Treatment of Moderate to Severe Lateral Canthal Lines: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Moderate to Severe Lateral Canthal Lines (NCT04249687), a randomized phase 3 study. The primary outcome is Percentage of Subjects With a ≥ 2-grade Improvement From Baseline on the Lateral Canthal Line Investigator and Subject Assessments at Maximum Smile at One Month..

2. Clinical Question

The registry describes the study objective as evaluating the efficacy and safety of a single dose of QM1114-DP relative to placebo. The primary outcome concerns change in the appearance of lateral canthal lines at maximum smile. Investigators and participants assess line severity using a 4-grade scale, with 0 meaning none and 3 meaning severe. The registered primary outcome is framed around the count of participants meeting the improvement threshold, although its title describes the measure as a percentage.

This is a comparison of randomized groups, not a comparison of participants before and after treatment alone. The placebo group provides a reference for changes that may occur over the same period without the active study intervention. The registry record does not describe further eligibility details, such as age limits or other inclusion criteria, so those should not be inferred from the trial title or outcome definition.

3. Trial Design

This was a multicenter, randomized, double-blind, placebo-controlled phase 3 study with a parallel-group model. The registry records quadruple masking. A total enrollment of 303 is reported. The trial is marked completed, with a start date of 2020-02-10 and a primary completion date of 2020-09-25.

The active intervention was QM1114-DP, described as botulinum toxin type A and given as an intramuscular injection. The comparator was a buffered solution, also given intramuscularly. The brief study description specifies a single dose. The registry record does not report the randomization procedure, the allocation ratio, or the details of how masking was maintained.

The primary outcome was assessed at Month 1. In the posted outcome counts, the treatment group has 204 participants and 106 meeting the outcome, while the placebo group has 69 participants and 1 meeting it. Those outcome denominators are not the same as the total enrollment. The registry record does not explain the difference, identify the analysis population for these counts, or give a detailed account of missing outcome data.

The study also has one posted secondary outcome, assessed at One Month. It concerns achieving grade 0 or 1 on the investigator scale at maximum smile. The secondary outcome has its own reported group counts. The registry record does not provide a full protocol, explain whether other outcomes were measured but not posted, or describe the original statistical plan or sample-size justification.

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 Percentage of Subjects With a ≥ 2-grade Improvement From Baseline on the Lateral Canthal Line Investigator and Subject Assessments at Maximum Smile at One Month., measured over Month 1.

The primary endpoint counts participants with at least a 2-grade improvement from baseline on the lateral canthal line investigator and subject assessments at maximum smile. The scheduled assessment is Month 1. The underlying scale has four grades: 0 indicates no lines and 3 indicates severe lines. The endpoint therefore focuses on a threshold in change in a rated appearance measure, rather than on the mean score or the size of improvement among all participants.

A threshold outcome can be useful because it expresses how many participants cross a prespecified level of change. It is also a binary outcome: each participant either meets the improvement criterion or does not. The registry lists the measure as a count of participants, while the endpoint title uses the word “Percentage.” The posted primary results give counts and denominators by group.

The registry wording refers to investigator and subject assessments but does not clarify whether the threshold must be met on both assessments or how disagreement between them is handled. That operational detail is not reported in the registry record. Nor does the record explain why the threshold or the one-month assessment time was selected. The endpoint should therefore be interpreted as the registered participant-count outcome at that assessment, without assuming additional scoring rules.

7. Results Posted in the Registry

• Treatment: 52.0% (106/204) versus 1.4% (1/69) on control; risk difference 50.5 percentage points (95% CI 43.1 to 57.9), risk ratio 35.85 (5.10–252.04); 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 Subjects Who Achieve Grade 0 or 1 in Lateral Canthal Line Investigator Scale at Maximum Smile.

• 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:
  • Treatment: 87.5% (175/200) versus 11.8% (8/68) on control; risk difference 75.7 percentage points (95% CI 66.8 to 84.7), risk ratio 7.44 (3.87–14.29); 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 Treatment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary outcome, assessing whether participants achieved grade 0 or 1 on the investigator scale at maximum smile at One Month. The group counts show a directional pattern consistent with the primary outcome: more treatment-group participants met the secondary criterion than placebo-group participants. This endpoint uses a different definition from the primary outcome, so the two should be understood as related but not interchangeable measures.

The secondary outcome can add context because it describes achievement of a specified severity level, whereas the primary outcome concerns improvement from baseline. Agreement in direction across these measures is descriptively supportive of a similar pattern in the posted results. It does not independently resolve the discrepancy between the sponsor’s primary analysis and the unadjusted recalculation, and it does not establish that either measure captures all dimensions of the study objective.

Unadjusted secondary results generally carry less confirmatory weight than a prespecified primary analysis. When several outcomes are tested, the chance of obtaining at least one apparently noteworthy result can increase unless the analysis plan accounts for multiplicity. The registry record does not report whether multiplicity was addressed, what hierarchy of outcomes was planned, or whether the secondary endpoint was intended to support a formal confirmatory claim.

The secondary outcome’s reported analysis also uses the Cochran-Mantel-Haenszel method and gives p = 0.05, while an unadjusted recalculation is separately available. Those inferential results should not be treated as interchangeable. The number of secondary outcomes posted is not evidence that no other outcomes were collected, and the registry does not describe a complete outcome-reporting plan.

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

• Percentage of Subjects Who Achieve Grade 0 or 1 in Lateral Canthal Line Investigator Scale at Maximum Smile.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either meets the registered improvement threshold or does not. For a binary outcome, the group counts can be expressed as proportions, and a between-group risk difference describes the absolute contrast between those proportions. A risk difference close to zero would indicate similar observed proportions; a positive value in the direction used for this comparison indicates a higher proportion meeting the criterion in the treatment group. The recalculated estimate is 0.505, but it is an unadjusted estimate based only on the posted summary counts.

What does the reported p-value test?

A p-value describes how compatible the observed data are with a specified statistical null hypothesis, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of a group difference. The registry gives the sponsor’s p-value as 0.05 for a superiority analysis. The unadjusted recalculation gives p < 0.001. These are results from different analyses and must not be conflated.

The sponsor identifies the Cochran-Mantel-Haenszel method. In general, this method can compare groups while accounting for strata, rather than simply pooling all observations into one unadjusted comparison. The registry record does not say which strata were used, how they were defined, whether any covariates were included, or what exact test variant was applied. It is therefore not possible to reconstruct the sponsor’s analysis from the posted record. The existence of a named method does not supply the missing analysis details.

Why can an adjusted result differ from a simple recalculation?

In general, an adjusted or stratified analysis can produce a different estimate or p-value from an unadjusted calculation because it uses information about the structure of the data. Differences can also arise from the analysis population, the handling of missing observations, or implementation choices. These are possible general explanations, not claims about what occurred in this trial. The registry does not report enough detail to identify the reason for the difference between p = 0.05 and p < 0.001.

For this reason, the sponsor’s reported analysis is the primary inferential result to cite. The recalculation remains useful as a transparent description of the contrast implied by the posted counts, but it is not a substitute for the sponsor’s method. The discrepancy should be visible to readers rather than resolved by selecting whichever p-value appears more compelling.

What does over-dispersion mean for a binary outcome?

Over-dispersion is a general concern when observations vary more than a statistical model expects. For binary outcomes, departures from model assumptions can affect standard errors and the resulting uncertainty. The registry does not report an over-dispersion assessment or indicate that over-dispersion was relevant to the sponsor’s analysis. It would be inappropriate to assume that such a correction was or was not needed.

Randomization supports a comparison between assigned groups, but statistical interpretation still depends on the analysis population and outcome data. The record does not report whether the primary analysis followed an intention-to-treat approach, whether any participants were excluded after randomization, or how incomplete assessments were treated. These details matter because a count-based comparison relies on knowing which participants contributed to each denominator.

Finally, statistical significance and estimation answer different questions. A p-value addresses compatibility with a null hypothesis, while an estimate and confidence interval describe the magnitude and precision of a contrast. The sponsor’s p-value is reported without an estimate or interval, leaving the posted primary effect size and interval to the unadjusted recalculation. The two forms of evidence should be described separately, with the sponsor’s own analysis taking precedence for the trial’s inferential conclusion.

11. Confidence Intervals and Precision

The unadjusted primary risk difference is 0.505, with a confidence interval from 0.431 to 0.579. A confidence interval gives a range of values compatible with the data and the assumptions of the calculation; it communicates uncertainty about the estimated difference rather than a guarantee that the true value lies within the displayed limits. This interval is for the unadjusted recalculation, not the sponsor’s Cochran-Mantel-Haenszel analysis.

The interval is entirely on the positive side of zero, which is consistent with the direction of the posted group counts. Its endpoints indicate that the unadjusted estimate is not a single exact value. However, this apparent precision does not address uncertainty from choices that are not described in the registry, such as the analysis population, missing-data handling, or any adjustment used by the sponsor.

The sponsor analysis has a reported p-value of 0.05 but no reported effect estimate or confidence interval. Consequently, the record does not give a directly comparable measure of the sponsor analysis’s effect size or precision. The unadjusted interval should not be presented as though it were the sponsor’s interval.

Other recalculated relative measures are also available, but relative measures can look especially large when the comparison group has very few participants meeting the outcome. A risk difference remains a direct description of the absolute contrast. Regardless of scale, estimates and intervals describe the observed comparison under their analysis assumptions; they do not establish generalizability beyond the study setting or resolve the discrepancy between analyses.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants and not total events. They are illustrations based on the observed effect, not the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each illustration is the stated fraction of the observed effect.

The 80% power column gives the illustrated number of participants per arm for a design with an 80% chance of detecting the assumed effect under those planning assumptions, if the effect and model assumptions were correct. The 90% power column gives the corresponding illustration for a 90% chance. These are design concepts, not guarantees for a future study, and the figures are not observed power.

The rows that use 100%, 75%, and 50% of the observed effect show how the planning illustration changes when the target effect is smaller than the observed one. Smaller effects need more participants to detect, all else equal. The observed result can be an optimistic basis for planning, particularly when it comes from a single study, so these figures should not be mistaken for a validated recruitment target.

The registry record does not report the assumptions or justification used to select the original trial enrollment. The illustrations therefore cannot explain why the trial enrolled its recorded number of participants. They are separate, hypothetical planning calculations, with their meaning limited to the stated assumptions.

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 = 0.014; treatment proportion p₁ = 0.520; average p̄ = 0.267.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6257 = 1.2263.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5137 = 0.4323.
4. n = (1.2263 + 0.4323)² / (0.5051)² = 10.8, rounded up to 11 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 <- 0.0144927536231884                          # control proportion
p1 <- 0.519607843137255                          # 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(4249687)
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 = 11 (80% power), 14 (90% power)
 75% of observed effect: n per arm = 17 (80% power), 22 (90% power)
 50% of observed effect: n per arm = 29 (80% power), 38 (90% power)
power.prop.test: 10.8 
Simulated power at n = 11 per arm: 0.853 (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 reports a sponsor analysis comparing the treatment and placebo groups with the Cochran-Mantel-Haenszel method. It is designated as a superiority analysis, and its reported p-value is 0.05. The record does not report the sponsor’s effect estimate or confidence interval, nor the analysis details needed to reproduce the result.

The simple recalculation from the posted primary counts gives a risk difference of 0.505, a confidence interval from 0.431 to 0.579, and p < 0.001. This is an unadjusted comparison and is not the same analysis as the sponsor’s reported result. The discrepancy means that the recalculated p-value should not be used in place of the sponsor’s p-value when describing the trial’s own analysis. The sponsor’s analysis takes precedence.

That precedence does not make the missing details immaterial. The registry does not explain why the results differ, what strata were used, or how participants with unavailable assessments were handled. Without those details, readers cannot determine which analysis features account for the discrepancy or independently verify the sponsor result. A careful account reports both results, labels the recalculation as unadjusted, and avoids treating either p-value as a measure of effect size.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical tests are conducted across multiple outcomes, time points, groups, or analysis choices. In general, testing many hypotheses without an appropriate plan can increase the chance that one result appears unusual by chance. A multiplicity strategy may define which outcome is primary, set a testing order, or adjust the threshold used for interpretation. These are general statistical principles, not details reported for this trial.

The registry identifies a primary outcome and one posted secondary outcome. It does not report whether the study had additional prespecified outcomes, whether the primary and secondary tests were ordered hierarchically, or whether any multiplicity adjustment was planned or applied. The statistical analysis plan and the original protocol details needed to answer those questions are not reported in the registry record. Accordingly, the secondary result should be treated as supportive descriptive evidence rather than assumed to have confirmatory status.

The registry also does not describe the primary analysis population, the handling of missing assessments, exclusions after randomization, or the approach to participants who did not complete the Month 1 assessment. The outcome denominators differ between the two groups, but the record does not give enough information to determine why or how those denominators were selected. No missing-data method should be inferred from the counts alone.

Interim analyses and any associated adjustment to the statistical plan are not reported in the registry record. Nor are the details of the sponsor’s stratification or the prespecified statistical model. These omissions prevent a full assessment of analysis flexibility and reproducibility. They do not prove that the trial lacked an analysis plan; they mean that the relevant details cannot be confirmed from this record.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: clavicle fracture (1.4%), gastroesophageal reflux disease (0.4%), invasive ductal breast carcinoma (0.4%), abortion spontaneous (0.4%), hypertension (0.4%).

The adverse-event record lists 230 participants at risk in the treatment group, with 3 affected by serious adverse events, and 73 at risk in the placebo group, with 1 affected. It reports 20 participants affected by other adverse events in the treatment group and 12 in the placebo group. Deaths are recorded as 0 in each group. These are the registry’s posted counts; the record does not provide a fuller account of event severity, timing, relatedness, or participant-level overlap between categories.

The listed serious-event terms include clavicle fracture at 1.4%, gastroesophageal reflux disease at 0.4%, invasive ductal breast carcinoma at 0.4%, abortion spontaneous at 0.4%, and hypertension at 0.4%. The registry does not give enough context in these fields to infer causation or to determine how each term relates to treatment exposure.

Safety counts should be read alongside their at-risk denominators and the study’s duration and follow-up, rather than as a complete safety profile. The registry record does not report detailed exposure time or a full narrative of adverse-event assessment. These figures describe what was posted and do not establish that an event was caused by the intervention.

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

The randomized comparison and posted outcome counts show a clear descriptive difference between groups in the number of participants meeting the primary improvement criterion at Month 1. The unadjusted recalculation quantifies that contrast, while the sponsor’s reported superiority analysis gives p = 0.05. Because the two analyses differ and the sponsor result lacks an estimate and interval in the record, a complete interpretation must keep them distinct and give precedence to the sponsor’s own analysis.

The result does not establish the size of a sponsor-adjusted treatment effect, because that estimate is not reported. The unadjusted risk difference and its confidence interval describe a recalculation from summary counts, not the sponsor’s model. The registry also does not provide the details needed to evaluate the impact of missing outcomes, the analysis population, or the statistical plan.

The findings are specific to the registered population, intervention, assessment method, and Month 1 endpoint. The record does not establish how the result applies to other populations, doses, assessment settings, or time points. It also does not show whether the observed outcome difference persists beyond the reported assessment timeframe.

Finally, statistical evidence is not the same as a judgment about clinical importance. The registry provides a threshold-based appearance rating but does not report a minimum clinically important difference or other interpretation standard. The posted results can describe group differences on the registered measure, but they do not alone establish how meaningful that difference is for an individual or how it should guide care.

18. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, its uncertainty, and the sponsor’s own inferential analysis should be read together. A straightforward recalculation from group counts yields an interpretable risk difference and confidence interval. The registry’s sponsor analysis, however, reports a different p-value and no corresponding effect estimate or interval. Reporting the discrepancy plainly is important: a reader should not mistake a transparent unadjusted calculation for a reproduction of the trial’s analysis.

The example also shows that the name of a statistical method is not enough to reproduce a result. The Cochran-Mantel-Haenszel method is reported, but the record does not identify the strata or provide other analysis details. Reproducibility requires enough information to understand how the estimate was formed, which participants contributed, and how incomplete outcomes were treated.

For clinical researchers and statisticians, the distinction between the primary outcome and a secondary outcome is also consequential. Related outcomes can offer context, but their interpretation depends on the prespecified analysis plan and any approach to multiplicity. Where those details are absent, a secondary result should not be elevated to the same evidential role as the primary analysis.

Finally, the planning illustrations demonstrate that a sample-size calculation is conditional on assumptions about the effect to detect and the design. They do not reveal the original study’s justification or show the probability that the completed trial “worked.” Keeping planning calculations separate from observed results helps prevent a common misreading of power and sample size.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry does not report the sponsor’s effect estimate or confidence interval, despite reporting a Cochran-Mantel-Haenszel p-value. It also does not describe the strata or other details of that analysis. This prevents independent reproduction and leaves the size and precision of the sponsor analysis unavailable in the record. The unadjusted recalculation is informative about the posted counts but cannot fill that gap.

The record does not explain the analysis population or why the primary outcome denominators are 204 and 69, rather than the total enrollment. It does not report the handling of missing outcomes, post-randomization exclusions, or protocol deviations. Those details are important for judging whether the compared groups reflect the randomized assignment as intended.

The primary endpoint wording does not clarify whether the investigator and subject assessments must both meet the improvement threshold or how their results are combined. The registry also does not report the sample-size justification, the full statistical analysis plan, interim analyses, or multiplicity procedures. These are limitations of what can be established from the registry record; they do not show that such procedures were absent from the trial.

The posted outcome is assessed at Month 1, and the registry record does not provide a longer-term primary outcome result in the information summarized. The safety fields give counts but limited context about duration, event relatedness, and overlap. Together, these gaps restrict interpretation of durability, analysis robustness, and the full safety context.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Treatment of Moderate to Severe Lateral Canthal Lines — NCT04249687.
• Registry record last updated 2023-06-18; status last verified 2021-03.
• Results first posted 2023-06-18.
• 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

NCT04249687 is a completed, multicenter, randomized, double-blind, placebo-controlled phase 3 study of QM1114-DP for moderate to severe lateral canthal lines. The parallel-group trial enrolled 303 participants and compared a single intramuscular dose of QM1114-DP, described as botulinum toxin type A, with an intramuscular buffered placebo solution.

The primary outcome was a participant count meeting the registered improvement criterion at Month 1. The sponsor reported a Cochran-Mantel-Haenszel superiority analysis with p = 0.05. An unadjusted recalculation from the posted counts gives a risk difference of 0.505, with a confidence interval from 0.431 to 0.579, and p < 0.001. The sponsor’s own analysis takes precedence, while the difference between results remains unresolved in the registry record.

One secondary outcome and safety counts are also posted. The record does not report key details of the analysis population, missing-data handling, original sample-size justification, or multiplicity plan.