Study of A-101 for the Treatment of Seborrheic Keratosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of A-101 for the Treatment of Seborrheic Keratosis (NCT02260180), a randomized phase 2 study. The primary outcome is Percentage of PLA Responders With Target Lesion Clear (PLA = 0) in Each Arm at Visit 8..

2. Clinical Question

This is a question about a particular lesion assessment at a particular visit. It is not a direct measure of every lesion, overall skin condition, or longer-term status. The record also describes a secondary question about mean change from baseline in PLA score at Visit 8. Together, these outcomes permit a comparison of a categorical clear-lesion endpoint and a change in the scale score, but the registry record does not report how many target lesions were assessed per participant or how target lesions were selected.

The record lists 119 enrolled participants and three randomized parallel arms. Its title identifies the study as a dose-response study, while the primary comparisons reported are each concentration versus vehicle. A direct statistical comparison between the two active concentrations is not reported in the registry record. Thus, results for each concentration against vehicle should not be read as a formal test that one concentration is superior to the other.

3. Trial Design

The registry record describes a randomized, double-blind, parallel-group Phase 2 study. It was marked completed, with enrollment of 119. The record gives a start of 2014-10 and primary completion of 2015-03. The sponsor was Aclaris Therapeutics, Inc.

There were three arms: A-101 40% topical solution, A-101 32.5% topical solution, and A-101 0% topical solution, the vehicle control. The reported primary-outcome groups included 37 participants in the 40% arm, 39 in the 32.5% arm, and 40 in the vehicle arm. The registry record’s adverse-event risk sets are not identical to those primary-outcome group sizes. Reasons for differences in the reported denominators are not reported in the registry record.

Randomization indicates that assignment was intended to be determined by chance; double masking indicates that the record classifies the study as double-blind. The identities of the masked parties and the randomization procedure are not reported in the registry record. The parallel-group model means the reported arms represent separate groups rather than a crossover comparison.

The stated purpose was to evaluate safety and dose-response for two A-101 concentrations versus vehicle in seborrheic keratosis. The primary outcome was the percentage with a target lesion judged clear at Visit 8, with the timeframe given as Day 106. A secondary outcome was mean change from baseline PLA score at Visit 8, also at Day 106. The registry record does not report the original sample-size justification, the detailed protocol, or the planned analysis population.

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:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of PLA Responders With Target Lesion Clear (PLA = 0) in Each Arm at Visit 8., measured over Day 106.

The primary endpoint is the percentage of participants in each arm whose target lesion was judged clear at Visit 8. The criterion was PLA = 0. The registry record describes the Physician’s Lesion Analysis as a four-point scale from 0 to 3, where 0 means lesion clear and 3 means the most severe lesion. For this endpoint, the response is therefore a yes-or-no classification based on whether the target lesion received the clear score.

This type of endpoint is useful because it expresses the result in a clinically interpretable form: the proportion meeting a specified lesion-status criterion. The reported counts are the number classified as clear and the number in the arm for that outcome. The primary comparison asks whether that proportion differed between each A-101 concentration and vehicle. The endpoint does not measure the full distribution of PLA scores, and it does not by itself describe change in every lesion or a participant’s overall condition.

The primary assessment was at Visit 8, with a timeframe of Day 106. The record does not explain how missing assessments were handled, whether the target lesion was selected before randomization, or whether the analysis used an intention-to-treat or other specified population. Those details matter for interpreting how participants without an observed Visit 8 score were treated in the endpoint calculation.

7. Results Posted in the Registry

• A-101 40%: 59.5% (22/37) versus 2.5% (1/40) on control; risk difference 57.0 percentage points (95% CI 40.4 to 73.5), risk ratio 23.78 (3.37–167.76); unadjusted two-proportion z-test p = <0.001.
• A-101 32.5%: 46.2% (18/39) versus 2.5% (1/40) on control; risk difference 43.7 percentage points (95% CI 27.3 to 60.0), risk ratio 18.46 (2.59–131.69); 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.

Mean Change From Baseline PLA Score at Visit 8

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • A-101 40%: mean -1.70 versus -0.10 on control; difference -1.60 (95% CI -2.00 to -1.20), standardized effect d = -1.84; z-test p = <0.001.
  • A-101 32.5%: mean -1.40 versus -0.10 on control; difference -1.30 (95% CI -1.70 to -0.90), standardized effect d = -1.45; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for A-101 40% than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for A-101 32.5% than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry record lists one secondary endpoint: mean change from baseline PLA score at Visit 8. Across the arms, the observed pattern is consistent with the primary endpoint in direction: the mean score decreased more in both A-101 groups than in the vehicle group. Since the scale runs from clear at zero to greater severity at higher values, a decrease is toward the clear end of the scale. This related measure offers context about score change in addition to the primary endpoint’s clear-versus-not-clear classification.

The sponsor reports ANCOVA analyses for the two secondary comparisons, and the summary-statistic recalculations also indicate differences from vehicle. These are supportive observations, but the secondary outcome does not constitute an independent confirmation free of the study’s design and analysis limitations. In particular, the primary and secondary outcomes are related assessments of the same condition and visit, and their results should not be treated as entirely separate evidence.

Unadjusted secondary results carry less weight when multiple outcomes or comparisons are examined because the chance of observing apparently strong results can increase across repeated tests. In general, multiplicity procedures can control or account for that issue, but the registry record does not report whether any adjustment was planned or applied to secondary analyses. The record also does not explain whether this secondary endpoint was prespecified in a detailed analysis plan or how missing measurements were handled. Accordingly, the secondary findings are best read as supportive descriptive and inferential information, not as a standalone basis for a broader conclusion.

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

• Mean Change From Baseline PLA Score at Visit 8

9. Statistical Interpretation

10. Statistical Methods Explained

Two kinds of outcomes appear in the registry record. The primary outcome is binary: each participant is counted as having or not having a clear target lesion at the specified visit. The secondary outcome is continuous: it is the mean change from baseline in PLA score. Different statistical summaries and tests are appropriate for these different outcome types.

How is the primary comparison expressed?

The recalculation expresses each active-arm comparison as a risk difference: the observed proportion with a clear lesion in the active arm minus the observed proportion in vehicle. A positive difference indicates a higher observed clear-lesion proportion in the active arm. The risk difference is expressed on the proportion scale, so it describes an absolute contrast rather than a relative measure. The posted counts also allow relative measures, but the risk difference is the measure used for the recalculated comparison described in the results.

For the 40% and 32.5% comparisons, the recalculated risk differences are positive and their intervals lie above zero. Each recalculated unadjusted p-value is <0.001. These calculations use the posted arm-level summary data and are not described as adjusted analyses. They should be distinguished from the sponsor’s analysis, which the registry reports as a chi-squared test for each active arm versus vehicle.

What does the chi-squared test address?

In general, a chi-squared test evaluates whether observed counts across categories are consistent with a null hypothesis of no association or no difference, under the test’s assumptions. For this endpoint, the categories are clear versus not clear. The registry record reports the test method and a superiority classification for each active-versus-vehicle comparison, but it does not provide the sponsor’s estimated effect size or confidence interval for these primary analyses. The exact analysis details beyond the named method are not reported in the registry record.

A p-value describes how compatible the observed data are with a specified null model, given the test assumptions. It does not give the probability that the null hypothesis is true, and it does not measure the clinical importance of a difference. A small p-value can coexist with uncertainty about the size of an effect or about whether the result generalizes. The p-values in the registry should be read together with the observed counts and the recalculated intervals, not on their own.

How is the secondary outcome analyzed?

The secondary endpoint summarizes each arm’s mean change in PLA score from baseline. The reported arm means are -1.7 for A-101 40%, -1.4 for A-101 32.5%, and -0.1 for vehicle. Because higher PLA scores indicate more severe lesions and zero denotes clear, a more negative change represents a larger decrease in the score. These arm means describe group averages; they do not show how scores varied for every participant.

The sponsor’s reported method for the secondary comparisons is ANCOVA. In general, analysis of covariance compares outcome means while accounting for one or more covariates. The registry record does not specify the covariates, model details, or treatment of missing values. The recalculated mean differences are unadjusted comparisons based on posted summary statistics and are not a replacement for the sponsor’s model. The record reports a sponsor p-value below its stated threshold for each secondary comparison, but does not give the sponsor’s estimates or confidence intervals.

For continuous outcomes, variability is important because a mean alone does not describe the spread of individual scores. The registry reports standard deviations for the arm-level changes. In general, a standard deviation describes how dispersed observations are around their group mean. A pooled standard deviation can be used in a standardized comparison, but such a summary does not preserve the original PLA scale units. The recalculation’s mean difference is more directly interpretable in score units.

Why can uncertainty differ across methods?

In general, a test and an interval estimate answer related but not identical questions. A test evaluates a null hypothesis under a model; an interval describes a range of values compatible with the data and the method used. Different assumptions, adjustments, and analysis populations can produce different estimates or p-values. Here, the registry gives sponsor test methods and p-values, while the recalculations use posted summary statistics. The registry does not provide enough detail to reproduce every aspect of the sponsor’s analyses.

For binary data, small or uneven cell counts can affect the behavior of approximations used by statistical tests. The record names chi-squared tests but does not report whether any alternative test or continuity correction was considered. For continuous data, ANCOVA can account for specified covariates, but the covariates and model diagnostics are not reported. As general statistical cautions, model assumptions and outcome completeness influence how confidently estimates can be interpreted; those details cannot be assessed from the reported summaries alone.

11. Confidence Intervals and Precision

A confidence interval communicates uncertainty around an estimated contrast. In general, an interval is constructed by a statistical method and reflects the range of effect values compatible with the observed data under that method. It is not a guarantee that the true effect lies inside the interval, and its interpretation depends on the method and confidence level. The confidence level for the recalculated intervals is not reported in the registry record.

The recalculated primary risk-difference intervals are entirely above zero for both comparisons with vehicle. This indicates that the intervals do not include no difference under the recalculation method. Their widths also matter: a wider interval represents less precision than a narrower interval, all else equal. The registry’s arm-level counts are relatively limited, so the interval estimates should be considered as estimates with uncertainty rather than exact values.

For the secondary mean-change comparisons, the recalculated intervals lie below zero. They describe uncertainty in the unadjusted mean differences, on the PLA score scale. The sponsor’s ANCOVA estimates and intervals are not reported in the registry record, so the recalculated intervals cannot be treated as the sponsor model’s uncertainty estimates.

Precision is distinct from statistical significance. An interval that excludes zero does not, on its own, establish clinical importance, and a p-value does not show how narrow or broad the plausible effect range is. Readers should consider the estimated contrast, the interval, the endpoint definition, and the analysis limitations together. Because exact confidence-level details and the sponsor’s estimates are absent, the intervals are best understood as recalculated summaries of the posted data, not as a full account of the sponsor’s inferential analysis.

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 figures are planning illustrations based on the observed effect, not the trial’s original design justification. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario considers an effect equal to a stated fraction of the observed effect. For these outcomes, the figures are participants per arm; the record’s special convention for time-to-event outcomes does not apply because these endpoints are not time-to-event measures.

The 80% power column gives the illustrative number of participants per arm associated with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and model assumptions held. The 90% power column uses a higher target probability of detecting the effect and therefore generally calls for more participants per arm. For example, planning for 75% of the observed primary effect gives 15 participants per arm for 80% power and 19 for 90% power in the 40% versus vehicle comparison; the corresponding figures for the 32.5% comparison are 22 and 28.

Rows based on smaller fractions of the observed effect require more participants: a less pronounced difference is harder to distinguish from random variation under the same assumptions. The table and curve are therefore useful for understanding how planning requirements change with the assumed effect size, not for identifying a definitive future-trial sample size. The trial’s own original sample-size assumptions are not reported in the registry record. These illustrations are not observed power.

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 = 0.025; treatment proportion p₁ = 0.595; average p̄ = 0.310.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6539 = 1.2817.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5152 = 0.4336.
4. n = (1.2817 + 0.4336)² / (0.5696)² = 9.1, rounded up to 10 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 <- 0.025                          # control proportion
p1 <- 0.594594594594595                          # 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(2260180)
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 = 10 (80% power), 12 (90% power)
 75% of observed effect: n per arm = 15 (80% power), 19 (90% power)
 50% of observed effect: n per arm = 26 (80% power), 34 (90% power)
power.prop.test: 9.1 
Simulated power at n = 10 per arm: 0.864 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses for both primary comparisons using chi-squared tests. Each is classified as a superiority comparison, and each reported p-value is below the threshold recorded for those tests. The sponsor’s primary effect estimates and confidence intervals are not reported in the registry record.

The recalculated primary comparisons use posted counts to estimate unadjusted risk differences and intervals; their p-values are <0.001. These are straightforward re-calculations from summary data, not a reconstruction of every part of the sponsor’s analysis. The registry does not identify a discrepancy between the posted results and the recalculations. Because the reported methods and available details differ, their p-values should not be treated as interchangeable numeric estimates.

For the secondary outcome, the sponsor reports ANCOVA comparisons, with p-values below the registry’s stated threshold. The recalculations instead compare the posted arm means using unadjusted summary statistics. The covariates and full model specifications for the sponsor analyses are not reported in the registry record. The sponsor’s analyses are the analyses reported by the trial record; the recalculations offer a separate, transparent comparison based on the posted summaries and do not establish what the sponsor’s detailed model would produce.

15. Multiplicity, Missing Data and Analysis Populations

The record includes two primary comparisons against vehicle and a secondary endpoint with two comparisons against vehicle. It does not report whether the analysis plan adjusted for testing more than one comparison or outcome. This matters because, in general, repeated testing can increase the chance of a nominally strong result arising by chance. No particular multiplicity procedure should be assumed from the reported p-values alone.

Missing-data handling is also not reported in the registry record. The record does not state how participants without a Visit 8 PLA assessment were treated, whether any values were imputed, or whether the primary analysis used all randomized participants or a subset. The number of participants contributing to the primary arm summaries is shown, but the reasons for any differences between outcome and safety denominators are not given. Without these details, it is not possible to assess whether missingness could have influenced the comparisons.

The analysis populations are not reported in the registry record. In general, intention-to-treat, per-protocol, and safety populations can include different participants and answer somewhat different questions. The posted summaries alone do not establish which population underlies each result, nor do they clarify how protocol deviations were handled.

The registry record names chi-squared tests for the primary analyses and ANCOVA for the secondary analyses, but does not give the full statistical analysis plan, model covariates, or detailed assumptions. Interim analyses are not reported in the registry record. Neither the original sample-size justification nor a detailed explanation of stopping or monitoring procedures is reported. These omissions limit assessment of whether all planned analyses and decision rules are represented in the posted 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: metastatic neoplasm (2.6%), renal failure (2.6%), squamous cell carcinoma of skin (2.6%), dizziness (2.6%), malignant melanoma (2.4%).

The registry reports serious adverse events and other adverse events by arm, with separate risk sets for those summaries. Serious adverse events were reported for 3 participants in the A-101 40% group, 0 in the A-101 32.5% group, and 1 in the vehicle group. The corresponding serious-event risk sets were 39, 39, and 41. The record reports 1 death in the A-101 40% group and 0 in each other group.

These figures describe reported events in the registry and should not be interpreted as proof that an event was caused by, or unrelated to, an intervention. The record does not provide the information needed to assess individual event circumstances, timing, relatedness, or comparative risk with precision. The arm-specific counts are small, so they provide limited detail about uncommon harms. The reported safety denominators also differ from the primary-outcome denominators; reasons are not reported in the registry record.

The registry lists serious-event terms with percentages, including metastatic neoplasm, renal failure, squamous cell carcinoma of skin, dizziness, and malignant melanoma. The record does not establish from these terms alone whether events were treatment-related. Safety interpretation therefore requires caution and should remain distinct from the primary effectiveness comparison.

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

The posted results show that clear target-lesion assessments at the Day 106 primary visit were more frequent in the observed A-101 groups than in the observed vehicle group. The recalculated risk differences are positive, with intervals above zero, and the sponsor reports superiority tests for both active-versus-vehicle comparisons. The secondary mean-change pattern is directionally consistent with those primary results. These findings describe the study’s recorded outcomes and the analyses reported for them.

They do not establish that one A-101 concentration is better than the other: a direct comparison between the two concentrations is not reported. They also do not establish what happens after the recorded assessment, whether all lesions respond similarly, or whether the results apply to people outside the study population. The registry record does not report participant characteristics in enough detail to assess representativeness.

Statistical evidence is not the same as a clinical judgment about importance. The registry record does not give a threshold for a clinically meaningful difference. It also does not provide enough detail about missing observations, analysis populations, or multiplicity to resolve all uncertainties surrounding the estimates. The results should therefore be read as evidence about a specific lesion endpoint and visit, not as a complete account of benefits, harms, durability, or overall treatment value.

No medical decision follows from these registry summaries alone. They are one trial’s posted results, with the design and reporting limitations. The record’s safety counts are descriptive and do not establish causation. A fuller assessment would depend on the broader evidence and clinical context, neither of which is posted by this trial record.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters. A binary clear-lesion outcome is easy to communicate, but it compresses the PLA scale into a single threshold: clear versus not clear. The secondary mean-change outcome retains more of the scale’s gradation, but group means can conceal variation among individual participants. Considering both makes the outcome structure clearer without turning either measure into a complete description of disease status.

It also shows the distinction between an observed contrast and uncertainty about that contrast. The arm-level counts are straightforward, while the recalculated risk differences and confidence intervals put the comparisons on an absolute scale and indicate precision. The sponsor’s reported test results and the recalculations address related comparisons through different reported methods. Reading the methods and estimates together is more informative than treating a p-value as a complete result.

The study is described as dose-response, yet the posted comparisons are each against vehicle. This is an important statistical distinction: evidence that two concentrations each differ from a control does not, by itself, answer whether the concentrations differ from each other or establish a trend across doses. The record does not report a direct active-dose comparison or a formal trend test.

Finally, the planning illustrations show how assumed effect size and desired power relate to participants per arm. They use the observed effects as a starting point and are not the original trial’s design rationale. Keeping planning calculations separate from observed trial evidence prevents a common misreading: sample-size illustrations are not evidence that the completed trial had a particular probability of success.

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 primary endpoint is a target-lesion assessment at Visit 8, with a timeframe of Day 106. It does not establish the status of every lesion or describe durability after that visit. The registry record does not report how lesions were selected, whether each participant contributed a single target lesion, or how assessors’ agreement was evaluated. Although the study was double-blind, the masked parties and procedures are not reported.

The registry lists 119 enrolled participants, while the reported primary-outcome arm sizes are 37, 39, and 40. Safety risk sets are 39, 39, and 41. The record does not explain these denominator differences, provide reasons for missing assessments, or state the analysis population. These reporting gaps limit evaluation of how complete the outcome data were and whether the analyzed groups reflect the randomized groups.

The record reports two active-versus-vehicle primary analyses and secondary comparisons, but does not describe multiplicity handling. It also does not provide the sponsor’s primary effect estimates or confidence intervals, the covariates used in ANCOVA, or the full statistical analysis plan. The recalculations are based on posted summaries and cannot fill those gaps.

The study was Phase 2 and followed participants to the stated Day 106 timeframe. The registry record does not report further follow-up for the outcomes, detailed demographic or clinical characteristics, or a direct comparison between active concentrations. These limits constrain conclusions about longer-term outcomes, generalizability, dose differences, and clinical importance.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of A-101 for the Treatment of Seborrheic Keratosis — NCT02260180.
• Registry record last updated 2020-12-02; status last verified 2020-11.
• Results first posted 2018-12-06.
• 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

NCT02260180 is a completed randomized, double-blind, parallel-group Phase 2 study of A-101 topical solution for seborrheic keratosis of the face. It compared A-101 40% and A-101 32.5% with A-101 0% vehicle and listed enrollment of 119.

The primary endpoint was the proportion with a target lesion judged clear on the PLA at Visit 8, reported at Day 106. Posted counts were 22 of 37, 18 of 39, and 1 of 40, respectively. Recalculated comparisons with vehicle have positive risk differences, intervals above zero, and p-values <0.001. The sponsor reports chi-squared superiority analyses for both primary comparisons.

The listed secondary endpoint was mean change from baseline PLA score at Visit 8. The record also reports serious adverse events and deaths by arm. Missing-data handling, analysis populations, multiplicity procedures, original sample-size assumptions, and detailed analysis specifications are not reported in the registry record.