A Phase 3 Molluscum Contagiosum Efficacy and Safety Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 3 Molluscum Contagiosum Efficacy and Safety Study (NCT04535531), a randomized phase 3 study. The primary outcome is Complete Clearance of All Treatable MC at Week 12.

2. Clinical Question

This is a question about a binary endpoint: each participant either met the complete-clearance definition at the specified assessment or did not. The recorded comparison estimates the difference in the proportions meeting that endpoint between SB206 and the vehicle/placebo group. The registry also lists related lesion-count outcomes and a complete-clearance outcome at Week 8, which provide additional views of treatment response but are not the designated primary question.

The registry record describes a Phase 3 study with randomized assignment and double masking. It reports enrollment of 891. The study summary describes participants with molluscum contagiosum who were at least 6 months of age; other eligibility details are not reported in the registry record. The clinical question therefore concerns the posted result for the specified study population and outcome, rather than a conclusion about people or settings not described in the record.

3. Trial Design

The registry record describes a Phase 3, multicenter, randomized, double-blind, vehicle-controlled, parallel-group study of SB206 10.3% berdazimer and vehicle gel. The study status is completed, and enrollment is recorded as 891. Its summary describes a planned population of up to approximately 850 participants 6 months of age and older with molluscum contagiosum. These are different record fields: the summary’s approximate planned figure should not be substituted for the reported enrollment.

Participants or their caregivers were to apply the assigned topical gel once daily to all lesions identified at baseline and to new treatable lesions arising during the study. Treatment was described as lasting a minimum of 4 weeks and up to 12 weeks. The arm descriptions specify SB206 10.3% berdazimer once daily and vehicle gel once daily. The primary endpoint was assessed at Week 12.

Randomization means that treatment assignment is intended to be allocated by chance, while double masking means the registry describes masking of two parties. The record does not identify who was masked, how the random sequence was generated, or how treatment allocation was concealed. It also does not report the randomization ratio. The sample-size planning illustration uses equal allocation as an assumption for its calculations, but that planning assumption does not by itself establish the trial’s actual allocation procedure.

The primary outcome is listed for the ITT population. The registry record does not provide a fuller definition of the analysis population, details of participant flow, or information about adherence and treatment discontinuation. It lists four secondary outcomes in addition to the primary endpoint. Formal reported analyses are not listed for those secondary outcomes. Protocol details beyond the study description, including the original sample-size justification and statistical analysis plan, 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: Subjects receiving current treatment for MC at the time of the Screening Visit entered a wash out period of up to 14 days prior to randomization.

Overall Study

Analysis population for the primary outcome, as defined in the registry: ITT

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 Complete Clearance of All Treatable MC at Week 12, measured over 12 Weeks.

The primary endpoint is complete clearance of all treatable molluscum contagiosum at Week 12, measured as the number and proportion of participants meeting that criterion in each treatment group. The outcome description says that the count of participants with complete clearance was divided by the number in the corresponding treatment group. This makes the endpoint binary at the participant level: clearance is either recorded or not recorded for the assessment.

A complete-clearance outcome is clinically interpretable as a threshold outcome: it distinguishes participants with no remaining treatable lesions from those who have not met that definition. In statistical terms, it allows comparison of the probability of meeting the endpoint between randomized groups. The registry also reports the group proportions as 0.324 for SB206 and 0.197 for Placebo, with an unadjusted risk difference of 0.128. These estimates describe the posted result; they do not, by themselves, establish the reason for the observed difference.

The endpoint is assessed at a specified time, Week 12, so its meaning is tied to that visit and the registry’s definition of treatable lesions. It does not summarize the timing of clearance, the number of lesions remaining among participants who did not achieve complete clearance, or outcomes after the stated assessment. Those are different questions. The registry record does not report further operational details about how complete clearance was verified, how missing Week 12 assessments were handled, or whether any additional adjudication procedures were used.

Using a participant-level binary endpoint can make the treatment comparison straightforward to interpret, but it also compresses potentially different lesion-count changes into the same outcome category. The separate secondary outcomes address some other dimensions of response, including lesion-count thresholds and assessment at Week 8.

7. Results Posted in the Registry

• SB206: 32.4% (144/444) versus 19.7% (88/447) on control; risk difference 12.7 percentage points (95% CI 7.0 to 18.5), risk ratio 1.65 (1.31–2.07); 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.

A Lesion Count of 0 or 1 of All Treatable MC at Week 12

• 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:
  • SB206: 43.5% (193/444) versus 24.6% (110/447) on control; risk difference 18.9 percentage points (95% CI 12.8 to 25.0), risk ratio 1.77 (1.46–2.14); 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 SB206 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

90% Reduction From Baseline in the Number of All Treatable MC at Week 12

• 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:
  • SB206: 43.0% (191/444) versus 23.9% (107/447) on control; risk difference 19.1 percentage points (95% CI 13.0 to 25.2), risk ratio 1.80 (1.48–2.19); 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 SB206 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Complete Clearance of All Treatable MC at Week 8

• 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:
  • SB206: 19.6% (87/444) versus 11.6% (52/447) on control; risk difference 8.0 percentage points (95% CI 3.2 to 12.7), risk ratio 1.68 (1.23–2.31); 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 SB206 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes show a broadly consistent direction in the posted unadjusted comparisons: each reported binary outcome has a higher observed proportion in the SB206 group than in the Placebo group. They cover different aspects and timing of lesion response, including having a lesion count of 0 or 1 at Week 12, achieving a 90% reduction from baseline at Week 12, and complete clearance at Week 8. The overall pattern aligns with the direction of the primary Week 12 complete-clearance result, while the outcomes remain distinct measures rather than interchangeable versions of the primary endpoint.

These results can add context about how the primary result relates to other response definitions. A lesion-count threshold and a reduction from baseline capture improvement without requiring complete clearance; the Week 8 outcome assesses complete clearance at an earlier time. Agreement in direction across related outcomes can be informative, but it does not independently establish that every endpoint has the same evidential status or interpretation. The outcomes may also be correlated because they assess related aspects of the same condition in the same trial population.

The secondary comparisons are unadjusted recalculations from posted summary counts, and no reported formal analyses are listed for them. Their p-values should therefore be read cautiously. When multiple outcomes are examined, the chance of obtaining at least one small p-value can increase unless the analysis plan accounts for multiplicity. The registry record does not report a multiplicity strategy or identify a hierarchy among the secondary tests. Without that information, the secondary p-values are not a substitute for a prespecified confirmatory analysis.

The secondary findings are best treated as supportive descriptive context rather than as independent proof. Their consistency with the primary direction is notable in describing the posted data, but interpretation should account for the lack of reported multiplicity handling, the absence of formal analyses in the record, and the fact that the outcome definitions answer different questions.

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

• A Lesion Count of 0 or 1 of All Treatable MC at Week 12
• 90% Reduction From Baseline in the Number of All Treatable MC at Week 12
• Complete Clearance of All Treatable MC at Week 8
• Change From Baseline in the Number of All Treatable MC at Week 4

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

For a binary endpoint, each group’s outcome proportion is the number of participants meeting the outcome divided by the number assessed in that group, as described in the registry. The risk difference subtracts one group’s proportion from the other. Its scale is an absolute difference in proportions, rather than a relative comparison. Here the posted proportions are 0.324 for SB206 and 0.197 for Placebo, and the risk difference is 0.128. The order of the groups matters when describing the direction of a difference. The estimate is unadjusted, so it does not reflect covariate adjustment in a model.

A risk ratio expresses the same group comparison as a ratio of probabilities. The registry reports 1.647, with a 95% confidence interval from 1.308 to 2.074. An odds ratio uses odds rather than probabilities; the posted value is 1.958, with a 95% confidence interval from 1.442 to 2.66. These relative measures can sound similar but have different definitions and scales. The odds ratio can be farther from the null value than the risk ratio when the outcome is not rare, so it should not be translated directly into a percentage-point difference.

What does a confidence interval add?

A confidence interval communicates uncertainty around an estimated effect. It is calculated using a method with a stated coverage property over repeated use under its assumptions. It is not a range that assigns a probability to the fixed true value after the data have been observed. For the primary risk difference, the 95% confidence interval is 0.070 to 0.184. Its endpoints describe the range of effect estimates compatible with the observed data under the calculation method and assumptions. A confidence interval does not account automatically for every source of uncertainty, including selection bias, missing data, measurement error, or choices made in analysis.

The posted primary comparison includes an unadjusted p-value of <0.001. A p-value measures how unusual data at least as incompatible with a specified null model would be if that model and the calculation assumptions were true. It does not indicate the probability that the null model is correct, the chance that the observed difference is due to chance, or the clinical importance of the effect. The estimate and confidence interval remain necessary to understand direction, scale, and precision.

Why distinguish reported analyses from recalculations?

The posted group counts and denominators support simple unadjusted comparisons. A recalculation from those summary statistics does not reproduce an analysis that might have used a prespecified model, covariate adjustment, stratification, imputation, or a different missing-data rule. The registry record does not list formal analyses for the primary result, and does not report a detailed statistical plan. The comparisons are therefore best described as unadjusted recalculations from the posted summaries, not as a substitute for an unavailable sponsor analysis. The discrepancy indicator is false; where a discrepancy is flagged, the sponsor’s own analysis takes precedence.

How should the sample-size illustrations be understood?

The planning figures are calculations based on the observed effect, not a report of how the original trial was designed. The stated assumptions are a two-sided significance level 0.05, equal allocation between the arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. Under this illustration, the listed values are participants per arm for the requested power level. The planning figures do not verify that the original trial used those assumptions. Its original sample-size justification and statistical design assumptions are not reported in the registry record.

Power is the probability, under a specified effect and statistical model, of rejecting the null hypothesis using a chosen test procedure. It depends on the target effect, variability or event rates, significance threshold, allocation, and analysis method. A planning calculation asks how many participants would be needed under stated assumptions to achieve a target probability of detecting the assumed effect. Because the figures use fractions of the observed effect, they illustrate how planning changes when the target effect is smaller than the observed estimate. They are not a measure of the probability that the completed trial detected an effect that truly exists.

What is not established by the design label?

Randomized, double-blind, parallel-group describes broad design features, not all safeguards or analysis decisions. The record does not explain the sequence-generation method, concealment, the parties masked, the handling of unmasking, or whether randomization was stratified. The record also does not specify how missing outcomes, protocol deviations, or treatment discontinuation were handled. These details matter because they can affect the risk of bias and the interpretation of an estimate, even when a trial is described as randomized and masked.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.128, and its 95% confidence interval runs from 0.070 to 0.184. The interval stays on the positive side of zero, indicating that the unadjusted calculation is inconsistent with no difference at the conventional two-sided 0.05 threshold. The posted p-value is <0.001. The confidence interval is more informative than the p-value alone for judging the range of effect estimates compatible with the data under the calculation assumptions.

The interval does not mean that the true effect has a 95% probability of falling within these particular endpoints. Rather, the confidence procedure has its stated coverage property over repeated applications when its assumptions hold. Those assumptions are not a guarantee that the estimate is free of bias. The interval reflects statistical uncertainty under the calculation; it does not incorporate uncertainty about endpoint measurement, the analysis population, missing data, or whether the analysis matches the prespecified plan.

The registry also gives relative-effect intervals: 1.308 to 2.074 for the risk ratio and 1.442 to 2.66 for the odds ratio. These intervals likewise exclude their respective no-association values, but their scales differ from the risk-difference scale. The risk-difference interval is especially direct for understanding the absolute contrast in the proportions meeting the endpoint. The relative measures can complement it, but should not replace it.

The width of an interval reflects the amount of information and the variability under the method used. A narrower interval generally indicates greater statistical precision, while a wider interval leaves more uncertainty about the effect’s magnitude. Precision should not be confused with validity: a narrow interval cannot correct systematic bias or an inappropriate analysis. Since the registry does not report the sponsor’s formal primary analysis or details of missing-data handling, the posted interval should be interpreted as precision for the unadjusted comparison based on the available summary counts.

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 expressed as participants per arm, not as a total across the trial. The stated planning assumptions are a two-sided significance level 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The figures are planning illustrations computed from the observed effect; the original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm needed, under those assumptions, for an 80% chance of detecting the assumed effect using the planning calculation. The 90% power column gives the corresponding participants per arm for a 90% chance. These are prospective planning targets under a model, not descriptions of what happened in the completed study. A higher target probability of detection generally requires more participants when the other assumptions stay fixed.

The rows that use 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect ask how planning changes when the target effect is progressively smaller relative to the observed estimate. Smaller effects need more participants to distinguish them from the null under the same significance threshold and other assumptions. The figures therefore help illustrate sensitivity to the target effect; they do not establish the effect that a future study would observe.

This is not observed power. Observed power is sometimes calculated by inserting the effect estimate from a completed study into a power formula, but it is not a useful substitute for interpreting the estimate and its confidence interval. The planning figures are conditional illustrations based on stated assumptions, not evidence that the completed trial had a particular probability of success.

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 = 0.197; treatment proportion p₁ = 0.324; average p̄ = 0.261.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6208 = 1.2167.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6142 = 0.5169.
4. n = (1.2167 + 0.5169)² / (0.1275)² = 185.0, rounded up to 186 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 <- 0.196868008948546                          # control proportion
p1 <- 0.324324324324324                          # 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(4535531)
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 = 186 (80% power), 248 (90% power)
 75% of observed effect: n per arm = 317 (80% power), 423 (90% power)
 50% of observed effect: n per arm = 681 (80% power), 911 (90% power)
power.prop.test: 185 
Simulated power at n = 186 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. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcomes: the primary Week 12 complete-clearance endpoint and secondary measures of lesion count, percentage reduction from baseline, and clearance at an earlier assessment. Testing several outcomes can increase the chance that at least one result appears statistically notable even when no treatment effect exists. Statistical plans often address this issue by defining a hierarchy of endpoints, adjusting significance thresholds, or identifying outcomes as exploratory. The registry record does not report whether any such approach was prespecified, how multiplicity was handled, or which secondary outcomes were intended to be confirmatory.

The posted comparison p-values are unadjusted recalculations. They do not account for testing multiple outcomes. This does not change the arithmetic of an individual comparison, but it changes how a collection of p-values should be interpreted. The primary endpoint is clearly identified as primary in the record, but the absence of a reported multiplicity plan limits conclusions based on secondary p-values.

The primary outcome description identifies the ITT population. The record does not provide the operational definition of ITT, the number included in each analysis beyond the outcome denominators, or a participant-flow account. It also does not report how missing Week 12 assessments were handled, whether participants with missing outcomes were counted as not achieving clearance, or whether imputation or sensitivity analyses were used. Because a binary endpoint depends on outcome classification, missing-data choices can affect the estimated proportions and comparison.

Further details not reported in the registry record include the prespecified statistical analysis plan, treatment of protocol deviations, the handling of intercurrent events, and whether adjusted analyses were planned. The posted summaries allow an unadjusted comparison, but they cannot reveal whether the analysis followed the original plan or how robust the result is to alternative missing-data assumptions. These omissions are important limits on interpreting both the precision and confirmatory status of the estimates.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: supracondylar fracture of right humerus, closed reduction (0.2%).

The adverse-event summary reports serious adverse events for 0 participants in the SB206 group and 1 participant in the Placebo group. It reports 0 deaths in each group. The most frequent serious-event term listed is Supracondylar Fracture of right humerus, closed reduction, at 0.2%. The record does not establish that this event was caused by study treatment, and the term alone does not provide enough detail to assess relatedness or clinical course.

Other adverse events are reported for 221 participants in the SB206 group and 37 in the Placebo group. These are counts of participants affected in the registry’s summary, not a breakdown of event types, severity, duration, or treatment relationship. The record does not provide the individual non-serious event terms or a fuller account of how adverse events were collected and classified.

Safety figures should be read as descriptive counts within the reported groups. They do not establish comparative safety on their own, particularly without detail about event definitions, exposure time, attribution, missing safety data, and statistical analysis. The serious-event and death counts do not replace a complete assessment of the safety profile.

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

The posted data show that the proportion meeting the Week 12 complete-clearance endpoint was higher in the SB206 group than in the Placebo group. The unadjusted risk difference is 0.128, with a 95% confidence interval from 0.070 to 0.184 and a p-value of <0.001. The interval conveys uncertainty about the magnitude of the contrast under the calculation assumptions; the estimate is not a guarantee of the result that would occur in another population or setting.

The result is specific to participants described in this trial, the registry’s definition of treatable lesions and complete clearance, the ITT population listed for the primary endpoint, and the Week 12 assessment. It does not tell when clearance occurred, whether it was sustained after Week 12, or how participants fared beyond the outcomes listed in the record. It also does not answer whether every participant experienced a similar outcome. Group-level proportions cannot describe the individual course of each participant.

A statistically small p-value is not a measure of clinical importance, and it does not establish a treatment mechanism. The absolute and relative effect estimates describe the observed group contrast, while confidence intervals describe statistical uncertainty under their assumptions. Neither can address all possible sources of bias or missing information. The registry record does not report a full analysis plan, detailed missing-data methods, or formal sponsor analyses, so the posted comparison should not be treated as a complete account of every planned analysis.

The safety summary reports serious adverse events and deaths by group, but the available information is not a comprehensive safety assessment. Counts do not establish causation, and the record does not provide detail on event relatedness or exposure-adjusted comparisons. The results therefore describe the outcomes recorded in this trial rather than making a general claim about treatment benefit or harm.

In short, the primary comparison provides evidence of a difference in the posted Week 12 endpoint, with the stated confidence interval showing its estimated precision. Interpreting that difference beyond the trial requires attention to the design, analysis information, endpoint definition, follow-up, and limitations of the registry record.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical endpoint should be interpreted alongside its definition and measurement time. Complete clearance at Week 12 is a clear binary criterion, but it captures a different aspect of response from a reduction in lesion count or a low residual lesion count. The registry includes secondary outcomes that broaden that view, while the primary endpoint remains the designated focus for the main comparison.

It also shows the value of presenting absolute and relative measures together. The risk difference communicates the absolute contrast in proportions, while the risk ratio and odds ratio provide relative comparisons. Reporting the confidence interval alongside the point estimate makes the uncertainty in the estimated effect visible; a p-value alone would not convey the range of plausible magnitudes under the calculation.

The record demonstrates a common distinction between trial results and planning calculations. Planning illustrations based on the observed effect can show how required enrollment changes as the target effect is made smaller, but they are not evidence about the completed study’s observed power and do not recover the original design rationale. Separating those concepts helps prevent a planning exercise from being mistaken for a trial protocol feature.

Finally, the record highlights how much interpretation depends on transparent analysis reporting. The outcome counts permit unadjusted comparisons, but the statistical plan, sponsor analyses, multiplicity approach, and missing-data handling are not reported. Those details are relevant to determining whether the posted estimates match the prespecified analysis and how confidently secondary findings can be interpreted. A statistically informative result is strongest when the estimate, uncertainty, outcome definition, and analysis choices can all be evaluated together.

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.

Important study-specific details are absent from the registry record. Although the trial is described as randomized and double-blind, the record does not report sequence generation, allocation concealment, which parties were masked, or how masking was maintained. These omissions limit independent assessment of potential selection and measurement biases. The record also does not explain whether randomization was stratified or describe the actual allocation ratio.

The primary endpoint is described as complete clearance of all treatable lesions at Week 12, but further operational details about lesion assessment and verification are not reported. The record does not provide participant flow, adherence, discontinuation, or protocol-deviation information. It identifies the primary population as ITT without reporting a fuller definition or the handling of missing Week 12 outcomes. Those issues may affect interpretation of the group counts and estimated proportions.

The registry record does not list a formal analysis for the primary endpoint or any reported analyses for the secondary outcomes. It does not provide the prespecified statistical analysis plan, the original sample-size justification, or a multiplicity strategy. The unadjusted comparisons recalculated from summary counts therefore should not be assumed to reproduce the sponsor’s planned analysis. The discrepancy indicator is false, but that does not supply missing analysis details.

Safety information is also limited: the registry provides counts of participants with serious and other adverse events, deaths, and a leading serious-event term, but not event-level detail, exposure duration, attribution, or a comprehensive safety analysis. Finally, the outcome summaries concern the specified assessments and do not report follow-up beyond the stated time points. These limitations do not erase the posted findings, but they constrain their interpretation and generalization.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Phase 3 Molluscum Contagiosum Efficacy and Safety Study — NCT04535531.
• Registry record last updated 2023-01-26; status last verified 2022-11.
• Results first posted 2023-01-26.
• 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.

22. Record Summary

NCT04535531 is a completed Phase 3, multicenter, randomized, double-blind, vehicle-controlled, parallel-group study of SB206 10.3% berdazimer and vehicle gel in participants with molluscum contagiosum. The registry reports enrollment of 891 and describes once-daily topical application for a minimum of 4 weeks and up to 12 weeks.

The primary endpoint was complete clearance of all treatable molluscum contagiosum at Week 12 in the ITT population. The posted counts were 144.0 of 444.0 for SB206 and 88.0 of 447.0 for Placebo. The unadjusted risk difference was 0.128, with a 95% confidence interval from 0.070 to 0.184 and p < 0.001.

The registry also reports secondary outcomes and descriptive adverse-event counts. Formal analyses, the original sample-size rationale, multiplicity handling, and missing-data methods are not reported in the registry record.