Cantharidin Application in Molluscum Patients-1: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cantharidin Application in Molluscum Patients-1 (NCT03377790), a randomized phase 3 study. The primary outcome is Percentage of Subjects Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 84 Visit (EOS).

2. Clinical Question

3. Trial Design

The registry identifies this as a Phase 3, randomized, double-blind, placebo-controlled pivotal study. It used a parallel-group model and records masking as quadruple; the official title describes the study as double-blind. The registry does not explain which roles were masked or how masking was implemented. Participants were assigned to VP-102 or placebo, with the groups compared on efficacy and safety outcomes.

The study included participants with molluscum contagiosum who were 2 years and older. The stated enrollment was 266. The registry lists 160 participants in the VP-102 arm and 106 in the placebo arm for the primary outcome. It does not report the allocation ratio or a detailed account of participant flow, so those aspects should not be inferred from the arm counts alone.

The treatment summary describes topical applications to treatable lesions once every 21 days for up to 4 applications. The primary assessment compared baseline and new lesions with lesion status at the Day 84 end-of-study visit. Other clearance assessments were recorded at Day 21, Day 42, and Day 63. These repeated assessments describe clearance status at particular visits; they do not, by themselves, establish when clearance occurred or whether it persisted after a visit.

The record lists a study start date of 2018-03-21 and a primary completion date of 2018-11-26. Its status is completed. The sponsor is Verrica Pharmaceuticals Inc. The registry record does not report the trial's original sample-size justification or the full statistical analysis plan. Those omissions limit what can be concluded about the intended design assumptions, analysis procedures, or planned handling of results beyond the information explicitly recorded.

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

Reasons for not completing this period:

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

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: ITT Population

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Subjects Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 84 Visit (EOS), measured over Day 1 (Baseline and new) compared to Day 84 (EOS).

The primary endpoint is the percentage of participants exhibiting complete clearance of all treatable molluscum lesions, including lesions present at baseline and new lesions, at the Day 84 end-of-study visit. The outcome description identifies the ITT Population. The posted arm results are counts: 74 participants in the VP-102 group and 19 in the placebo group met the endpoint, with arm denominators of 160 and 106, respectively.

Complete clearance is a binary outcome: each participant either meets the stated all-lesions-clear criterion at the assessment or does not. In general, a binary endpoint can make the clinical target relatively direct to interpret, especially when the outcome requires clearance of all lesions designated as treatable. It also compresses a potentially varied lesion burden into a single participant-level response. It does not describe how many lesions remained for participants who did not meet the endpoint, or how much improvement occurred short of complete clearance.

The endpoint is assessed at a specific visit, rather than continuously. It therefore addresses clearance status at Day 84 and does not establish the timing of clearance between visits or its persistence after the assessment. The record does not report a rationale for selecting this endpoint or additional detail about how treatable lesions were defined. Those details matter when assessing how the endpoint was operationalized, but should not be assumed from its title.

7. Results Posted in the Registry

• VP-102: 46.2% (74/160) versus 17.9% (19/106) on control; risk difference 28.3 percentage points (95% CI 17.7 to 39.0), risk ratio 2.58 (1.66–4.01); 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 Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 63 Visit

• 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:
  • VP-102: 31.9% (51/160) versus 17.0% (18/106) on control; risk difference 14.9 percentage points (95% CI 4.7 to 25.1), risk ratio 1.88 (1.16–3.03); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for VP-102 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Subjects Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 42 Visit

• 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:
  • VP-102: 20.6% (33/160) versus 9.4% (10/106) on control; risk difference 11.2 percentage points (95% CI 2.8 to 19.6), risk ratio 2.19 (1.13–4.25); unadjusted two-proportion z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for VP-102 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Proportion of Subjects Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 21 Visit

• 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:
  • VP-102: 11.2% (18/160) versus 3.8% (4/106) on control; risk difference 7.5 percentage points (95% CI 1.4 to 13.6), risk ratio 2.98 (1.04–8.56); unadjusted two-proportion z-test p = 0.030.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for VP-102 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary clearance assessments follow a consistent overall pattern: the posted group comparisons favor VP-102 at the earlier visits as well as at the primary Day 84 assessment. The reported sponsor analyses and the unadjusted recalculations also show evidence of group differences across these secondary outcomes. Taken together, the pattern is directionally aligned with the primary result rather than suggesting a reversal at an earlier assessment.

These are separate snapshots of complete clearance at scheduled visits. They provide information about the timing of observed clearance status across the study assessments, but do not establish the precise time of response between visits or whether clearance persisted after any assessment. The pattern across visits adds context to the primary endpoint, while the Day 84 outcome remains the designated primary question in the registry record.

The secondary findings should carry less weight than the primary result because multiple outcomes and assessment times create opportunities to observe apparently notable differences by chance. The registry record does not report a multiplicity adjustment or a testing hierarchy for these secondary outcomes. The p-values should therefore be treated as unadjusted evidence, not as confirmatory findings protected against the increased false-positive risk from examining multiple comparisons. The record also identifies only three posted secondary clearance outcomes, while other outcome measures are not described in the results summarized for these comparisons. Their absence from the available results does not establish that they were not measured.

In general, secondary endpoints can help describe whether the primary pattern is coherent across related measures and timepoints. They do not independently validate the primary finding when their analysis plan and multiplicity handling are unknown. Their interpretation is most appropriately supportive and exploratory, with attention to the same limits on endpoint definition, missing data, and precision that apply to the main result.

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

• Percentage of Subjects Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 63 Visit
• Percentage of Subjects Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 42 Visit
• Proportion of Subjects Exhibiting Complete Clearance of All Treatable Molluscum Lesions (Baseline and New) on the Day 21 Visit

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: complete clearance either occurred by the endpoint definition at the assessment or it did not. The posted arm values are counts of participants meeting the criterion, alongside the corresponding arm sizes. A proportion is the natural way to describe a binary outcome because it relates the event count to the number assessed in that group. The primary comparison then asks whether those group proportions differ. The registry's endpoint title uses the word “percentage,” while the posted results are represented as participant counts; no percentage conversion is needed to understand the reported comparison.

What does a risk difference mean?

A risk difference is the proportion with the outcome in one group minus the proportion with the outcome in the comparison group. It expresses an absolute contrast on the probability scale. A positive estimate for VP-102 versus placebo means the observed outcome proportion is higher in the VP-102 group. Unlike a relative measure, the risk difference makes the magnitude of the absolute separation the focus. Its value depends on the event proportions in both groups, so it should be read together with the arm counts and denominators.

The recalculated risk difference uses the posted summary counts and is unadjusted: it does not account for covariates or other model terms. The registry record does not report adjusted covariate results for the primary outcome. An unadjusted comparison can be informative for a randomized study, but the result remains a summary contrast and does not describe potential variation across participant subgroups.

How should the confidence interval be read?

A confidence interval conveys statistical uncertainty around an estimate. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. The interval is not a range containing a fixed proportion of individual participant outcomes, and it is not a probability statement about the particular estimate after the data have been observed. It is a repeated-sampling concept: under the method's assumptions, intervals constructed in the same way would cover the target parameter at the stated confidence level with the stated long-run frequency. The confidence level for the recalculated risk difference is not specified in the registry record, so it should not be assigned by assumption.

For the primary recalculation, the reported interval for the risk difference is entirely above zero. This agrees with the direction of the point estimate and indicates that zero difference is not included in the interval as reported. The interval still allows a range of possible effect sizes, so the point estimate should not be treated as exact. Confidence intervals also do not address systematic problems such as outcome misclassification, incomplete follow-up, or a mismatch between the trial population and a population of interest.

What does the p-value add?

The p-value measures how unusual results at least as incompatible with the null hypothesis as the observed result would be, assuming the null hypothesis and the test's conditions. It is not a measure of treatment effect size and does not state the probability that a finding is due to chance. The sponsor reports a chi-squared test for the primary comparison. The recalculation reports an unadjusted p-value based on the posted counts. Both p-values are small, but the effect estimate and its interval remain important for understanding magnitude and precision.

A chi-squared test evaluates an association between group and binary outcome under its assumptions. In general, this test compares observed outcome counts with counts expected under a no-association model. The registry does not provide enough methodological detail to determine whether any continuity correction or alternative test was considered. The sponsor's recorded method is described as chi-squared; more specific implementation details are not reported in the registry record.

Why distinguish relative from absolute effects?

The posted recalculation also includes relative measures, such as a risk ratio and an odds ratio. A risk ratio compares proportions as a ratio; an odds ratio compares odds. These measures answer different descriptive questions from a risk difference. Relative measures can appear large even when absolute differences are modest, or the reverse, depending on the underlying event frequency. Odds are not the same as probabilities. No single measure is sufficient in every context, so the absolute contrast, group counts, and relative contrasts should be interpreted together rather than treated as interchangeable.

General statistical interpretation also depends on the study's analysis population and missing-data handling. The primary endpoint identifies the ITT Population, but the registry record does not state how missing endpoint observations were handled or whether all randomized participants had outcome data. It also does not report the detailed analysis plan. Those unreported procedures can affect how directly the posted results represent the randomized comparison. They should be treated as uncertainties in the record, not filled in with presumed trial practices.

11. Confidence Intervals and Precision

The primary risk-difference recalculation has a reported confidence interval from 0.177 to 0.390. The interval lies above zero, which is consistent with the positive direction of the estimated contrast. Its span also shows that the data do not identify a single exact value for the underlying difference. The estimate is therefore more informative when read with the interval than when read as a point estimate alone.

Precision and statistical significance are related but not identical. An interval that excludes zero can correspond to evidence against a zero-difference hypothesis under the method used, while the interval's width indicates how uncertain the effect magnitude remains. A p-value cannot replace that information: it addresses compatibility with a null model, not the range of plausible effect sizes. Nor does a confidence interval account for every source of uncertainty, such as unreported missing-data procedures, outcome measurement issues, or limited generalizability.

Because complete clearance is a binary participant-level endpoint, the estimate depends on the number of participants and the distribution of event counts across the arms. The arm denominators are 160 and 106, and the event counts are 74 and 19. The registry record does not report a separate precision target for the trial's original design. The uncertainty interval is thus best understood as precision around the posted comparison, not evidence that all relevant sources of uncertainty have been captured.

The interval's confidence level is not specified in the registry record. It should not be labeled with a particular confidence percentage based on assumption. The reported bounds nevertheless provide a range for reading the recalculated estimate, conditional on the interval method. The result supports a positive group contrast in the posted data, while leaving uncertainty about its precise size and about what would be observed in other populations or follow-up periods.

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 events. They are illustrations based on the observed primary effect and the assumptions stated for the planning calculation: a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The original trial design assumptions and sample-size justification are not reported in the registry record. These planning figures therefore should not be read as a description of how the trial was designed.

The 80% power column represents the number of participants per arm estimated to give an 80% chance of rejecting the null hypothesis under the planning assumptions if the specified effect were the true effect. The 90% power column has the same interpretation with a higher target probability of detecting that effect. These are design-planning probabilities under a model, not guarantees about the outcome of a particular study. They depend on the assumed event rates and effect size as well as the stated calculation method.

Rows that plan for 100% of the observed effect use the full observed primary contrast as the target. Rows planning for 75% or 50% of that effect set smaller target contrasts. Smaller effects are generally harder to distinguish from random variation, so they require more participants per arm under otherwise comparable assumptions. This is why the planning counts increase as the target fraction of the observed effect decreases. The values are not observed power; observed power is not a useful substitute for reading the estimate and its uncertainty after results are available.

The planning exercise is an illustration of how sample requirements depend on the effect chosen for detection. It does not establish that the observed effect is the true or reproducible effect, and the trial's own planned effect size is not reported in the registry record. The calculations also do not establish whether the actual recruitment target included allowances for missing outcomes or other design considerations.

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 = 0.179; treatment proportion p₁ = 0.463; average p̄ = 0.321.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6602 = 1.2939.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6291 = 0.5294.
4. n = (1.2939 + 0.5294)² / (0.2833)² = 41.4, rounded up to 42 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 <- 0.179245283018868                          # control proportion
p1 <- 0.4625                          # 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(3377790)
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 = 42 (80% power), 55 (90% power)
 75% of observed effect: n per arm = 70 (80% power), 93 (90% power)
 50% of observed effect: n per arm = 146 (80% power), 195 (90% power)
power.prop.test: 41.4 
Simulated power at n = 42 per arm: 0.813 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor reports a chi-squared superiority analysis for the primary comparison, with p < 0.001. The unadjusted recalculation from the posted counts gives p < 0.001 and a positive risk difference whose reported confidence interval is above zero. The reported p-values differ in their displayed precision and thresholds, but they point in the same direction and both indicate a statistically notable contrast under their respective analyses.

The registry record does not report a numerical sponsor estimate or confidence interval for the primary comparison, nor does it give enough detail to reproduce the sponsor's full analysis procedure. The recalculated risk difference is therefore a simple unadjusted analysis of the posted group counts, not a replacement for the sponsor's analysis. The discrepancy flag is false, so the record does not identify a conflict between the recalculation and the posted sponsor result. The sponsor's own analysis remains the primary reported analysis, while the recalculation offers a transparent summary of the absolute difference from the counts.

Differences in p-value display can arise from calculation and reporting choices, and the registry record does not describe the exact choices behind each result. The numerical distinction should not be taken to imply a substantive disagreement: both results indicate a positive comparison favoring VP-102 on this endpoint. Neither p-value alone conveys effect magnitude, precision, or the implications of unreported analysis details.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when more than one hypothesis is tested. Each test has a chance of producing a low p-value even when there is no true group difference for that particular outcome. As the number of comparisons increases, the chance of at least one apparently notable result can increase unless the analysis plan accounts for it. The registry record lists a primary endpoint and three secondary clearance endpoints at different visits. It does not report whether any family-wise error control, false-discovery procedure, gatekeeping strategy, or other multiplicity adjustment was used.

The primary endpoint is the clearest basis for interpretation because it is designated as primary in the record. The secondary results may add descriptive context, but their p-values should not be treated as confirmatory without knowing how the trial planned to handle multiple testing. The registry record also does not report a hierarchy specifying whether secondary tests were contingent on the primary result. Such a hierarchy should not be inferred from the sequence of visit days or the pattern of results.

The primary endpoint names the ITT Population. The registry record does not provide detailed information on the analysis population construction, participant disposition, or whether all randomized participants contributed an endpoint result. It does not report how missing Day 84 observations were handled, whether imputation was used, or whether sensitivity analyses evaluated alternative assumptions. Missing outcomes can affect a binary response comparison if missingness differs across groups or relates to the likelihood of clearance. The direction and size of any such effect cannot be determined from the record.

Other elements of the statistical plan are also not reported in the registry record, including a detailed sample-size justification, planned interim analyses, and the full model or test specifications beyond the reported chi-squared analysis. This does not demonstrate that these procedures were absent; it means the registry record does not establish them. Interpretation should distinguish what is recorded from what remains unknown, especially when considering the strength of secondary evidence or the sensitivity of results to unreported analysis choices.

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: serious treatment emergent adverse events (1.0%).

The safety record lists serious treatment-emergent adverse events as affecting 0 participants at risk of 161 in the VP-102 group and 1 participant at risk of 104 in the placebo group. It lists 0 deaths in each group. The record also gives a top serious-event term of “Serious Treatment Emergent Adverse Events” at 1.0%. These are the posted serious-event figures; they do not, on their own, establish a comparative safety profile or explain the clinical circumstances of the event.

The denominators in the safety summary differ from those listed for the primary efficacy endpoint. Safety and efficacy populations can differ, and the registry record does not explain the participant-level reasons for the different at-risk counts. The serious-event counts are small, so estimates of uncommon harms would be imprecise. A count of zero in one group does not establish that an event cannot occur, and the one event recorded in the other group does not establish that the study treatment caused it.

The record lists other treatment-emergent adverse events in 159 participants at risk of 161 for VP-102 and 76 participants at risk of 104 for placebo. Those broader events are not equivalent to serious adverse events. Interpretation of safety should consider definitions, duration of observation, event types, severity, and attribution, but further detail on these matters is not reported in the registry record. No medical advice or treatment conclusion follows from these summary counts alone.

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

The posted primary results show a higher observed complete-clearance proportion in the VP-102 arm than in the placebo arm at Day 84. The direction is supported by the sponsor's reported chi-squared analysis and by the unadjusted recalculation from the posted counts. The estimated absolute contrast is positive, and its reported interval excludes zero. These results describe the trial's recorded endpoint and analysis; they do not resolve every question about the magnitude, durability, or broader applicability of the outcome.

Complete clearance is a stringent all-or-none participant-level outcome. A participant who did not meet that criterion may still have experienced some reduction in lesions, but the primary endpoint does not quantify partial improvement. The result also refers to clearance at the Day 84 assessment. It does not establish the timing of clearance between visits, its persistence after the visit, or effects on outcomes that were not reported.

The comparison is specific to the study population, intervention, placebo, and treatment schedule recorded in the registry. Generalizing beyond participants 2 years and older with molluscum contagiosum or beyond the study procedures requires evidence beyond this endpoint summary. The record does not report all eligibility details, missing-data procedures, multiplicity handling, or the full statistical analysis plan. These uncertainties affect how completely the results can be evaluated.

A statistically notable difference is not synonymous with a guarantee of benefit for an individual participant, and a p-value does not measure clinical importance. The estimates are group summaries and do not predict an individual outcome. Likewise, the serious adverse-event counts are too limited to settle questions about uncommon safety outcomes. The results support a statistical description of the observed comparison; they do not establish that every relevant outcome has been measured or that the same pattern will hold in other circumstances.

18. Why This Trial Matters Statistically

This trial offers a clear example of how to interpret a binary clinical endpoint alongside its absolute group contrast. Complete clearance is expressed at the participant level, while the risk difference puts the separation between groups on an absolute probability scale. Reading the event counts, arm sizes, estimate, and uncertainty together is more informative than relying on a p-value alone.

The repeated clearance assessments also illustrate the distinction between a primary endpoint and related secondary outcomes. The earlier assessments provide descriptive context for the pattern over scheduled visits, but their multiplicity makes unadjusted p-values less definitive. This distinction is central to avoiding overstatement when several related outcomes are reported.

The record also highlights the difference between sponsor analyses and simple recalculations from summary data. The sponsor reports a chi-squared test, while the recalculation makes the absolute contrast explicit. Because the registry does not include the sponsor's numerical effect estimate or full analysis details, the recalculation aids interpretation but cannot reproduce every aspect of the original analysis.

Finally, the sample-size illustrations demonstrate how planning requirements depend on the target effect and power goal. They are not evidence about the trial's original design or a post-study measure of success. Together, the efficacy, uncertainty, multiplicity, and planning issues show why statistical interpretation requires more than deciding whether a single p-value crosses a threshold.

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 record leaves several trial-specific details unavailable. It does not report the original sample-size justification, the intended effect size for design, or the full statistical analysis plan. The planning illustrations based on the observed effect cannot fill those gaps. Details of randomization implementation, allocation ratio, masking roles, and participant flow are also not reported. The record labels masking as quadruple while the official title calls the trial double-blind, without explaining the distinction.

The primary result is reported as counts and a recalculated risk difference, but the registry does not provide a sponsor-reported effect estimate with its own confidence interval. Nor does it explain the difference between the safety denominators and the efficacy arm sizes. Without participant disposition and endpoint-completion details, the impact of missing data cannot be assessed. The ITT Population is named, but missing endpoint handling and sensitivity analyses are not reported.

Three secondary clearance outcomes are posted, but the registry does not state whether statistical testing was adjusted for multiple comparisons or ordered hierarchically. This limits the confirmatory interpretation of those results. The endpoint itself is defined around complete clearance of treatable baseline and new lesions, but the record does not describe the operational criteria for treatability or the process used to assess clearance. It also does not provide detailed results for every outcome measure listed in the record.

The follow-up assessment described for the primary endpoint is Day 84. The registry result does not address longer-term persistence or recurrence. The safety summary gives serious-event counts and a broader adverse-event count, but does not provide detailed event narratives or enough context to make causal assessments. These limitations do not negate the posted comparison; they define what can and cannot be concluded from the recorded results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Cantharidin Application in Molluscum Patients-1 — NCT03377790.
• Registry record last updated 2022-01-11; status last verified 2021-12.
• Results first posted 2021-12-14.
• 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

NCT03377790 is a completed, randomized, parallel-group Phase 3 study of topical VP-102 versus placebo for molluscum contagiosum in participants 2 years and older. The study summary describes applications once every 21 days for up to 4 applications. The primary outcome was complete clearance of all treatable baseline and new lesions at Day 84 in the ITT Population.

The posted primary counts are 74 of 160 for VP-102 and 19 of 106 for placebo. The unadjusted recalculation gives a positive risk difference, with a reported confidence interval above zero and p < 0.001; the sponsor reports a chi-squared result of p < 0.001. Earlier secondary clearance assessments follow the same direction, but multiplicity handling is not reported. Serious adverse events were recorded for 0 participants in the VP-102 safety group and 1 in the placebo safety group, with 0 deaths in either group.