Clinical Study Between Two Clindamycin 1%/Benzoyl Peroxide 5% Topical Gels: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Study Between Two Clindamycin 1%/Benzoyl Peroxide 5% Topical Gels (NCT01138514), a randomized phase 3 study. The primary outcome is Percent Change From Baseline in Inflammatory Lesions.

2. Clinical Question

The study was designed to compare efficacy and safety profiles for the Perrigo product and the reference gel, and to compare both active treatments with vehicle. The registry describes the study as randomized, double-blind, multicenter, vehicle-controlled, and parallel-group. Its primary endpoint concerns the mean percentage reduction in inflammatory lesions, while a posted secondary outcome concerns clinical success on the Investigator’s Global Assessment (IGA).

The reported primary comparison of particular interest is between the Perrigo gel and the reference product. Their posted mean lesion reductions are close, and the recalculated unadjusted confidence interval for their mean difference includes values in either direction. The vehicle comparisons have a different pattern: the posted mean reduction is lower in the vehicle group. These results describe the recorded outcomes; they do not by themselves establish a formal equivalence conclusion or settle questions beyond the measured outcomes and analysis populations.

3. Trial Design

The registry identifies this as a Phase 3, randomized, double-blind, parallel-group study of topical treatment for acne vulgaris. It lists Padagis LLC as sponsor, enrollment of 1555, a start date of 2009-10, primary completion of 2010-10, and status as completed. The official title describes a multicenter, vehicle-controlled comparison of the Perrigo clindamycin 1%/benzoyl peroxide 5% gel, a comparator clindamycin/benzoyl peroxide gel, and vehicle.

The three listed groups are Clindamycin 1%/Benzoyl Peroxide 5%, Reference Product, and Vehicle. The brief summary identifies the reference gel as Benzaclin. Random allocation and double masking are recorded, but details such as the allocation procedure, masking procedures, and how adherence was assessed are not reported in the registry record. The record also does not report the original protocol’s sample-size justification or other design assumptions.

The primary endpoint was measured at 10 weeks and is reported as a mean with standard deviation in the per-protocol population. The analysis counts shown for that endpoint are 430 for the Perrigo group, 419 for the reference group, and 427 for vehicle. These outcome analysis counts should not be assumed to represent every participant enrolled or to match the safety population. For safety, the registry reports separate at-risk counts of 522, 516, and 517, respectively.

The posted secondary outcome is the number of participants with clinical success on the IGA at 10 weeks. The registry metadata lists 3 outcome measures, while the posted secondary result available in the record concerns the IGA. Details of any other unposted outcome results 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Per protocol 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.

6. Primary Endpoint

The registry lists the primary outcome as Percent Change From Baseline in Inflammatory Lesions, measured over 10 weeks.

The primary endpoint is percent change from baseline in inflammatory lesions, expressed as percentage of lesion reduction and summarized as a mean with standard deviation. It was assessed at 10 weeks in the per-protocol population. The endpoint describes the average change in inflammatory lesion burden over the study period, with higher reported reductions corresponding to a greater reduction in lesions. It is a continuous outcome, so each participant’s measurement contributes a value to the group mean rather than being classified only as a success or failure.

A mean provides a compact description of the group’s results, while the standard deviation describes the spread of individual measurements around that mean. The standard deviation is not the uncertainty in the estimated difference between groups; that uncertainty is represented by a confidence interval. This distinction matters because participants can vary substantially even when the mean difference between groups is estimated with reasonable precision.

The endpoint is useful for comparing average lesion change across the active treatments and vehicle. The registry reports mean reductions of 79.87 for the Perrigo gel, 80.86 for the reference product, and 45.6 for vehicle. The posted summary does not provide baseline means, a participant-level distribution, or details on how the percentage change was calculated. Those details are therefore not reported in the registry record, and interpretation should stay with the stated endpoint and the posted analysis population.

7. Results Posted in the Registry

• Clindamycin 1%/Benzoyl Peroxide 5%: mean 79.87 versus 80.86 on control; difference -0.99 (95% CI -4.49 to 2.51), standardized effect d = -0.04; z-test p = 0.580.
• Vehicle: mean 45.60 versus 80.86 on control; difference -35.26 (95% CI -40.06 to -30.46), standardized effect d = -0.99; 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.

Number of Participant With Clinical Success on the Investigator's Global Assessment (IGA)

• 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:
  • Clindamycin 1%/Benzoyl Peroxide 5%: 57.4% (247/430) versus 55.8% (234/419) on control; risk difference 1.6 percentage points (95% CI -5.1 to 8.3), risk ratio 1.03 (0.91–1.16); unadjusted two-proportion z-test p = 0.639.
  • Vehicle: 18.5% (79/427) versus 55.8% (234/419) on control; risk difference -37.3 percentage points (95% CI -43.4 to -31.3), risk ratio 0.33 (0.27–0.41); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Clindamycin 1%/Benzoyl Peroxide 5% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Vehicle than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcome is clinical success on the Investigator’s Global Assessment at 10 weeks. Its broad pattern is similar to the primary outcome: the two active-product groups are relatively close to one another, while the vehicle group is more separated from the reference group. The secondary endpoint is binary rather than continuous, so it captures the share of participants meeting the IGA success definition rather than average lesion reduction. The posted results do not include the detailed definition of clinical success.

The secondary pattern is directionally consistent with the primary outcome’s comparison structure, but it does not duplicate the primary measure. Agreement between endpoints can add context, while differences in endpoint construction and analysis mean that one should not be treated as a direct confirmation of the other. The secondary result also does not resolve the uncertainty about formal equivalence between the active products; the sponsor’s equivalence analysis and its criteria remain the relevant record for that intended claim.

Secondary results carry less weight when the analysis is unadjusted and the approach to multiplicity is not reported. When several outcomes or comparisons are examined, chance findings become more likely unless the analysis plan accounts for that selection. The registry metadata lists 3 outcome measures, while the posted secondary result is the IGA outcome. The record does not report a multiplicity-control strategy or explain the status of other outcome results. The IGA findings are therefore best read as supportive descriptive evidence, not as a replacement for the prespecified primary endpoint or a standalone confirmatory finding.

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

• Number of Participant With Clinical Success on the Investigator's Global Assessment (IGA)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so the posted group summaries are means and standard deviations. The recalculated comparisons use differences in group means. Such a difference is expressed in the endpoint’s units—in this case, percentage points of lesion reduction—and is easier to interpret than a standardized effect size for the clinical scale itself. The direction of a difference depends on the order of subtraction. The reported active-product contrast is Perrigo minus reference; the vehicle contrast is vehicle minus reference.

What does the mean difference represent?

A mean difference compares the average endpoint values in two groups. A value near zero means the group averages are close in the observed data, but closeness of point estimates alone does not establish equivalence. The confidence interval is needed to assess the range of differences compatible with the estimate under the calculation’s assumptions. A formal equivalence or non-inferiority analysis also requires a prespecified margin and an appropriate analysis plan. Those details are not reported in the registry record.

The standard deviations in the primary outcome describe variability among participant measurements. The pooled standard deviation used for the recalculated comparison is 26.07 for the active-product comparison and 35.76 for the vehicle comparison. Pooling is a way to combine the two groups’ within-group variability for an unadjusted comparison when using the stated calculation. It does not correct for baseline imbalance, missing observations, or differences in the analysis populations.

How should the confidence intervals and p-values be read?

A confidence interval expresses uncertainty around an estimated contrast under the model and calculation used. A narrower interval indicates greater precision than a wider interval, while an interval spanning zero is compatible with both a negative and positive mean difference for a difference measure. The interval does not assign probabilities to particular true values, and it does not account for design or reporting limitations that are not represented in the calculation.

The recalculated p-values are unadjusted. They quantify how unusual the observed data, or more extreme data, would be under a null model of no difference, subject to the calculation’s assumptions. They are not the probability that the null hypothesis is true, and they do not measure the size or practical importance of a contrast. No multiplicity adjustment is reflected in these recalculated p-values.

The active comparison also has a sponsor-reported equivalence ratio analyzed with Fieller’s method, with a 90% confidence interval. Fieller’s method is used for confidence limits on a ratio when uncertainty in both numerator and denominator matters. The registry also records a Wald-based equivalence-difference analysis for the IGA result, with a Yates continuity correction. A continuity correction modifies a large-sample approximation for discrete outcomes. The record does not provide enough detail to reconstruct the sponsor’s full analyses or verify the criteria used for a formal equivalence decision.

Why can outcome type affect the analysis?

The primary endpoint is continuous, but the IGA secondary outcome is binary at the participant level: a participant either met the recorded clinical-success definition or did not. The recalculated secondary comparisons use risk differences, which compare the proportions in the two groups, while the sponsor’s legacy analysis is described as an equivalence difference. These are not interchangeable analyses. A risk difference expresses a contrast on the probability scale; a mean difference expresses a contrast in the continuous endpoint’s units.

General statistical context: over-dispersion occurs when outcome variation exceeds what a chosen model expects. It can make standard errors too small if the model does not accommodate the extra variation. The primary endpoint’s standard deviations show substantial spread in the lesion-reduction measurements, but the registry record does not report a model-based over-dispersion assessment, nor is one needed to describe the simple unadjusted mean comparison. The summary data alone cannot establish whether a more complex model would be preferable.

What is recalculated, and what is not?

The recalculated comparisons are simple, unadjusted estimates from the posted group summaries. They do not reproduce any covariate adjustment, protocol-specific analysis, or sponsor decision process that may have been used. The discrepancy flag means that the sponsor’s own analysis takes precedence for its intended conclusion. Recalculated results can still help readers understand the raw scale and uncertainty of the posted group contrasts, but they should not be substituted for the sponsor’s analysis when interpreting the sponsor’s formal claim.

The registry record does not report the full statistical analysis plan, the handling of missing primary outcomes, the procedure for controlling multiplicity, or whether interim analyses occurred. These omissions limit assessment of prespecification and robustness. They also mean that a reader cannot determine from the posted summary alone whether all planned analyses, populations, or outcomes are represented.

11. Confidence Intervals and Precision

For the Perrigo-versus-reference primary comparison, the recalculated estimate is -0.99 percentage points and its 95% confidence interval runs from -4.493 to 2.513. Because this interval includes zero and spans both directions, the posted summary does not precisely establish which active product had the higher mean lesion reduction. The point estimate is small relative to the interval’s range, and the interval still allows for differences on either side of that estimate. The unadjusted p-value is 0.58.

For vehicle versus reference, the recalculated estimate is -35.26 percentage points, with a 95% confidence interval from -40.06 to -30.46. This interval is separated from zero and is comparatively distinct in direction. The p-value is <0.001. These intervals concern the unadjusted comparisons and should not be confused with the sponsor’s separate equivalence analysis, which reports a 90% confidence interval for a ratio.

Precision depends on outcome variability and the amount of information in the relevant analysis population. The primary outcome standard deviations are 27.38 for the Perrigo group, 24.65 for the reference group, and 44.01 for vehicle. Greater spread generally makes a group contrast harder to estimate precisely, all else being equal. The registry does not report confidence intervals for the individual group means, and the recalculated intervals do not represent adjustment for other factors.

Confidence intervals are not a guarantee that the true effect lies within the stated limits. They describe uncertainty under a statistical method and its assumptions. The intervals also do not account for missing data, outcome selection, or multiplicity unless those are built into the analysis. Since those procedures are not fully reported, the stated precision is limited to the posted unadjusted summary comparison.

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 illustrations give participants per arm for the continuous endpoint and for the binary IGA endpoint. They do not give total event counts. Each row represents planning for a stated fraction of the observed effect, with separate columns for 80% and 90% power. The 80% power column means the planned design would have an 80% chance of detecting the specified effect under the stated assumptions if that effect were the true effect. The 90% column expresses the corresponding chance at the higher power target.

The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. For example, the entries labeled 75% of the observed effect are planning for an effect smaller than the observed estimate; those labeled 50% of the observed effect plan for a still smaller effect. Smaller effects require more participants per arm to detect with the same power target, which is why the required sample sizes rise as the assumed fraction falls.

These are planning illustrations calculated from the observed effect, not the original trial’s design rationale. The trial’s own sample-size assumptions and justification are not reported in the registry record. The illustrations are not observed power: they do not describe the probability that the completed study detected an effect, and they should not be used to reinterpret the observed p-values. The displayed values are specific to the assumptions stated and do not account for unreported design features or analysis procedures.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.990; pooled standard deviation σ = 26.068.
2. n = 2 × (1.96 + 0.842)² × 26.068² / -0.990² = 10,884.3, rounded up to 10,885 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
delta <- -0.989999999999995                      # observed difference in means
sigma <- 26.0684828864282                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1138514)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 10,885 (80% power), 14,571 (90% power)
 75% of observed effect: n per arm = 19,350 (80% power), 25,904 (90% power)
 50% of observed effect: n per arm = 43,538 (80% power), 58,284 (90% power)
power.t.test: 10885.2 
Simulated power at n = 10,885 per arm: 0.799 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 the sponsor’s active-product primary analysis as an equivalence ratio of 98.77, using Fieller’s method, with a 90% confidence interval from 95.2 to 102.5 and p = 0.05. The sponsor analysis is distinct from the recalculated unadjusted mean difference of -0.99 percentage points, whose 95% confidence interval is -4.493 to 2.513 and unadjusted p-value is 0.58. The measures and methods differ, so the estimates should not be treated as competing versions of the same calculation.

The record flags a discrepancy. In that circumstance, the sponsor’s own analysis takes precedence for its intended inferential conclusion; the recalculation is useful for understanding the contrast from the posted means and standard deviations, not for replacing the sponsor’s method. The registry does not report the equivalence margin, its justification, or the full decision criteria. Consequently, the ratio and interval alone do not allow independent confirmation of a formal equivalence conclusion.

For the IGA outcome, the sponsor’s reported analysis is a Wald equivalence difference of 1.6, with a 90% confidence interval from -4.2 to 7.4 and p = 0.05. The record does not explain the sponsor’s analysis population, missing-data approach, or multiplicity handling for this result. Those details should be considered unresolved rather than inferred from the reported method label.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report how multiplicity was handled. Multiplicity arises when investigators make several comparisons or assess multiple outcomes; without an appropriate plan, interpreting each unadjusted result as if it were the only test can overstate the strength of evidence. The recalculated p-values are unadjusted, and the posted secondary comparison results should be read with that limitation in mind. Whether the sponsor used a multiplicity procedure in its own analysis is not reported in the registry record.

Missing-data handling is also not reported. The primary endpoint is identified as a per-protocol analysis, but the record does not explain how participants with missing measurements were handled, why participants were excluded from that population, or whether a separate intention-to-treat analysis was performed. The analysis counts for the primary result differ from the safety at-risk counts; the record does not explain the reasons for that difference. No assumptions about missing outcomes can therefore be verified from the posted summary.

The record does not report the full statistical analysis plan, any interim analyses, or the trial’s original sample-size justification. It also does not provide enough detail to determine whether the per-protocol population was defined before unblinding or how protocol deviations were assessed. These omissions do not invalidate the reported summaries, but they constrain assessment of prespecification, selective reporting, and sensitivity to analysis choices.

The sponsor’s equivalence methods are named, but the equivalence margin and full decision criteria are not reported. A method label and confidence interval are not sufficient to reconstruct every inferential decision. The discrepancy flag further cautions against treating the simple recalculation as a substitute for the sponsor’s intended analysis.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in each group’s safety at-risk population: 522 for the Perrigo gel, 516 for the reference product, and 517 for vehicle. The listed counts of other adverse events are 49, 49, and 72, respectively. These are counts as posted, not rates calculated for comparison. Death counts are not reported in the registry record.

Zero recorded serious events in these groups means that none were listed in the posted serious-event counts for the stated at-risk populations. It does not establish that serious events are impossible or that the treatments have identical safety profiles. The registry’s serious-event terms list is empty, and the record does not give event definitions, severity details for other events, exposure-adjusted summaries, or the method used to collect events. The counts therefore provide a limited descriptive view of safety and should be read alongside the trial’s incomplete safety detail rather than as a comprehensive safety comparison.

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

The results describe average inflammatory-lesion reduction at 10 weeks in the per-protocol population, plus a posted IGA clinical-success outcome and adverse-event counts. In the primary summary, the Perrigo and reference product means are close. The recalculated interval for their mean difference includes zero and extends in both directions, so the unadjusted comparison does not precisely identify which product had the higher mean result. The sponsor’s separate equivalence analysis is reported, but the registry does not provide the margin or full decision criteria needed to assess that claim independently.

The vehicle group’s posted mean lesion reduction is lower than the reference group’s, and the recalculated unadjusted interval for that comparison is separated from zero. The IGA outcome follows a broadly similar comparison pattern. These statements concern the posted outcomes, analysis populations, and calculations; they do not establish effects for other populations, time points, or outcomes not reported in the registry.

The results do not establish that either active product is interchangeable with the other without a prespecified equivalence margin and analysis details. Nor do the posted summaries resolve how missing data, multiplicity, or any other analysis choices affected the findings. Safety counts are descriptive and incomplete, with death counts not reported. Accordingly, the record supports a bounded statistical reading of the measured outcomes, not medical advice or a general conclusion about treatment choice.

18. Why This Trial Matters Statistically

This study illustrates why the estimand and analysis method matter. The primary endpoint is a continuous measure of lesion reduction, and its mean difference has an interpretable percentage-point scale. The active-product point estimate is close to zero, but the confidence interval conveys uncertainty that cannot be captured by looking at the means alone. A small observed contrast is not synonymous with proof of equivalence.

It also shows how an active comparator, vehicle control, and distinct secondary endpoint address different questions. The active-versus-reference comparison concerns similarity between products, while comparison with vehicle describes separation from the control condition on the recorded outcome. The IGA outcome supplies a different, binary perspective. These contrasts cannot be collapsed into one overall conclusion, particularly when their analysis plans and multiplicity handling are not fully reported.

Finally, sponsor-reported inference and simple recalculation serve different purposes. The sponsor’s equivalence analysis is the primary source for its intended formal conclusion, while recalculation makes the posted summary statistics and uncertainty easier to inspect. The discrepancy flag, missing analysis details, per-protocol population, and incomplete safety reporting all make transparent interpretation important. This is a useful example of reading effect estimates, confidence intervals, and registry reporting limitations together rather than relying on a single p-value.

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 result is reported for the per-protocol population, and the registry does not describe exclusions, adherence criteria, or a complementary intention-to-treat analysis. The primary endpoint counts are not the same as the safety at-risk counts, but the record does not explain the difference. Missing outcome handling is not reported, limiting assessment of possible bias from incomplete measurements.

The posted summary supplies means and standard deviations but not baseline group summaries, participant-level distributions, or details of the percentage-change calculation. Recalculated comparisons are unadjusted and do not reproduce any covariate-adjusted sponsor analysis. The registry flags a discrepancy, and the sponsor’s formal equivalence margin and decision criteria are not reported. This prevents independent reconstruction of the sponsor’s equivalence conclusion.

Only one secondary outcome is posted in the available results, while the record lists 3 outcome measures. The multiplicity plan and status of other outcome results are not reported. Safety reporting is also limited: serious-event counts are zero in the listed at-risk groups, other adverse-event counts are reported, but death counts are not reported in the registry record. Event definitions, follow-up details, and comparative safety methods are absent. These limitations qualify interpretation of the reported estimates without changing the values recorded.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Study Between Two Clindamycin 1%/Benzoyl Peroxide 5% Topical Gels — NCT01138514.
• Registry record last updated 2021-10-13; status last verified 2021-10.
• Results first posted 2016-03-29.
• 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

NCT01138514 is a completed Phase 3 randomized, double-blind, parallel-group study sponsored by Padagis LLC. It compared Perrigo clindamycin 1%/benzoyl peroxide 5% gel and a reference product with vehicle in acne vulgaris. The registry lists enrollment of 1555 and dates of 2009-10 for study start and 2010-10 for primary completion.

The primary endpoint was mean percent change from baseline in inflammatory lesions at 10 weeks in the per-protocol population. The registry also posts IGA clinical success at 10 weeks and adverse-event counts. The active-product primary means are close, while the vehicle mean is lower than the reference mean. A sponsor-reported equivalence analysis is available, but the margin and full decision criteria are not reported. Missing-data and multiplicity methods are also not reported, and the registry flags a discrepancy between sponsor analysis and recalculation.