BOTOX® for the Treatment of Platysma Prominence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BOTOX® for the Treatment of Platysma Prominence (NCT03915067), a randomized phase 2 study. The primary outcome is Percentage of Participants With at Least 1-Grade Improvement at Day 14 as Rated by Investigator Using the Clinician Allergan Platysma Prominence Scale (C-APPS).

2. Clinical Question

The primary endpoint is a short-term, categorical measure of change on an investigator-rated scale. It records whether each participant met a threshold for improvement, rather than the size of any change beyond that threshold. The registry identifies the study as a phase 2, randomized, double-blind, placebo-controlled, dose-ranging trial. Its stated purpose was to assess efficacy and safety in adults with moderate to severe platysma prominence.

3. Trial Design

This was a completed phase 2, multicenter, randomized, double-blind, placebo-controlled, dose-ranging study of BOTOX® purified neurotoxin complex for platysma prominence. The design used parallel groups and quadruple masking. The registry records enrollment of 171 participants. The study began on 2019-04-23, and primary completion was 2020-04-16.

Participants were assigned to placebo, BOTOX® Low Dose, or BOTOX® High Dose. Each regimen was administered on Day 1 as superficial intramuscular injections to the platysma muscle. The primary endpoint was assessed at Day 14, when investigators rated severity using the C-APPS. A secondary endpoint assessed improvement at the same time point using the participant-rated P-APPS.

The primary analysis population was the mITT population, defined in the registry record as all randomized participants with at least one post-baseline primary efficacy assessment, as described in the protocol. The overall number analyzed was the number with data available for analyses. The primary endpoint description specifies a Cochran-Mantel-Haenszel (CMH) chi-squared test. Further detail about the randomization procedure, masking roles, dose amounts, or the strata and adjustment factors used in the CMH analysis is not reported in the registry record.

There are results for the primary endpoint and one posted secondary endpoint. The registry lists 24 outcome measures and 4 analyses, but the full set of outcome-level results and the rationale for which outcomes were posted are not reported in the registry record. These omissions limit how fully the analysis plan and reporting completeness can be assessed from the registry alone.

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: Participant flow and all-cause mortality tables are based on all participants randomized on Day 1. Adverse events are reported for safety population, which included all participants who were administered study intervention.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT population included all randomized participants who had at least 1 post-baseline assessment of the primary efficacy parameter, the C-APPS, as described in the protocol. Overall number analyzed is the number of participants with data available for analyses.

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: mITT population included all randomized participants who had at least 1 post-baseline assessment of the primary efficacy parameter, the C-APPS, as described in the protocol.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With at Least 1-Grade Improvement at Day 14 as Rated by Investigator Using the Clinician Allergan Platysma Prominence Scale (C-APPS), measured over Day 14.

The primary endpoint is the percentage of participants with at least a 1-grade improvement at Day 14, rated by an investigator using the C-APPS. The scale assesses platysma prominence severity at maximum contraction on a 5-grade scale, with 1 meaning minimal and 5 meaning extreme. Higher values indicate worse severity. The endpoint reduces the scale assessment to whether a participant crossed the prespecified threshold of at least a 1-grade improvement.

A threshold-based endpoint is used to express the proportion of participants who met a defined response criterion. It can be easier to interpret as a response rate than a change in the full scale score, but it does not describe how much improvement occurred among participants who responded, nor does it show the distribution of all score changes. Participants just reaching the threshold and those improving further count alike for this measure.

The primary outcome description says that percentages were rounded to the nearest whole number at the nearest decimal. The posted arm-level estimates are accompanied by 95% confidence intervals. The registry identifies the mITT population for this efficacy assessment and names the CMH chi-squared test as the analysis method. Information about the handling of missing Day 14 assessments or the details of any additional model is not reported in the registry record.

7. Results Posted in the Registry

• BOTOX® Low Dose: 77.8% (42/54) versus 12.0% (6/50) on control; risk difference 65.8 percentage points (95% CI 51.5 to 80.1), risk ratio 6.48 (3.02–13.92); unadjusted two-proportion z-test p = <0.001.
• BOTOX® High Dose: 88.2% (45/51) versus 12.0% (6/50) on control; risk difference 76.2 percentage points (95% CI 63.6 to 88.9), risk ratio 7.35 (3.45–15.68); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants With at Least a 1-Grade Improvement at Day 14 as Rated by Participant Using the Participant Allergan Platysma Prominence Scale (P-APPS)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • BOTOX® Low Dose: 75.9% (41/54) versus 18.0% (9/50) on control; risk difference 57.9 percentage points (95% CI 42.3 to 73.5), risk ratio 4.22 (2.29–7.77); unadjusted two-proportion z-test p = <0.001.
  • BOTOX® High Dose: 88.2% (45/51) versus 18.0% (9/50) on control; risk difference 70.2 percentage points (95% CI 56.4 to 84.1), risk ratio 4.90 (2.69–8.93); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for BOTOX® Low Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for BOTOX® High Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted participant-rated secondary endpoint follows the same broad pattern as the primary investigator-rated endpoint: improvement at Day 14 was more frequent in both BOTOX® arms than in the placebo arm. This directional agreement offers a complementary view because the secondary measure is based on participant ratings rather than investigator ratings. It does not make the two scales interchangeable, and each measures response using its own assessment approach.

The secondary findings can be read as supportive context for the primary result, not as an independent confirmation with the same statistical standing. The registry lists one secondary outcome result, while also listing 24 outcome measures and 4 analyses. The availability and selection of posted secondary results, and how they relate to all outcomes assessed, are not explained in the registry record.

Unadjusted secondary results carry less inferential weight when many outcomes or comparisons may have been examined. In general, testing multiple hypotheses without an adjustment or a prespecified hierarchy increases the chance of at least one small p-value arising by chance. Whether the trial controlled the family-wise error rate or used another multiplicity strategy is not reported in the registry record. The secondary result is therefore best treated as descriptive or supportive unless the full analysis plan establishes its intended confirmatory role.

The participant-rated endpoint also provides information about a different perspective on the same general construct. Agreement in direction across participant and investigator ratings is useful to note, but does not resolve questions about missing assessments, the durability of response, or the clinical meaning of the threshold. Those matters require information beyond the posted Day 14 response rates.

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

• Percentage of Participants With at Least a 1-Grade Improvement at Day 14 as Rated by Participant Using the Participant Allergan Platysma Prominence Scale (P-APPS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each assessed participant either did or did not achieve at least a 1-grade improvement by Day 14. The arm-level percentage is the proportion meeting that threshold. This is a response-rate analysis, not an analysis of average change across the full C-APPS scale. It therefore answers how often the specified response was observed, rather than how much score change occurred overall.

What the rate difference represents

A rate difference subtracts the response rate in the comparator group from the response rate in the treatment group. It is expressed in percentage points when the rates are presented as percentages. For the posted primary endpoint, the reported CMH rate differences are 65.8 for Low Dose versus placebo and 76.2 for High Dose versus placebo. The associated 95% confidence intervals give a range of values compatible with the data and the analysis, subject to the method’s assumptions. The sponsor’s reported comparisons use the CMH method.

Why a CMH method may be used

In general, the Cochran-Mantel-Haenszel approach compares categorical outcomes while accounting for groups or strata specified in the analysis. It can produce a test of association or a common effect estimate across strata. Which stratification variables were used, whether the reported rate difference was adjusted in a particular way, and the details of the implementation are not reported in the registry record. The primary endpoint description names a CMH chi-squared test, while the posted results report CMH rate differences and confidence intervals.

A test statistic and a confidence interval answer related but distinct questions. The p-value summarizes how incompatible the observed data are with a null hypothesis under the test’s assumptions. The confidence interval communicates the uncertainty and range of plausible effect sizes under the estimation method. Neither measure alone establishes clinical importance, generalizability, or the probability that a hypothesis is true. The sponsor’s p-values were reported as p < 0.001 for both primary comparisons.

What the recalculation adds

Simple unadjusted recalculations can be made from the posted event counts and analyzed group sizes. Those calculations help readers check the broad scale of the arm contrast using summary data, but they do not reproduce a stratified or otherwise adjusted sponsor analysis. The sponsor’s reported analysis is the primary source for the trial’s inferential result. In this record the recalculated differences are close to the sponsor-reported rate differences, and the record indicates no discrepancy. The recalculations should not replace the CMH results or be treated as a new prespecified analysis.

Other familiar measures for binary outcomes include risk ratios and odds ratios. They describe relative rather than absolute contrasts and can behave differently from a rate difference, especially when the outcome is common. The numerical estimates should be interpreted on their own scales; a relative measure is not interchangeable with a difference in percentage points. The reported primary analysis is framed as a rate difference, so the interpretation emphasizes the absolute contrast in response rates.

Planning illustrations and power

Sample-size illustrations based on an observed effect are conditional on assumptions about the effect to detect, significance level, allocation, and statistical approximation. They do not reconstruct the trial’s original design process. In general, power is the probability of detecting an effect of a specified size under a stated design and model, if that effect is real. Higher target power generally requires a larger planned sample, all else equal. When the effect assumed for planning is smaller, more participants are generally needed to detect it with the same target power.

The planning illustrations in this analysis use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They consider effects described as 100%, 75%, and 50% of the observed effect. For non-time-to-event outcomes, the displayed sample sizes are participants per arm. These are planning examples derived from the observed results, not the trial’s original sample-size justification. The original design assumptions and sample-size justification are not reported in the registry record.

Interpretation limits of the methods

Analyses based on percentages depend on having outcome data available and on the definition of the analysis population. The registry states that the mITT population included randomized participants with at least one post-baseline assessment of the primary efficacy parameter. That definition does not by itself explain how missing Day 14 data were handled, whether any imputation was used, or whether sensitivity analyses were conducted; those details are not reported in the registry record.

The trial lists multiple outcome measures and analyses. Testing many outcomes or contrasts can increase the chance of at least one apparently positive result if no adjustment or hierarchy is used. Whether multiplicity was controlled, which comparisons were designated primary for testing, and the order of testing are not reported in the registry record. The primary endpoint and sponsor-reported comparisons should therefore be distinguished from secondary findings, whose inferential weight depends on the analysis plan and multiplicity handling.

11. Confidence Intervals and Precision

The 95% confidence intervals for the primary rate differences are 51.5 to 80.1 for BOTOX® Low Dose versus placebo and 63.6 to 88.9 for BOTOX® High Dose versus placebo. They describe uncertainty in the estimated differences, rather than a range containing 95% of individual participant outcomes. Under the methods and assumptions used, the intervals are compatible with a range of positive rate differences. Their lower bounds remain above zero, consistent with the sponsor’s reported p-values of p < 0.001.

The intervals have meaningful width, so the exact magnitude of the difference is not pinned down to a single value. Their span reflects sampling uncertainty and the amount of information available for the estimates. The arm-level confidence intervals also show uncertainty in each response proportion: 3.0 to 21.0 for placebo, 66.7 to 88.9 for Low Dose, and 79.4 to 97.1 for High Dose. These intervals should not be compared as if they were themselves formal tests of the differences between arms.

Confidence intervals do not account for every possible source of uncertainty. They do not resolve uncertainty about missing outcomes, analysis choices, multiplicity, generalizability, or how well the endpoint captures outcomes that matter to participants. The registry record does not report enough information to assess all those issues. Precision is therefore best understood as the statistical uncertainty around the reported endpoint estimates, not as certainty about broader or longer-term effects.

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 are planning calculations based on the observed effect, not a record of the original trial design. For these binary endpoints, the figures mean participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider an effect equal to 100%, 75%, or 50% of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design intended to have an 80% chance of detecting the assumed effect, under the planning assumptions. The 90% power column gives the corresponding number per arm for a 90% target chance. These are prospective planning concepts applied to hypothetical effects; they are not measures of how much power the completed trial had after observing its results. This is not observed power.

For example, for the primary Low Dose comparison, the illustration ranges from 8 participants per arm for 80% power and 10 for 90% power when planning for 100% of the observed effect, to 29 and 38 when planning for 50% of the observed effect. For High Dose, the corresponding figures are 6 and 7 for 100% of the observed effect, and 22 and 29 for 50% of the observed effect. The values are sensitive to the assumed effect size: smaller effects need more participants to reach the same target power. These calculations should not be read as recommendations for a future study without considering its own assumptions and design.

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 = 0.120; treatment proportion p₁ = 0.778; average p̄ = 0.449.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7034 = 1.3786.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5277 = 0.4441.
4. n = (1.3786 + 0.4441)² / (0.6578)² = 7.7, rounded up to 8 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 <- 0.12                          # control proportion
p1 <- 0.777777777777778                          # 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(3915067)
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 = 8 (80% power), 10 (90% power)
 75% of observed effect: n per arm = 14 (80% power), 18 (90% power)
 50% of observed effect: n per arm = 29 (80% power), 38 (90% power)
power.prop.test: 7.7 
Simulated power at n = 8 per arm: 0.881 (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 sponsor-reported primary comparisons use the Cochran-Mantel-Haenszel method. For Low Dose versus placebo, the registry reports a rate difference of 65.8, with a 95% confidence interval from 51.5 to 80.1 and p < 0.001. For High Dose versus placebo, it reports a rate difference of 76.2, with a 95% confidence interval from 63.6 to 88.9 and p < 0.001.

The simple recalculations from the posted arm counts are unadjusted. They are useful as a check on the general magnitude of the contrasts, but they do not substitute for the sponsor’s CMH analysis. The recalculated primary estimates are close to the sponsor’s reported estimates, and the registry record indicates no discrepancy. The sponsor’s own analysis therefore remains the appropriate result to emphasize. The small differences in displayed values reflect the reported rounding and should not be treated as evidence of a conflict between analyses.

The registry does not report the CMH stratification details or enough of the statistical analysis plan to reconstruct every feature of the sponsor analysis. The reported sponsor estimates, confidence intervals, and p-values should be interpreted as the trial’s formal posted results; the unadjusted calculations are supplementary checks based on summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and posts one secondary endpoint result. It also lists 24 outcome measures and 4 analyses. This creates a multiplicity question: if multiple outcomes, time points, or comparisons are tested, the chance of obtaining at least one nominally significant result can rise. In general, prespecifying a testing hierarchy or adjusting for multiple testing can help control that risk. The registry record does not report whether such a strategy was used, how the primary and secondary analyses were ordered, or whether the reported p-values were adjusted.

The primary analysis population is described as the mITT population, consisting of randomized participants with at least one post-baseline assessment of the primary efficacy parameter, as described in the protocol. The number analyzed is the number with data available for the analysis. This definition gives some information about inclusion, but does not specify how participants without an available Day 14 result were treated. Missing-data methods, imputation rules, sensitivity analyses, and reasons for missing assessments are not reported in the registry record.

These details matter because a response percentage depends on which participants contribute data and on the assumptions used for missing outcomes. If availability of an assessment is related to treatment or outcome, an analysis limited to available data may not represent all randomized participants in the same way. This is a general methodological concern, not a claim that such bias occurred in this trial.

The record names a CMH chi-squared test for the primary endpoint, but does not report the analysis strata, adjustment factors, or the full statistical analysis plan. It also does not report interim analyses or a sample-size justification. Without those details, readers cannot fully evaluate the prespecification, multiplicity control, or robustness of the inferential strategy from the registry record alone.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: thrombocytosis (1.7%), appendicitis (1.7%).

The posted serious adverse event summary reports 0 serious adverse events among 56 participants at risk in the placebo group, 2 among 59 participants at risk in the BOTOX® Low Dose group, and 0 among 54 participants at risk in the BOTOX® High Dose group. The registry lists thrombocytosis and appendicitis among the top serious event terms, each at 1.7%. No deaths were reported in any of the three groups.

These counts describe the posted serious adverse event data; they are not a complete account of all safety outcomes. The registry also reports other adverse events affecting 10 participants at risk in placebo, 6 in Low Dose, and 8 in High Dose. The summary does not establish whether an event was caused by treatment, and the presence or absence of a serious event in these groups does not by itself determine comparative risk. The numbers of participants at risk for safety reporting differ from the primary efficacy analysis denominators, so the two sets of counts should not be conflated.

The registry record does not provide enough detail to assess event timing, duration, severity beyond the serious-event classification, or all event categories. Safety findings should be interpreted as a limited descriptive summary rather than a comprehensive estimate of safety.

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

The posted results show that, in this trial, a larger proportion of participants assigned to either BOTOX® dose than to placebo met the investigator-rated threshold of at least a 1-grade improvement at Day 14. The sponsor-reported rate differences were positive, their 95% confidence intervals were above zero, and the reported p-values were p < 0.001. These are statistical descriptions of the observed endpoint and comparisons.

The result does not establish how long any improvement lasted, because the primary endpoint is at Day 14. It does not describe the size of improvement beyond the one-grade threshold, and it does not by itself establish effects on outcomes that were not posted. The study compares each dose with placebo; it does not report a direct inferential comparison of Low Dose against High Dose. A numerical ordering of the response proportions should not be mistaken for a tested dose-to-dose difference.

The findings also do not resolve all questions about safety, missing data, multiplicity, or the generalizability of results beyond the participants and procedures in this trial. The registry reports a limited adverse-event summary, while details about missing outcome handling and multiplicity methods are not reported in the registry record. Statistical significance does not answer whether a change is important to every participant or whether results will be similar in other settings.

Accordingly, the most direct interpretation is limited to the endpoint, time point, analysis population, and comparisons reported: response rates at Day 14 were higher in each BOTOX® arm than in placebo under the sponsor’s primary analysis. Broader conclusions require evidence about outcomes, duration, safety, and populations beyond what these posted results establish.

18. Why This Trial Matters Statistically

This trial illustrates how the choice of endpoint shapes a clinical-trial result. A threshold response rate is accessible to interpret, but compresses a graded scale into a yes-or-no outcome. The investigator-rated C-APPS result answers how many participants crossed the 1-grade improvement threshold, while leaving the full distribution of score changes unrepresented in this primary summary.

The record also gives an example of why a reported analysis and a simple recalculation are not necessarily the same thing. Unadjusted calculations from summary counts can serve as a check, whereas the sponsor’s stated CMH analysis is the formal reported method. In this case the estimates are close and the record notes no discrepancy, allowing the reader to distinguish the robustness of the broad pattern from the exact method used for inference.

Confidence intervals add information beyond a declaration of statistical significance. They show a range of plausible rate differences and make the uncertainty in the estimated magnitude visible. At the same time, precision in an endpoint estimate does not remove uncertainty about missing data, analysis choices, multiplicity, or clinical interpretation.

Finally, the planning illustrations make clear that sample-size requirements depend on the effect assumed for future planning. A calculation anchored to the observed effect can look very different from one designed to detect a smaller effect. Such illustrations are not evidence of the completed trial’s observed power and do not reveal the original planning assumptions. The registry record’s omissions on these points are an important part of a careful statistical reading.

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 primary endpoint captures response at Day 14 and does not report persistence of improvement. It is based on a threshold on the C-APPS, so the posted percentages do not convey the full scale-score distribution or the magnitude of changes beyond the response cutoff. The registry does not report a direct statistical comparison between the two BOTOX® dose arms.

The mITT definition is reported, but the handling of missing Day 14 assessments, any imputation, and sensitivity analyses are not reported in the registry record. This limits assessment of how missing outcome data may affect the response estimates. The record names the CMH method but does not give the strata or adjustment details needed to reproduce the sponsor analysis fully.

The registry lists multiple outcome measures and analyses, but does not report whether multiplicity was controlled or whether secondary tests were arranged in a prespecified hierarchy. Only one secondary endpoint result is posted, limiting assessment of the broader set of measured outcomes. The original sample-size justification and planning assumptions are not reported; observed-effect sample-size illustrations should not be confused with those original assumptions.

The safety summary is limited to posted event counts and does not provide a complete account of event timing, duration, or all safety categories. The study is described as multicenter, but further information on participant characteristics, site distribution, and the representativeness of the enrolled group is not reported in the registry record. These limitations qualify interpretation of the posted findings without changing what the reported comparisons state.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: BOTOX® for the Treatment of Platysma Prominence — NCT03915067.
• Registry record last updated 2023-05-03; status last verified 2023-04.
• Results first posted 2023-05-03.
• 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

NCT03915067 is a completed phase 2, randomized, double-blind, placebo-controlled, dose-ranging trial of BOTOX® for adults with moderate to severe platysma prominence. The registry records 171 enrolled participants and three parallel arms: placebo, BOTOX® Low Dose, and BOTOX® High Dose. Injections were administered on Day 1, and the primary investigator-rated response endpoint was assessed at Day 14.

The posted primary results show higher response proportions in both BOTOX® arms than placebo, with sponsor-reported CMH rate differences of 65.8 for Low Dose and 76.2 for High Dose. Each comparison had a reported p-value of p < 0.001. These findings concern the specified Day 14 threshold endpoint and do not alone establish duration, dose-to-dose differences, or broader outcomes.