Comparison of Dysport Reconstitution at 1.5 mL and 2.5 mL for the Treatment of Moderate to Severe Glabellar Lines: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Dysport Reconstitution at 1.5 mL and 2.5 mL for the Treatment of Moderate to Severe Glabellar Lines (NCT02718118), a randomized phase 4 study. The primary outcome is Proportion of Composite Responders Who Achieve at Least a 1-point Reduction From Baseline in Glabellar Line Severity Score (GLSS) at Maximum Frown..

2. Clinical Question

The comparison concerns the reconstitution volume and injection volume, not the stated total treatment dose: both arm descriptions specify 50 units. The primary endpoint is a composite response, meaning that response is based on assessments by the subject and a blinded evaluator. The main statistical contrast is the risk difference for the 2.5 mL group relative to the 1.5 mL group. A negative risk difference indicates a lower observed response proportion in the 2.5 mL group; a positive value indicates a higher one.

The registry also describes evaluation of glabellar line severity at maximum frown and at rest, onset of effect, satisfaction, psychological well-being, age appraisal, and adverse events. These are additional questions rather than substitutes for the specified primary comparison. The posted primary result is a comparison of observed responses at Day 30; it does not by itself answer every question about these other outcomes or assessments over time.

3. Trial Design

This was a Phase 4, randomized, parallel-group trial with double masking, described in the official title as subject- and evaluator-blinded. The registry identifies Galderma R&D as sponsor and lists the study status as completed. Enrollment was 60. The start is listed as 2016-04 and primary completion as 2016-10.

Participants were assigned to one of two Dysport reconstitution groups: 1.5 mL or 2.5 mL. The arm descriptions specify corresponding injection volumes of 0.05 mL and 0.08 mL per injection, respectively, and state that each participant received a single treatment session of 50 units at the Day 1 visit. The record describes the study as multi-center. Details about the number or location of centers are not reported in the registry record.

The primary outcome was the proportion of composite responders at maximum frown on Day 30. A responder had to achieve at least a 1-point reduction from baseline in glabellar line severity score, based on subject and blinded-evaluator assessment. The registry lists 15 outcome measures and 14 secondary outcomes posted. Secondary assessments include responder outcomes reported separately by subject, blinded evaluator, or treating investigator, and combination-responder outcomes involving subject and blinded-evaluator assessments. The specified secondary time frame for the detailed outcomes is 120 days.

The original sample-size justification, the trial’s planned statistical analysis, details of allocation concealment, and the handling of deviations from assigned treatment are not reported in the registry record. The reported design features establish the broad comparison but do not establish how the sponsor planned every statistical decision.

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

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 Proportion of Composite Responders Who Achieve at Least a 1-point Reduction From Baseline in Glabellar Line Severity Score (GLSS) at Maximum Frown., measured over 30 days.

The primary endpoint is the proportion of participants who met a composite response definition at maximum frown on Day 30. To qualify, a participant had to have at least a 1-point reduction from baseline in glabellar line severity score, with the response based on both subject and blinded-evaluator assessments. The registry describes the measure as a count of participants, with the outcome expressed as a proportion.

A responder endpoint translates a continuous or graded clinical assessment into a yes-or-no outcome according to a prespecified threshold. General statistical context: this can make a result easier to interpret as the share of participants meeting a defined response criterion, but it also means that differences within the responder and nonresponder groups are not represented in the binary outcome. The threshold and assessment time matter because they define what counts as response and when it is evaluated.

Using a composite based on both the subject and a blinded evaluator incorporates two perspectives into the primary response definition. The registry’s description does not specify the detailed rule for resolving any disagreement between those assessments, nor does it report the complete scoring instructions. Those details are not reported in the registry record. The endpoint therefore supports interpretation of the posted composite responder counts, but it should not be read as a complete account of every aspect of line severity, satisfaction, or change over the whole study period.

7. Results Posted in the Registry

• 2.5 mL Reconstitution: 86.7% (26/30) versus 90.0% (27/30) on control; risk difference -3.3 percentage points (95% CI -19.6 to 12.9), risk ratio 0.96 (0.80–1.16); unadjusted two-proportion z-test p = 0.688.

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.

Proportion of Responders, at Maximum Frown (Subject)

• 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:
  • 2.5 mL Reconstitution: 56.7% (17/30) versus 46.7% (14/30) on control; risk difference 10.0 percentage points (95% CI -15.2 to 35.2), risk ratio 1.21 (0.74–1.99); unadjusted two-proportion z-test p = 0.438.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2.5 mL Reconstitution and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Responders, at Maximum Frown (Blinded Evaluator)

• 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:
  • 2.5 mL Reconstitution: 66.7% (20/30) versus 70.0% (21/30) on control; risk difference -3.3 percentage points (95% CI -26.9 to 20.2), risk ratio 0.95 (0.67–1.34); unadjusted two-proportion z-test p = 0.781.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2.5 mL Reconstitution and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Responders, at Maximum Frown (Treating Investigator)

• 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:
  • 2.5 mL Reconstitution: 53.3% (16/30) versus 63.3% (19/30) on control; risk difference -10.0 percentage points (95% CI -34.8 to 14.8), risk ratio 0.84 (0.55–1.30); unadjusted two-proportion z-test p = 0.432.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2.5 mL Reconstitution and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results do not form a single consistent pattern pointing toward one reconstitution volume. At maximum frown, the subject-assessed responder count is higher in the 2.5 mL group, while the blinded-evaluator and treating-investigator counts are higher in the 1.5 mL group. The estimates are uncertain, and the reported intervals for these detailed comparisons include zero. They therefore do not establish clear differences between groups.

The primary outcome combines subject and blinded-evaluator assessments at Day 30. The secondary outcomes separate assessor perspectives and are listed at a 120-day time frame. Those distinctions matter: the outcomes are related through assessment of glabellar lines, but they are not identical replications of the primary endpoint. A different assessor or assessment time can yield a different responder pattern without resolving the primary comparison.

The registry identifies 14 secondary outcomes, including outcomes at rest and combination-responder outcomes. Detailed results for every listed secondary outcome are not reported in the registry record. The secondary findings that are detailed should not be used to override the primary result or to infer a general pattern across all listed measures.

General statistical context: testing many outcomes increases the chance that at least one comparison may look unusual by chance. The registry record does not report a multiplicity adjustment or a prespecified testing sequence, and the detailed secondary results are unadjusted. This makes them less persuasive as confirmatory evidence than a single outcome analyzed according to a documented, prespecified plan. Their best use is descriptive: they show how the observed results vary by assessor and outcome, while leaving substantial uncertainty about group differences.

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

• Proportion of Responders, at Maximum Frown (Subject)
• Proportion of Responders, at Maximum Frown (Blinded Evaluator)
• Proportion of Responders, at Maximum Frown (Treating Investigator)
• Proportion of Combination Responders, at Maximum Frown (Blinded Evaluator and Subject)
• Proportion of Responders, at Rest (Subject)
• Proportion of Responders, at Rest (Blinded Evaluator)
• Proportion of Responders, at Rest (Treating Investigator)
• Proportion of Combination Responders, at Rest (Blinded Evaluator and Subject)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference express?

General statistical context: a risk difference subtracts the event proportion in one group from the event proportion in another group. Here, the reported contrast is for 2.5 mL relative to 1.5 mL, so a negative estimate means the observed responder proportion was lower in the 2.5 mL group. The registry reports the primary estimate as -0.033. This estimate describes the observed group contrast; it does not adjust for other variables.

What does the confidence interval add?

General statistical context: a confidence interval gives a range of values compatible with the data under the method used to construct it. It conveys uncertainty around an estimate rather than identifying a range containing the true value with certainty. For the primary risk difference, the reported interval is -0.196 to 0.129. Because this interval spans zero, the data do not clearly distinguish a difference favoring either group. The interval is also wide enough to include differences in either direction, so the point estimate should not be treated as a precise estimate of the underlying contrast.

How should the p-value be read?

General statistical context: a p-value measures how unusual data at least as extreme as the observed data would be under a specified null hypothesis and model. It does not measure the probability that the null hypothesis is true, nor does it measure the probability that the finding is due to chance. The reported primary p-value is 0.688 and is unadjusted. The registry record does not report a sponsor analysis plan that would clarify the intended testing framework or any adjustment for multiple outcomes.

What does an unadjusted comparison mean?

General statistical context: an unadjusted comparison contrasts the groups without an adjustment for other characteristics or covariates. The posted primary comparison gives a risk difference, confidence interval, and unadjusted p-value. The registry record does not report a model-based adjusted estimate for this endpoint. The absence of a reported adjusted result does not establish that no additional analysis was conducted outside the registry; it means such an analysis is not reported in the registry record.

Why does the endpoint definition matter?

The primary measure is binary: each participant is counted as a composite responder or not, according to the criterion of at least a 1-point reduction from baseline at maximum frown on Day 30, based on subject and blinded-evaluator assessment. General statistical context: converting a graded score into a responder outcome makes the threshold central to interpretation. Participants just above and well above the threshold are both counted as responders, while participants just short of it are counted as nonresponders. The posted counts therefore answer the threshold-based question, not every question about the amount of score change.

The record describes the composite assessment but does not provide all operational details of how assessor ratings were combined. That rule, the original analysis population, and the treatment of missing endpoint observations are not reported in the registry record. Consequently, the posted counts can be interpreted as recorded results, while finer judgments about the endpoint’s implementation require information not reported in the record.

How do the secondary outcomes fit the analysis?

Several secondary outcomes use binary responder counts, with the assessment attributed to the subject, blinded evaluator, or treating investigator. General statistical context: multiple outcomes create multiple opportunities to observe an apparently notable result, even when there is no true difference. Methods for controlling this issue can include prespecified testing sequences or multiplicity adjustments. The registry record does not report whether either approach was planned or applied. The detailed secondary comparisons are identified as unadjusted, so they should be read as exploratory descriptions rather than as a set of independent confirmatory tests.

For all such comparisons, the count and group size provide the basic observed result, while a risk difference and its interval describe the contrast and uncertainty. The endpoint, assessor, and assessment time should be kept in view when comparing results: an outcome at maximum frown assessed by the subject is not the same measurement as one at rest or one assessed by an investigator. Similarity or difference among these secondary results does not replace the primary analysis.

What information about the analysis plan is missing?

The registry reports no analyses in the analysis listing. It does not report the original sample-size justification, the planned significance threshold for the trial, interim analyses, a missing-data strategy, or analysis-population definitions. The planning assumptions used for the sample-size illustration are separately described and should not be mistaken for the trial’s own design assumptions. General statistical context: prespecified methods help distinguish planned confirmatory analyses from exploratory findings, but the registry record does not contain enough detail to assess those decisions for this trial.

11. Confidence Intervals and Precision

The primary risk difference is -0.033, with a reported 95% confidence interval from -0.196 to 0.129. In plain terms, the interval includes a range of plausible contrasts that extends from a lower response proportion in the 2.5 mL group to a higher one. It includes zero, which represents no difference in the risk-difference scale. The data therefore do not estimate the direction of the group difference precisely.

The sample size for the primary comparison is 30 participants in each group. With these group sizes, the confidence interval is an important part of the result: the point estimate alone would give an incomplete impression of the evidence. The interval is consistent with a range of effects, rather than narrowly locating the difference. This imprecision limits how strongly the observed point estimate can be generalized to the underlying group contrast.

General statistical context: a confidence interval reflects sampling uncertainty under the calculation method and assumptions; it does not account automatically for every possible source of bias or uncertainty. The registry record does not report details of the interval-construction method or an analysis plan for the primary endpoint. The interval should therefore be read as the reported statistical precision, not as a guarantee that other uncertainties are absent.

The secondary comparisons also have uncertainty intervals, and those intervals span zero. Their small group sizes likewise limit precision. Intervals from different secondary outcomes should not be used to select a preferred finding without regard to the distinct assessors, outcomes, time frames, and multiplicity of comparisons. The primary and secondary intervals describe the observed data; none establishes a definitive difference or equivalence between the reconstitution groups.

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 table and curve are planning illustrations based on the observed effect, not on a reported original design justification. The listed 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 the stated fraction of the observed effect. For binary outcomes in these results, figures are participants per arm, not total events. The special total-events convention for time-to-event outcomes does not apply to this trial’s binary responder endpoint.

The 80% power column gives the number of participants per arm estimated to yield an 80% chance of detecting the specified effect under those assumptions, if that effect and the other assumptions hold. The 90% power column uses a higher target chance of detecting that effect, so its planning requirement is larger. These are design calculations, not observed trial outcomes.

For the primary endpoint, the row planning for 100% of the observed effect lists 1,455 participants per arm for 80% power and 1,948 participants per arm for 90% power. Planning for 75% of the observed effect lists 2,507 and 3,356 participants per arm, respectively. Planning for 50% of the observed effect lists 5,458 and 7,306 participants per arm, respectively. The pattern illustrates the general principle that smaller effects require more participants to detect under otherwise unchanged assumptions.

These planning figures are not observed power for the completed trial. They are illustrations based on the observed effect and stated calculation assumptions; the trial’s own original design assumptions are not reported in the registry record. They should not be read as evidence that the study was designed or conducted with these sample sizes.

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 = 0.900; treatment proportion p₁ = 0.867; average p̄ = 0.883.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4540 = 0.8898.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4534 = 0.3816.
4. n = (0.8898 + 0.3816)² / (-0.0333)² = 1,454.8, rounded up to 1,455 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 <- 0.9                          # control proportion
p1 <- 0.866666666666667                          # 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(2718118)
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 = 1,455 (80% power), 1,948 (90% power)
 75% of observed effect: n per arm = 2,507 (80% power), 3,356 (90% power)
 50% of observed effect: n per arm = 5,458 (80% power), 7,306 (90% power)
power.prop.test: 1454.8 
Simulated power at n = 1,455 per arm: 0.801 (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 a primary endpoint and multiple secondary outcomes, including separate responder assessments by subject, blinded evaluator, and treating investigator, as well as outcomes at maximum frown and at rest. Examining multiple outcomes creates a multiplicity issue: the more comparisons considered, the greater the chance that one or more may appear notable even when there is no underlying group difference.

The registry record does not report a multiplicity adjustment, a prespecified testing hierarchy, or a statistical analysis plan explaining how the primary and secondary endpoints were to be interpreted together. The posted secondary comparisons are unadjusted. They therefore should be treated cautiously and should not be considered independent confirmations of the primary endpoint.

The record lists no analyses in its analysis listing. This does not establish that no analyses were performed; it means analyses beyond the posted results are not reported in the registry record. The original sample-size justification and any interim-analysis plan are also not reported in the registry record. No such methods should be inferred from the completed status or the sample-size planning illustration.

The analysis population used for each outcome is not reported in the registry record. Details about whether all randomized participants were included, how treatment discontinuations were handled, or whether participants were analyzed according to assigned group are not reported. Missing-data handling for the primary and secondary endpoints is likewise not reported. These omissions limit assessment of how the posted counts relate to the randomized groups and whether missing observations could affect the estimates.

General statistical context: a complete interpretation of randomized comparisons benefits from transparent reporting of the analysis population, missing-data procedures, and multiplicity plan. Without those details, the observed counts and unadjusted comparisons remain interpretable as posted, but the full inferential framework cannot be reconstructed from the registry record.

15. 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 non-serious adverse event terms

The registry reports no serious adverse events in either group: 0 of 30 participants at risk in the 1.5 mL group and 0 of 30 at risk in the 2.5 mL group. Deaths are reported as 0 in both groups. The registry does not list serious adverse-event terms.

For other adverse events, the record reports 2 in the 1.5 mL group among 30 at risk and 0 in the 2.5 mL group among 30 at risk. These counts describe the registry’s posted safety figures; they do not by themselves establish that the groups differ in safety. With no serious events recorded in either group, the trial results also cannot establish that serious events are absent beyond the observation captured in this study.

General statistical context: safety counts are most informative when considered alongside event definitions, follow-up, severity, and completeness of reporting. The registry record does not provide further detail about the two other adverse events or a more detailed safety analysis. The figures should therefore be read as the reported counts, not as a comprehensive assessment of all possible harms.

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

The primary result shows that the observed Day 30 composite-responder counts were similar in size across the two groups: 27 of 30 in the 1.5 mL group and 26 of 30 in the 2.5 mL group. The estimated risk difference is -0.033, and the reported 95% confidence interval is -0.196 to 0.129. The interval spans zero and permits differences in either direction, so the observed contrast is not precise enough to establish a clear group difference.

This result does not demonstrate that the reconstitution approaches are equivalent. Equivalence requires a suitable prespecified margin and analysis, neither of which is reported in the registry record. Nor does the result establish that there is no difference: the interval includes a range of possible contrasts. A nonsignificant unadjusted p-value is not proof that the groups are identical.

The endpoint addresses a specific threshold-based composite response at maximum frown on Day 30. It does not directly summarize the amount of score change for every participant, the response at rest, each assessor’s result separately, satisfaction, onset, psychological well-being, or safety over time. Those are separate outcomes with their own results and uncertainties. The secondary findings do not provide a clear consistent pattern that resolves the primary uncertainty, and the registry record does not report a multiplicity plan.

General statistical context: trial estimates describe the enrolled study population and depend on the design, measurements, and analysis. The record does not report enough detail about analysis populations, missing data, or the original statistical plan to assess every possible source of uncertainty. The results should be interpreted as the posted evidence from this completed randomized comparison, not as a definitive statement about all participants or settings.

The safety figures report no serious adverse events or deaths in either group, and report other adverse events in the 1.5 mL group but not the 2.5 mL group. Those counts are limited observations from the study and do not establish a broad safety comparison. Overall, the registry results describe observed outcomes and their uncertainty; they do not support medical advice or a conclusion that one approach works or does not work.

17. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through both its estimated contrast and its uncertainty. The primary point estimate is close to zero on the risk-difference scale, but the confidence interval is broad enough to include differences in either direction. The small observed difference is not, by itself, evidence that the groups are equivalent or that a meaningful difference has been ruled out.

The comparison also highlights the distinction between an endpoint and the broader clinical question. A composite responder definition at maximum frown on Day 30 is a clear, threshold-based measure, but it is only one way to describe outcomes. Subject, blinded-evaluator, and treating-investigator assessments can produce different observed patterns, and outcomes at rest or at another time frame ask different questions. Keeping those distinctions visible helps prevent one result from being generalized to all measures.

The trial’s 60 participants are far fewer than the planning illustrations based on the observed primary effect. Those illustrations show how sample requirements can rise when the effect to detect is smaller, but they are not evidence about the original design or observed power. The original sample-size justification and analysis plan are not reported in the registry record.

Finally, multiple secondary outcomes make transparent reporting of prespecification and multiplicity important. Without those details, secondary comparisons are useful as descriptive context but carry less confirmatory weight. The record’s combination of randomized allocation, masked assessment, posted event counts, and uncertainty estimates supports a structured reading of what was observed, while the unreported analysis details constrain stronger conclusions.

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 total enrollment was 60, with 30 participants in each group. This limits precision for the primary comparison, as reflected by the reported confidence interval. The study results do not establish whether smaller group differences are present or absent.

The registry describes a multi-center study but does not report the number or locations of centers. It does not report participant characteristics beyond the condition, so the composition of the enrolled population cannot be assessed from this record. Further eligibility and baseline details are not reported in the registry record.

Although the title describes subject- and evaluator-blinding, the record does not provide further operational details about masking or allocation procedures. It also does not report the original sample-size justification, the trial’s statistical analysis plan, the analysis populations, or the approach to missing data. These omissions limit assessment of how the posted estimates were planned and derived.

The primary outcome is a threshold-based composite response at one stated assessment time. The registry does not report the detailed rule used to combine the subject and blinded-evaluator assessments. The secondary outcomes involve different assessors and measures, and detailed results for every listed secondary outcome are not reported in the registry record. The record also does not report whether multiplicity was addressed.

The safety summary lists no serious adverse events or deaths and gives limited detail on other adverse events. No serious adverse-event terms are listed. These registry figures cannot characterize rare events or provide a complete safety account beyond the recorded observations.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Dysport Reconstitution at 1.5 mL and 2.5 mL for the Treatment of Moderate to Severe Glabellar Lines — NCT02718118.
• Registry record last updated 2022-08-01; status last verified 2018-09.
• Results first posted 2018-09-25.
• 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

NCT02718118 is a completed Phase 4 randomized, double-masked, parallel comparison sponsored by Galderma R&D. It compared Dysport reconstituted at 1.5 mL with Dysport reconstituted at 2.5 mL for moderate to severe glabellar lines. The registry lists enrollment of 60, with 30 participants in each group.

The primary outcome was the proportion of composite responders at maximum frown on Day 30, defined by at least a 1-point reduction from baseline in glabellar line severity score based on subject and blinded-evaluator assessment. The registry reports 27 responders in the 1.5 mL group and 26 in the 2.5 mL group. The risk difference for 2.5 mL relative to 1.5 mL is -0.033, with a 95% confidence interval of -0.196 to 0.129 and an unadjusted p-value of 0.688.

The registry also reports secondary outcomes and safety counts. No serious adverse events or deaths were reported in either group. The original sample-size justification, analysis plan, missing-data approach, and multiplicity strategy are not reported in the registry record.