Investigation of the Effectiveness and Safety of MRZF111 in the Treatment of Décolleté Wrinkles: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Investigation of the Effectiveness and Safety of MRZF111 in the Treatment of Décolleté Wrinkles (NCT04177212), a randomized na study. The primary outcome is Responder Rate for Décolleté Wrinkles According to the Merz Aesthetics Scale (MAS)-At Rest Scale as Assessed by the Blinded Live Rater.

2. Clinical Question

The primary endpoint is a responder rate: it classifies each evaluable participant according to whether the score improved by the specified threshold, then reports the percentage classified as responders. The question is therefore about the proportion meeting that threshold at the stated follow-up, not the average amount of score change. The scale ranges from no wrinkles to very severe wrinkles, and higher scores indicate worse outcomes. A response represents an improvement in score, but the endpoint alone does not describe the size of improvement beyond the threshold.

The study was randomized and parallel-group, with single masking and evaluator blinding stated in the official title. The record does not explain who, beyond the blinded live rater, was masked. It also does not identify a comparison with another product or an untreated group. Consequently, the posted arm-to-arm response rates address the schedules used in this study; they do not directly estimate how either schedule compares with no intervention.

3. Trial Design

The registry describes a prospective, multicenter, parallel-group, evaluator-blind, randomized study of MRZF111 for décolleté wrinkles. Enrollment was 117, and the study status is completed. The registry lists phase as not applicable. The intervention is categorized as a device. Further details about the participating centers and randomization procedure are not reported in the registry record.

The two schedules differed in the number and timing of injection cycles. Group A was assigned 3 cycles, on Day 1, Week 8, and Week 16. Group B was assigned 2 cycles, on Day 1 and Week 16. Both schedules therefore included treatment at the start and at Week 16, while only Group A had the additional Week 8 cycle. The registry does not report the reason for choosing these schedules or the intended clinical contrast between them.

The primary outcome was assessed at Week 32, described as 16 weeks after the last treatment on Week 16. The responder assessment used the MAS-At Rest scale and a blinded live rater. The modified full analysis set included participants treated at least once; the record says observed cases were used for Groups A and B. Its text then begins to describe an imputation approach but is incomplete, so the approach for any other group is not clear from the registry record.

Group-specific primary outcome analyses list 39 evaluable participants for Group A and 49 for Group B, while the pooled treatment analysis lists 117. The registry does not reconcile these analysis counts. This matters because the pooled group combines the two treatment schedules rather than serving as a separate randomized arm. Details of allocation ratios, sample-size justification, the planned statistical analysis, and any interim analyses are not reported in the registry record.

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: Primary effectiveness analysis was done on pooled data.Further supportive explorative analyses done separately by Groups A and B for primary effectiveness outcome measure(OM) and for secondary effectiveness OM 2,but this analysis was not part of main primary effectiveness analysis.As per planned analysis based on protocol and SAP,data for secondary effectiveness outcome measures(3 to 6)were planned to be analyzed for pooled treatment groups,hence pooled data reported for these outcome measures.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The modified full analysis set (FAS) included participants who were treated at least once. Here, overall number of participants analyzed signifies participants who were evaluable for this outcome measure. Modified FAS (observed cases) was used for Groups A and B. Modified FAS (missing data imputed via multiple imputation approach) was used for pooled treatment group.

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: The safety analysis set (SAS) included participants who were randomized to Group A but treated according to the injection scheme of Group B due to COVID-19 pandemic measures and were analyzed in Group B. Participants who were treated only once were analyzed in Group B.

6. Primary Endpoint

The registry lists the primary outcome as Responder Rate for Décolleté Wrinkles According to the Merz Aesthetics Scale (MAS)-At Rest Scale as Assessed by the Blinded Live Rater, measured over 16 weeks after the last treatment on Week 16 (at Week 32).

The primary endpoint is the percentage of participants meeting a response threshold on the Merz Aesthetics Scale for décolleté wrinkles at rest. A responder was defined as having at least a 1-point improvement from baseline to 16 weeks after the last treatment. The assessment was made by a blinded live rater at Week 32. The scale has five categories, ranging from no wrinkles to very severe wrinkles, with higher scores indicating worse outcomes.

A threshold-based responder endpoint is useful because it expresses the result as the proportion of participants who reached a specified degree of improvement on the rating scale. It is distinct from a mean change: two groups could have similar responder percentages while differing in the size of score changes among responders, or could have different percentages despite similar average change. The registry reports the responder definition, but it does not state why this threshold was selected or whether it was considered a clinically important change.

Responder rates need to be read alongside their uncertainty intervals and the analysis population. The reported rates describe participants evaluable for the outcome under the stated analysis approach; they are not automatically estimates for every person enrolled. The scale is specific to wrinkles at rest, so this primary endpoint does not by itself capture the separate dynamic scale outcome or the treatment-satisfaction and global-improvement measures listed as secondary outcomes.

7. Results Posted in the Registry

• Group B: MRZF111 (2 Injections): 83.7% (41/49) versus 71.8% (28/39) on control; risk difference 11.9 percentage points (95% CI -5.6 to 29.4), risk ratio 1.17 (0.92–1.47); unadjusted two-proportion z-test p = 0.179.
• Pooled Treatment Group (Group A: MRZF111 [3 Injections] + Group B: MRZF111 [2 Injections]): 73.5% (86/117) versus 71.8% (28/39) on control; risk difference 1.7 percentage points (95% CI -14.5 to 17.9), risk ratio 1.02 (0.82–1.28); unadjusted two-proportion z-test p = 0.835.

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.

Responder Rate for Décolleté Wrinkles According to the MAS-Dynamic Scale as Assessed by the Blinded Live Rater (Last Observation Carried Forward [LOCF])

• 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:
  • Group B: MRZF111 (2 Injections): 69.4% (34/49) versus 74.4% (29/39) on control; risk difference -5.0 percentage points (95% CI -23.8 to 13.9), risk ratio 0.93 (0.72–1.21); unadjusted two-proportion z-test p = 0.607.
  • Pooled Treatment Group (Group A: MRZF111 [3 Injections] + Group B: MRZF111 [2 Injections]): 65.8% (77/117) versus 74.4% (29/39) on control; risk difference -8.5 percentage points (95% CI -24.7 to 7.6), risk ratio 0.89 (0.71–1.11); unadjusted two-proportion z-test p = 0.322.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group B: MRZF111 (2 Injections) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pooled Treatment Group (Group A: MRZF111 [3 Injections] + Group B: MRZF111 [2 Injections]) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes listed in the registry cover a dynamic wrinkle scale, treatment satisfaction assessed by the investigator and participant, global aesthetic improvement assessed by the investigator and participant, and treatment-related treatment-emergent adverse events. Six secondary outcomes are listed. Numerical arm results are posted for the dynamic-scale responder outcome; numerical results for the other listed secondary outcomes are not reported in the registry record.

The available dynamic-scale results do not show a uniform pattern of higher response in the same schedule across every reported group comparison. Group A's posted rate is 74.4%, Group B's is 69.4%, and the pooled rate is 65.8%. The sponsor's listed test for the pooled group is one-sided, with p < 0.001, while the recalculated unadjusted comparisons do not establish a clear difference between the schedules. These are separate analyses and should not be collapsed into a single conclusion.

The dynamic scale is a different assessment from the primary MAS-At Rest endpoint. It can provide related but not identical information: the primary outcome concerns wrinkles at rest, while the secondary endpoint concerns the dynamic scale. A secondary result cannot replace the primary result, and differences in scale, assessment, or analysis approach can produce different patterns without either measure being a direct confirmation of the other.

Secondary outcomes are often examined as a group, creating a multiplicity concern: the more hypotheses assessed, the greater the chance that at least one result appears noteworthy by chance if no adjustment is made. The registry does not report a multiplicity strategy. The dynamic-scale p-value should therefore be read as a result for that specific listed test, not as decisive evidence across the full family of outcomes. The other secondary measures may broaden the description of participant and investigator assessments, but absent numerical results they cannot be used to confirm or qualify the primary result.

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

• Responder Rate for Décolleté Wrinkles According to the MAS-Dynamic Scale as Assessed by the Blinded Live Rater (Last Observation Carried Forward [LOCF])
• Percentage of Participants With Aesthetic Improvement After the Décolleté Wrinkles Treatments Based on Investigator's Treatment Satisfaction Assessment Scale (LOCF)
• Percentage of Participants With Aesthetic Improvement After the Décolleté Wrinkles Treatments Based on Participant's Treatment Satisfaction Assessment Scale (LOCF)
• Percentage of Participants With Global Aesthetic Improvement Based on the Investigator's Global Aesthetic Improvement Scale on Décolleté Wrinkles (iGAIS-Wrinkles) as Assessed by the Treating Investigator (LOCF)
• Percentage of Participants With Global Aesthetic Improvement Based on the Subject's Global Aesthetic Improvement Scale on Décolleté Wrinkles (sGAIS-Wrinkles) as Assessed by the Participant (LOCF)
• Percentage of Participants With at Least One Treatment-related Treatment-emergent Adverse Event (TEAE)

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the quantities reported for this outcome. The primary outcome is binary at the participant level: a participant either meets the responder threshold or does not. A responder rate is the number of responders relative to the number analyzed, expressed as a percentage. A confidence interval describes uncertainty around an estimated rate or difference under the assumptions of the method used. It is not a range guaranteed to contain the true value, and it does not account for every possible source of bias or data-quality problem.

What does a risk difference express?

A risk difference compares two response proportions by subtracting one proportion from the other. The posted recalculations express the difference as a proportion, with values near zero indicating little estimated separation. Positive values indicate a higher response proportion in the named comparison group than in Group A; negative values indicate a lower proportion. The interval around a risk difference conveys the range of differences compatible with the data and method. If it includes zero, the data do not clearly distinguish the groups on that measure at the usual two-sided significance level. That does not prove the groups are identical.

The posted risk differences and their intervals are simple unadjusted recalculations from summary results. They do not incorporate participant-level covariates or any adjustment described in a sponsor analysis. The registry's reported pooled analysis uses a one-sided binomial test, whereas the recalculated comparisons use risk differences and unadjusted p-values. A p-value from one procedure should not be read as if it tested the same contrast as another procedure. The null hypothesis for the sponsor's binomial test is not reported, so its exact interpretation is limited.

Why do the analysis groups matter?

Randomization supports comparisons between the groups as assigned, provided the analysis preserves the randomized comparison and the analysis population is clear. The primary-outcome description states that the modified full analysis set included participants treated at least once and that the analyzed number refers to participants evaluable for the outcome. It further says observed cases were used for Groups A and B. The remaining description of missing-data handling is truncated. The record therefore does not fully establish how missing outcome values were handled across all displayed groups.

Observed-case analyses use values available for participants with an observed endpoint; participants without an evaluable result may not contribute to that particular estimate. If missingness is related to outcome or treatment experience, an observed-case rate can differ from the rate that would have been seen with complete follow-up. This is a general statistical concern, not evidence that missingness was related to outcome in this study. The registry does not report enough detail to assess the assumptions behind its imputation wording or the extent of missing outcome data.

The reported counts also need care. The primary results list 39 analyzed participants in Group A and 49 in Group B, and 117 in the pooled treatment group. The record does not explain how those counts relate to the stated analysis population or resolve the apparent inconsistency. Without a reconciliation, the pooled result cannot simply be treated as a combined estimate derived from the two displayed group-specific analyses.

What does a confidence interval add?

A confidence interval communicates statistical precision in a way that a point estimate alone cannot. A relatively narrow interval indicates less sampling uncertainty under the method; a broad interval indicates greater uncertainty. For a difference, an interval spanning zero is compatible with no difference as well as with differences in either direction. For a rate, the interval reflects uncertainty about the underlying proportion. Neither interval accounts for systematic error, such as biased outcome assessment, an unsuitable analysis population, or an undocumented departure from the planned analysis.

Here, evaluator blinding is part of the study description and the primary endpoint is based on a rater's scale assessment. Blinding can reduce the risk that knowledge of group assignment influences an assessment, but the registry does not report masking details beyond evaluator blinding and single masking. The record also does not report the statistical model, confidence-interval construction method, or any adjustment for covariates.

Why can over-dispersion matter?

General statistical explanation: a simple binomial model treats participant outcomes as independent observations with a common underlying response probability within a group. Over-dispersion means that observed variation is greater than that model expects. It can arise in some settings when outcomes are more alike within clusters than across clusters, or when participant risks differ more than a simple model assumes. If over-dispersion is present but ignored, standard errors may be too small and confidence intervals may be too narrow. The registry does not report whether over-dispersion was assessed or whether a model that allows it was used; the posted endpoint is a responder percentage and the sponsor's listed test is a one-sided binomial test.

Randomization, blinded evaluation, analysis-population definitions, and missing-data handling address different sources of uncertainty. None replaces the others. Randomization concerns allocation; blinding concerns assessment or behavior; the analysis population defines who contributes to an estimate; and the statistical method determines how sampling uncertainty is quantified. Details about the original statistical plan, interim analyses, and sample-size justification are not reported in the registry record, so it is not possible to verify whether the posted analysis follows the original plan.

11. Confidence Intervals and Precision

The group-specific primary response estimates have visible uncertainty. Group A's rate is 71.8%, with a 95% confidence interval from 56.2% to 83.5%; Group B's rate is 83.7%, with an interval from 71.0% to 91.5%. The intervals overlap substantially. Overlap is not itself a formal test of a difference, but it signals that the individual estimates are not sharply separated relative to their uncertainty.

The recalculated Group B versus Group A risk difference is 0.119, and its 95% confidence interval ranges from -0.056 to 0.294. Because the interval crosses zero, it is compatible with no difference and also with differences in either direction. The unadjusted p-value is 0.179. These results do not provide strong precision for the size or direction of a schedule contrast.

For the pooled-group comparison with Group A, the recalculated risk difference is 0.017, with a 95% confidence interval from -0.145 to 0.179. This interval is also broad and crosses zero. The pooled group includes Group A, so this comparison has a structural overlap that differs from a comparison of two independent randomized arms. Its numerical precision should not be mistaken for a clean estimate of a separate treatment contrast.

Confidence intervals represent sampling uncertainty under the statistical procedure, not certainty about all sources of uncertainty. They do not resolve the inconsistent analysis counts, clarify the incomplete missing-data description, or demonstrate that an unreported analysis plan was followed. The sponsor's reported binomial-test result is a different analysis and does not supply a confidence interval in the registry record. Overall, the posted rates are informative descriptions, while the comparative estimates remain imprecise and should be interpreted cautiously.

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 planning figures are participants per arm, not total events. They are planning illustrations based on the observed effect, rather than the original trial design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were present. The 90% power column gives the corresponding number per arm for a higher chance of detection. These are prospective design calculations, not evidence about whether the completed study had enough power for its observed result. They are not observed power.

The rows that plan for 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the planned sample size. Smaller effects are harder to distinguish from sampling variation, so detecting them generally requires more participants. This is a general feature of power calculations, not a claim that any particular effect is true or clinically important.

The posted planning figures are based on recalculated observed contrasts, which are uncertain estimates. A planning exercise based on an unstable or small observed effect can produce very large sample-size estimates, and those estimates should not be read as a recommendation or as the registry's original target. The planning assumptions do not address the inconsistency in the displayed analysis counts, the pooled group's overlap with Group A, or the incomplete missing-data description. Any sample-size curve should be read as illustrating the relationship between assumed effect size and required enrollment under the stated assumptions, not as an observed trial outcome.

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 = 0.718; treatment proportion p₁ = 0.837; average p̄ = 0.777.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5884 = 1.1532.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5823 = 0.4901.
4. n = (1.1532 + 0.4901)² / (0.1188)² = 191.4, rounded up to 192 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 <- 0.717948717948718                          # control proportion
p1 <- 0.836734693877551                          # 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(4177212)
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 = 192 (80% power), 256 (90% power)
 75% of observed effect: n per arm = 357 (80% power), 478 (90% power)
 50% of observed effect: n per arm = 839 (80% power), 1,122 (90% power)
power.prop.test: 191.4 
Simulated power at n = 192 per arm: 0.803 (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 lists a sponsor-reported one-sided binomial test for the pooled treatment group, with p < 0.001. It does not report the null value or the detailed hypothesis for that test. The registry also provides group response rates and recalculated unadjusted risk-difference comparisons, including a pooled-group comparison with Group A. These analyses do not necessarily test the same question, so their p-values should not be treated as direct alternatives for a single hypothesis.

The record flags a discrepancy. Under that circumstance, the sponsor's own analysis takes precedence over the simple recalculations for reporting what the sponsor concluded statistically. The recalculated results are useful as transparent, unadjusted contrasts based on posted summary statistics, but they do not reproduce a full sponsor analysis or account for any model, adjustment, or analysis rule that is not described in the registry.

The sponsor analysis is reported for the pooled group, whereas the displayed recalculations compare Group B with Group A and the pooled group with Group A. The pooled group includes both schedules, including Group A; it is not an independent randomized comparator. The registry does not explain the discrepancy or provide sufficient detail to determine whether it reflects different populations, methods, or another issue. The sponsor-reported p-value should therefore be quoted as a registry result, while its precise inferential meaning remains limited by the missing test details.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, groups, or statistical hypotheses. If each test is interpreted without adjustment, the chance of at least one false-positive finding can increase across the set of tests. This is a general statistical issue. The registry lists a primary outcome and six secondary outcomes, and it reports a one-sided binomial test for the pooled primary analysis and another for the dynamic secondary endpoint. A plan for controlling multiplicity, prioritizing outcomes, or treating secondary tests as exploratory is not reported in the registry record.

The record also does not provide a complete statistical analysis plan. The precise null hypothesis for the sponsor's binomial test, the confidence-interval methods, adjustment procedures, covariate models, and any interim analyses are not reported. Without those details, the reported p-values cannot be fully placed in the context of a prespecified testing hierarchy. The recalculated comparisons are explicitly unadjusted and should be read as descriptive statistical contrasts rather than as replacements for the sponsor's planned analysis.

Missing-data handling is another unresolved point. The primary endpoint description says the modified full analysis set consisted of participants treated at least once and that observed cases were used for Groups A and B. The remaining sentence about imputation is incomplete. The registry does not report the amount or reasons for missingness, the assumptions for imputation, or sensitivity analyses examining alternative assumptions. Missing values can affect response estimates if participants with missing outcomes differ systematically from those observed; whether that occurred in this study is not reported.

Analysis populations are not fully reconciled either. The primary results list group-specific analyzed counts and a larger pooled analyzed count, but the registry does not explain the relationship among these figures. Nor does it explain how the pooled analysis was constructed or how its test relates to the two randomized schedules. This limits evaluation of whether all analyses use comparable populations.

These gaps do not establish that the analysis was inappropriate; they mean the registry record does not contain enough detail to assess the relevant choices. The observed-case wording, incomplete imputation description, absence of a reported multiplicity plan, and unreconciled counts should all temper confidence in precise interpretation of the posted inferential results.

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: ankle fracture (2.3%), concussion (2.3%), contusion (2.3%), post-traumatic neck syndrome (2.3%), superficial spreading melanoma stage unspecified (2.3%).

The registry lists serious adverse event information for both schedules. For Group A, 43 participants are listed as at risk and 4 as affected by serious adverse events. For Group B, 74 are listed as at risk and 5 as affected. The listed death count is 0 in each group. The registry also lists other adverse-event counts of 21 among 43 at risk in Group A and 25 among 74 at risk in Group B. These are counts as reported; they do not by themselves establish that an event was caused by MRZF111.

The serious-event terms listed at the top are ankle fracture, concussion, contusion, post-traumatic neck syndrome, superficial spreading melanoma stage unspecified, and vaginal haemorrhage, each reported as 2.3%. The registry record does not provide enough context to determine the timing, clinical course, relatedness, or distribution of every listed term by treatment schedule. These categories should not be interpreted as a complete account of all possible safety outcomes.

The safety counts use at-risk totals that differ from the primary endpoint analysis counts. The registry does not explain the difference. Safety and efficacy analyses can have different populations or follow-up rules, but the specific reason in this study is not reported in the registry record. The counts describe the posted safety information and do not support a causal comparison between schedules on their own.

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

The primary endpoint shows that the registry recorded responder rates of 71.8% for Group A and 83.7% for Group B at the stated follow-up, with the pooled group reported at 73.5%. A responder met the specified threshold of at least a 1-point improvement on the MAS-At Rest scale. These percentages describe the evaluable participants counted in the registry analyses; they are not a direct estimate of benefit relative to no treatment.

The recalculated unadjusted comparison between the two schedules is uncertain. Its risk-difference interval includes zero and permits differences in either direction. The pooled comparison also has an interval including zero, and the pooled group includes Group A, which limits its use as an independent between-arm contrast. The sponsor-reported pooled binomial test is a separate result with an unspecified null value. Because the registry flags a discrepancy, the sponsor's own analysis takes precedence when describing the sponsor's reported finding, while the recalculations remain useful as limited, unadjusted context.

These data do not establish whether either schedule is better than no intervention, because no untreated or placebo arm is listed. They also do not establish that the schedules are equivalent: a non-significant or uncertain comparison is not proof of equal outcomes. Nor does the responder rate indicate how much individual participants improved beyond the threshold, how durable any change was beyond the stated assessment, or how participants valued the change.

The result is also bounded by uncertainty about the analysis population, missing-data handling, and the mismatch between displayed analysis counts. Secondary measures may add perspectives on dynamic wrinkles and aesthetic assessments, but most listed secondary outcomes do not have numerical results in the registry record. Safety counts are descriptive and do not resolve causality. The most defensible interpretation is therefore that the posted record describes response and safety counts under the study's two schedules, while important comparative and methodological questions remain unresolved.

18. Why This Trial Matters Statistically

This study illustrates why a reported response percentage should not be interpreted without its endpoint definition, analysis population, comparator, and uncertainty. The primary outcome is not simply any perceived improvement: it requires at least a 1-point change on a specified rating scale, assessed at a defined follow-up by a blinded live rater. That detail gives the percentages a concrete meaning while also limiting them to this particular scale and threshold.

The randomized comparison is between two active schedules. This is a useful design for asking whether the schedule with an additional injection cycle differs from the schedule with fewer cycles, but it cannot directly estimate treatment effects compared with no intervention. A high responder rate within an active group is not itself evidence that the intervention caused the observed changes, since there is no untreated or placebo comparison in the listed arms.

The record also shows why statistical precision matters. The recalculated risk-difference intervals are broad and include zero, so the displayed data do not sharply distinguish the schedules. A point estimate alone could invite an overly confident reading of the apparent separation in rates. Confidence intervals communicate how much uncertainty remains, while the sponsor analysis and recalculations need to be kept distinct because their hypotheses and methods are not fully aligned in the registry record.

Finally, the discrepancy flag, inconsistent-looking analysis counts, incomplete missing-data description, and unreported multiplicity plan are not merely technical details. They affect how confidently readers can connect the posted results to a particular statistical question. The case is a reminder that transparent reporting of analysis populations and methods is needed to make registry results independently interpretable.

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.

Several limitations are specific to the available registry record. The primary outcome is based on a scale assessment and a responder threshold, but the rationale for the threshold and its clinical importance are not reported. The endpoint captures wrinkles at rest and does not represent every dimension of appearance, treatment satisfaction, or participant experience. The dynamic scale is listed separately, underscoring that the primary measure is not a complete account of all wrinkle-related outcomes.

The listed arms provide no untreated or placebo comparator. As a result, the response rates cannot separate changes associated with the intervention from changes that might occur over time or from other influences. The two schedules also differ in cycle count and timing, but the registry does not state which contrast was the principal design objective or why these schedules were selected.

There are reporting uncertainties in the analysis. The modified full analysis set description is incomplete, and the missing-data sentence ends before the imputation approach is fully specified. The displayed analyzed counts for the group-specific and pooled outcomes are not reconciled. The registry flags a discrepancy, and the sponsor's analysis is not described in enough detail to reproduce its one-sided binomial test or identify its null hypothesis.

The registry does not report a sample-size justification, original design assumptions, full statistical analysis plan, interim analyses, multiplicity handling, or the method used to calculate confidence intervals. Numerical results are also absent for most listed secondary outcomes. Safety counts are not accompanied by enough detail to establish event timing or relatedness. These limitations concern what can be interpreted from the registry record; they do not demonstrate that unreported procedures or information were absent from the conduct of the study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Investigation of the Effectiveness and Safety of MRZF111 in the Treatment of Décolleté Wrinkles — NCT04177212.
• Registry record last updated 2023-12-26; status last verified 2023-12.
• Results first posted 2023-12-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, prospective, multicenter, parallel-group study of MRZF111 for décolleté wrinkles. Participants were assigned to a schedule of 3 injection cycles or 2 injection cycles. The primary outcome was the percentage with at least a 1-point improvement on the MAS-At Rest scale at Week 32, assessed by a blinded live rater.

Posted primary response rates were 71.8% for Group A, 83.7% for Group B, and 73.5% for the pooled treatment group. The sponsor reports a one-sided binomial test for the pooled group with p < 0.001; the null value is not stated. Recalculated unadjusted schedule comparisons have confidence intervals that include zero. The record flags a discrepancy, so the sponsor's own analysis takes precedence over these simple recalculations.

The registry also lists six secondary outcomes, but numerical results are reported for the dynamic-scale responder endpoint only. Serious adverse event counts and several serious-event terms are listed. Missing-data handling, multiplicity procedures, original sample-size assumptions, and the relationship among analyzed counts are not fully reported in the registry record.