are not the same analysis.

What does logistic regression do?

As a general explanation, logistic regression models the probability of a binary outcome, such as meeting a responder definition. It can estimate group differences while accounting for variables included in the model. The registry record says the primary group estimates were adjusted using a multivariate logistic regression model, but the covariates, model specification, and details of the adjustment are not reported in the registry record. The adjusted percentages should therefore be understood as model-based estimates rather than as simple fractions of the listed group counts.

The registry-reported primary analysis gives p < 0.001. The recalculated unadjusted comparison gives p < 0.001. A p-value is a measure of how unusual data at least as incompatible with a null hypothesis would be under the assumptions of the specified statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. The analyses also have different adjustment status, so the p-values should be identified by their source and method rather than collapsed into one result.

Why report a confidence interval?

As a general explanation, a confidence interval communicates uncertainty around an estimated quantity. For the primary endpoint, the record gives 95% confidence intervals for the adjusted percentage in each group. The interval is not a range that guarantees the true value lies within it. Under the method’s assumptions, confidence intervals describe the variability of estimates across repeated samples and help readers assess how precisely the group percentages have been estimated.

The reported intervals are for the group percentages, not a directly reported interval for the adjusted difference between groups. A separate recalculated risk-difference interval is available in the posted comparison summary, but it is an unadjusted re-calculation from posted summary statistics. Keeping the interval’s target quantity and method clear matters: uncertainty around each group percentage is not identical to uncertainty around a difference or ratio.

What does the time-to-event method estimate?

The secondary time-to-onset analysis concerns the time until treatment response, based on the participant’s diary card over Day 1 to 7. The registry reports a Cox proportional hazard model and a hazard ratio of 6.561, with p < 0.001. As a general explanation, a hazard ratio compares event rates over time between groups, conditional on the model and its assumptions. It is not a ratio of median times and should not be interpreted as a direct multiplier of how quickly an individual responds. The registry record does not report a confidence interval for this hazard ratio.

The record also reports a log-rank analysis for time to response, with p < 0.001. In general, a log-rank test compares the event-time distributions between groups, while the Cox model estimates a relative hazard under a proportional-hazards framework. The proportional-hazards assumption means that the relative hazard is treated as stable over the time period modeled. Whether that assumption was assessed, and how censoring or ties were handled, is not reported in the registry record. The placebo median time to response is also not reported in the registry record.

What should be kept distinct?

Three statistical elements answer different questions: the adjusted group percentages describe modeled responder proportions; the unadjusted recalculation summarizes the posted group counts without the primary model’s adjustment; and the time-to-event analysis concerns when a response was recorded. They should not be substituted for one another. A small p-value does not establish precision on its own, which is why the estimates and confidence intervals matter. Nor does statistical significance establish that the endpoint captures all outcomes of interest.

As a general statistical point, binary outcomes can be affected by a threshold choice, because a small change around the cutoff can change a classification. The underlying scale has four ordered grades, but the primary endpoint reduces those grades to a responder status using the specified baseline and Day 29 criteria. The registry’s listed secondary assessments include measures at rest, participant assessment, satisfaction, and response timing. Those measures address related but nonidentical aspects of the study question.

The registry record does not report the full statistical analysis plan, the covariates in the primary model, the handling of missing observations beyond the partial population description, or any planned interim analyses. Those details should not be inferred from the fact that an adjusted model was used. General explanations of these methods describe their usual statistical meaning, not additional details about how the trial implemented them.

11. Confidence Intervals and Precision

The adjusted Day 29 responder estimate for BTX-A-HAC Next Generation is 88.3%, with a 95% confidence interval from 76.1% to 94.7%. For placebo, the estimate is 1.4%, with a 95% confidence interval from 0.3% to 6.5%. The intervals express uncertainty around the estimated group percentages under the model used for those estimates. They do not guarantee that the underlying population percentages fall within the stated ranges.

The primary confidence intervals are reported for the adjusted percentage in each group. They are not a single interval for the adjusted difference between groups. The posted recalculation separately gives an interval for an unadjusted risk difference, based on posted summary statistics. These estimates answer different questions because one is adjusted and one is unadjusted. The interval type and target quantity should be kept in view when comparing them.

The active-treatment group’s interval is wider in percentage-point span than the placebo group’s interval, while the placebo estimate is close to the lower end of its possible range. In general, confidence-interval width reflects factors such as sample size, outcome variability, and the method used. It is not appropriate to infer a precise explanation for the widths without the full model details and data.

For time to response, the active-treatment median is reported as 3.0 days, with a 95% confidence interval from 2.0 to 3.0 days. The record does not report the placebo median or a confidence interval for the hazard ratio. This limits direct assessment of precision for the comparative time-to-event estimate from the registry record alone. Confidence intervals are one part of statistical interpretation; they do not address unreported outcomes, model assumptions, or the possibility of bias.

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 illustrations translate the observed effect into hypothetical planning quantities. For the primary binary outcome, the figures are participants per arm. For time-to-event planning, the figures are total events, not participants per arm. These are different units, so the two sets of figures should not be compared as though they counted the same thing.

The stated 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 to a stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld approach. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 4 participants per arm for 80% power and 5 participants per arm for 90% power. Planning for 75% of the observed effect gives 8 participants per arm for 80% power and 10 participants per arm for 90% power. Planning for 50% of the observed effect gives 14 participants per arm for 80% power and 19 participants per arm for 90% power. The time-to-event illustrations instead express requirements as total events: for 100% of the observed effect, 9 total events for 80% power and 12 for 90% power; for 75%, 16 and 22 total events; and for 50%, 36 and 48 total events.

In plain language, the 80% power column is the illustrative number needed under the stated assumptions for an 80% chance of detecting the specified effect if that effect is present; the 90% column applies the corresponding higher power target. Smaller effects need more participants or, for time-to-event outcomes, more events. These are planning illustrations based on the observed result, not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.017; treatment proportion p₁ = 0.879; average p̄ = 0.448.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7033 = 1.3784.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3511 = 0.2955.
4. n = (1.3784 + 0.2955)² / (0.8618)² = 3.8, rounded up to 4 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 <- 0.0172413793103448                          # control proportion
p1 <- 0.879032258064516                          # 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(2353871)
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 = 4 (80% power), 5 (90% power)
 75% of observed effect: n per arm = 8 (80% power), 10 (90% power)
 50% of observed effect: n per arm = 14 (80% power), 19 (90% power)
power.prop.test: 3.8 
Simulated power at n = 4 per arm: 0.907 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry record reports the primary result as adjusted responder percentages estimated with a multivariate logistic regression model. It also reports a logistic-regression analysis with p < 0.001. The posted recalculation is an unadjusted comparison based on the group summary counts and sizes, with p < 0.001. Because the adjustment differs, the recalculated comparison is best treated as a supplementary summary rather than a replacement for the trial’s reported analysis.

The adjusted percentages and their confidence intervals describe the primary result as reported in the registry. The recalculated risk difference is a simple, unadjusted estimate from the posted summaries; it does not reproduce the primary model’s adjustment. The two analyses may therefore differ in what they estimate and how they account for participant characteristics. The registry record does not report the covariates or further details needed to reconstruct the adjusted analysis.

The registry record reports no discrepancy flag for this result. The sponsor-reported analysis and the unadjusted re-calculation are consequently presented as distinct statistical summaries, not as evidence that one was recalculated to contradict the other. The unadjusted result can help readers understand the contrast in the posted counts, while the sponsor-reported model remains the analysis described for the primary endpoint.

15. Multiplicity, Missing Data and Analysis Populations

The record specifies a primary endpoint and lists seven secondary outcomes. The primary question is focused on the Day 29 responder proportion at maximum frown. The secondary list spans repeated visits, persistence of response, assessments at rest, a two-grade reduction, participant self-assessment, satisfaction, and time to onset. Because these are multiple outcomes and time points, multiplicity is relevant to how secondary findings should be interpreted.

As a general statistical explanation, the more hypotheses tested, the greater the chance of at least one nominally significant result arising by chance when all null hypotheses hold. Researchers may address this through prespecified testing hierarchies or multiplicity adjustments, but the registry record does not report a multiplicity-control procedure. It also does not report a detailed testing hierarchy. Without those details, secondary p-values should be considered exploratory or interpreted cautiously unless the record identifies a specific confirmatory strategy.

The primary endpoint’s adjusted group percentages are described as coming from a multivariate logistic regression model. The covariates and model specifications are not reported in the registry record. The record also does not report an interim-analysis plan or the original sample-size justification. Their absence from the registry record does not prove that no such plans existed; it means their details are not reported in the registry record.

The modified intent-to-treat population is described as including randomized participants who received at least one injection into an injection site and had baseline and at least one postbaseline ILA value at maximum frown. The remainder of the population description is truncated. The registry record therefore does not report the full rules for inclusion, missing outcomes, or any imputation or sensitivity analyses. Missing-data methods can affect results when outcome availability is related to treatment or response, so the incomplete reporting limits assessment of that issue.

Different posted outcomes use different analysis counts. For example, the primary efficacy groups and the adverse-event groups have different at-risk counts, while the time-to-onset analysis lists its own group sizes. These population differences should be considered when reading results across endpoints. The record does not provide enough detail to explain every difference in analysis population or missingness.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: aphthous ulcer (1.7%), mydriasis (0.8%), foot deformity (0.8%).

The registry reports serious adverse events for the safety groups using their stated at-risk counts. In the BTX-A-HAC Next Generation group, 2 serious adverse events were reported among 125 at risk. In the placebo group, 1 was reported among 59 at risk. These are counts for participants with serious adverse events as presented in the record; they do not provide a complete account of event severity, timing, relatedness, or participant-level experience.

The record lists Aphthous ulcer at 1.7%, Mydriasis at 0.8%, and Foot deformity at 0.8% among the top serious-event terms. These are registry-listed terms and percentages; the record does not provide enough detail to establish whether events were considered treatment-related. Death counts are not reported in the registry record.

Serious adverse-event counts should be read separately from other adverse-event counts and from efficacy outcomes. The record also gives counts for other adverse events, but a count alone does not establish causation or comparative risk. Differences in at-risk population, event definitions, and follow-up can affect interpretation. The registry summary does not provide the fuller clinical narratives or adjudication details needed to assess individual events.

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

The primary result describes a marked contrast in the adjusted proportion meeting the study’s Day 29 responder definition: 88.3% for BTX-A-HAC Next Generation and 1.4% for placebo. The confidence intervals communicate uncertainty around those adjusted group estimates. The endpoint is specific to the investigator’s photographic assessment at maximum frown and the rule requiring a baseline moderate or severe grade and a Day 29 none or mild grade.

The result does not describe every possible change in glabellar-line severity. Because the primary outcome is binary, it does not preserve the full detail of the four-grade scale. Nor does it directly answer questions about appearance at rest, participant satisfaction, participant self-assessment, or response at every follow-up visit. Those are separate secondary questions, and most of their results are not reported in the registry record.

The trial was randomized, double blind, and placebo controlled, which are design features intended to support a comparison between groups. The registry record does not provide all details about allocation procedures, blinding, model covariates, missing-data methods, or analysis planning. The estimates should be interpreted alongside those limits in the available record, rather than as a complete account of every design and analysis choice.

The findings also do not settle how long any response persisted for all participants. The registry describes secondary follow-up assessments and a time-to-onset analysis, but the full set of secondary results is not reported. A secondary time-to-onset result addresses timing under its own event definition and model; it is not equivalent to long-term persistence or to the primary Day 29 response.

These statistical results are a description of the trial outcomes, not medical advice. They do not establish an outcome for every individual or resolve questions beyond the measured population, treatment, comparator, endpoint, and follow-up reported in the registry.

18. Why This Trial Matters Statistically

This trial illustrates how a clinical question becomes a statistical endpoint. The study did not simply ask whether appearance changed; its primary endpoint defined a responder using a specified baseline grade, a Day 29 grade, and an assessment at maximum frown. That operational definition determines what the reported percentage means and what it leaves out.

It also demonstrates why adjusted and unadjusted results should be distinguished. The registry’s primary result is based on adjusted estimates from logistic regression, while the recalculation summarizes posted group data without that adjustment. Both can be informative, but they address the data through different methods. Clear labeling helps prevent readers from treating them as interchangeable.

Confidence intervals add information that a p-value alone cannot provide. They show the uncertainty attached to the estimated group percentages, while the p-values describe results under particular statistical tests and assumptions. The record’s separate time-to-event analysis further shows that related questions—whether response occurred and when it occurred—require different estimands and methods.

Finally, the registry record shows the importance of transparent reporting. It identifies the trial design, endpoint, and some analysis methods, but it does not report the full sample-size rationale, model covariates, multiplicity strategy, or complete missing-data handling. Those omissions limit how fully readers can assess the analysis. Recognizing what is reported and what is not is an essential part of interpreting clinical trial statistics.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record gives an incomplete description of the modified intent-to-treat population: the text ends before all inclusion or analysis rules are available. It does not report the full primary-model specification, including its covariates, or detailed procedures for missing outcomes. These gaps limit reproducibility and make it difficult to assess how the adjustment and analysis population may have affected the estimates.

The original sample-size justification and design assumptions are not reported in the registry record. The separate sample-size illustrations use the observed effect and stated planning assumptions; they should not be mistaken for evidence about how the trial was originally designed. The record also does not report an interim-analysis plan or a multiplicity strategy for the listed secondary outcomes.

The primary endpoint is a threshold-based binary outcome derived from a four-grade photographic scale. It focuses on maximum frown at Day 29 and may not represent the full range of severity changes or other assessments. The remaining secondary outcome results are not reported in the registry record, which prevents evaluation of consistency across the listed assessment types and visits.

The time-to-onset result includes a reported hazard ratio but no confidence interval in the registry record, and the placebo median is not reported. The registry record also does not report details about assessment of the proportional-hazards assumption or event-time data handling. For safety, the summary counts do not establish event relatedness or provide detailed case descriptions. These are limitations of the available registry information, not proof that the underlying study did not collect additional data.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Clostridium Botulinum Toxin Type A to Improve Appearance of Moderate to Severe Glabellar Lines — NCT02353871.
• Registry record last updated 2022-09-28; status last verified 2022-09.
• Results first posted 2017-10-02.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed, phase III, randomized, double-blind, parallel-group, placebo-controlled study sponsored by Ipsen. It assessed a single treatment of BTX-A-HAC Next Generation against placebo in people with moderate to severe glabellar lines.

The primary endpoint was the adjusted proportion of responders at Day 29 on the investigator’s assessment at maximum frown. The adjusted estimates were 88.3% for active treatment and 1.4% for placebo, with reported 95% confidence intervals. The primary analysis used multivariate logistic regression; the registry also reports a logistic-regression p-value of < 0.001.

The record lists several secondary questions, but most secondary outcome results are not reported in the registry record. It reports a time-to-onset analysis and serious adverse-event counts. Important additional details—including the original sample-size rationale, full model specification, multiplicity handling, and complete missing-data methods—are not reported in the registry record.