To Compare the Efficacy and Safety of Clindamycin Phosphate 1.2% / Benzoyl Peroxide 5% Gel of CHL Versus DUAC® Gel: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Compare the Efficacy and Safety of Clindamycin Phosphate 1.2% / Benzoyl Peroxide 5% Gel of CHL Versus DUAC® Gel (NCT02005666), a randomized phase 3 study. The primary outcome is Mean Percent Change From Baseline to Week 11 (Study Day 77) for Inflammatory (Papules and Pustules) Lesions..

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, phase 3 clinical study with three arms: the test clindamycin phosphate 1.2% / benzoyl peroxide 5% gel, DUAC® Gel as the active reference, and vehicle-gel placebo. The registry record describes it as multicentric and active- and placebo-controlled. Its stated allocation ratio was 2:2:1, respectively, and the planned enrollment was 850 subjects.

The structured trial information classifies masking as quadruple, while the narrative description calls the study double-blind. The precise roles of masked participants and study staff, and how masking was maintained, are not reported in the registry record. Both active gels and placebo were described as thin layers, pea-sized, applied once a day every evening for 77 consecutive days. The brief summary gives a total study duration of 78 days, including the 77-day treatment period.

The trial status is completed. The recorded start is 2013-11 and primary completion is 2016-09-28. These dates describe the registry record; they do not establish when every participant entered or completed follow-up.

Although the planned enrollment was 850, the primary outcome results are reported for per-protocol populations of 236 in the test arm, 233 in the reference arm, and 128 in the placebo arm. The reasons these analysis counts differ from the planned enrollment, and the flow of participants through randomization, treatment, and analysis, are not reported in the registry record. Nor are the original sample-size justification and detailed analysis protocol reported. The posted outcome counts should therefore be read as the sizes of the reported analyses, not as a complete account of trial participation.

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

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 Mean Percent Change From Baseline to Week 11 (Study Day 77) for Inflammatory (Papules and Pustules) Lesions., measured over week 11.

The primary endpoint measures the average percentage change from baseline in the count of inflammatory acne lesions—papules and pustules—by week 11, study day 77. A negative percent change represents a reduction from baseline. Papules are described in the registry as small, solid, palpable inflammatory lesions; pustules are small, inflamed swellings containing pus. Both definitions specify lesions less than 5 mm in diameter.

Lesion counts are a continuous outcome when summarized as a mean change. A mean gives a central summary across participants, while the standard deviation describes how much individual results vary around that average. The endpoint was selected to represent change in inflammatory lesion burden over the treatment period. The trial also included a non-inflammatory lesion-count outcome and a clinical-response success outcome at week 11.

The registry identifies the primary endpoint as mean percent change in the per-protocol population. It states that the test product would be judged therapeutically equivalent to the reference product if a 90% confidence interval fell within (0.80, 1.25). That interval is expressed as a criterion for the study’s equivalence judgment, but the posted arm summaries and unadjusted mean-difference results do not themselves report a formal comparison on that criterion. The formal equivalence analysis and its conclusion are not reported in the registry record.

7. Results Posted in the Registry

• Test-Cadila Healthcare Limited: mean -67.60 versus -71.30 on control; difference 3.70 (95% CI -1.22 to 8.62), standardized effect d = 0.14; z-test p = 0.141.
• Placebo: mean -51.90 versus -71.30 on control; difference 19.40 (95% CI 12.63 to 26.17), standardized effect d = 0.67; 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 Percent Change From Baseline to Week 11 in the Non-inflammatory Lesion Count

• 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:
  • Test-Cadila Healthcare Limited: mean -61.70 versus -61.30 on control; difference -0.40 (95% CI -5.65 to 4.85), standardized effect d = -0.01; z-test p = 0.881.
  • Placebo: mean -42.00 versus -61.30 on control; difference 19.30 (95% CI 12.22 to 26.38), standardized effect d = 0.62; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test-Cadila Healthcare Limited 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 mean is statistically higher for Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes listed in the registry concern mean percent change in non-inflammatory lesion count and the proportion of participants with a clinical response of success at week 11. The posted quantitative secondary summary is for non-inflammatory lesion-count change. Results for the clinical-response success outcome are not reported in the registry record.

Across the primary inflammatory-lesion outcome and the posted non-inflammatory lesion-count outcome, the broad pattern is similar: the two active arms have mean changes in the same general range, while the placebo arm shows a less negative mean change. This offers contextual consistency across lesion-count measures, but it does not turn the secondary endpoint into confirmation of the primary bioequivalence question. The endpoints measure different lesion categories, and the registry does not report a formal combined analysis.

Secondary results generally carry less weight when they are unadjusted and when the analysis plan and multiplicity approach are not reported. If several outcomes or comparisons are examined, the chance of at least one apparently notable result can increase. An unadjusted result does not account for that issue. The record does not report a hierarchy, multiplicity adjustment, or confirmatory status for the secondary outcomes.

The secondary summaries can therefore be read as descriptive evidence about the observed pattern, not as a substitute for a prespecified primary analysis or a reported formal equivalence test. Because the response-success results are absent and the analysis details are limited, the secondary evidence is incomplete. It can add context to the lesion-count findings, but it does not resolve the uncertainties about the primary analysis or the equivalence conclusion.

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

• Mean Percent Change From Baseline to Week 11 in the Non-inflammatory Lesion Count
• Proportion of Subjects With a Clinical Response of "Success" at Week 11

9. Statistical Interpretation

10. Statistical Methods Explained

Mean percent change is a continuous-outcome summary. For each arm, the posted mean describes the average percentage change from baseline at week 11. Negative values indicate a decrease from baseline. The standard deviation describes the spread of individual changes around the mean; it is not the uncertainty interval for the mean. A standard deviation can be large even when the mean is estimated with some precision, because the two quantities describe different features of the data.

What does a mean difference represent?

The posted pairwise comparisons express the difference between the mean in an arm and the mean in the reference arm. For the primary endpoint, the test-versus-reference contrast is reported as test minus reference. A difference of zero would correspond to equal reported means. A positive difference in this setting means the test arm’s change is less negative than the reference arm’s change; a negative difference means it is more negative. This is a description of the scale and direction, not a judgment about clinical importance.

The placebo comparisons use the same reference arm. These contrasts are separate from the test-versus-reference comparison and address a different question. The trial’s stated primary objective concerns the active formulations, while placebo provides an additional context for the observed changes. A result from the placebo comparison cannot establish equivalence between the active arms.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the data under the method used to calculate it. It conveys uncertainty around an estimate rather than listing every possible individual outcome. A narrow interval indicates greater precision for the estimated contrast than a wide interval, but it does not by itself establish that the estimate is clinically important or that a formal equivalence criterion has been met. The confidence level for the posted mean-difference intervals is not reported in the registry record.

The registry’s equivalence description refers separately to a 90% confidence interval within (0.80, 1.25). That criterion is stated on a ratio-like scale, whereas the posted pairwise summaries present mean differences. The registry record does not explain how the formal equivalence analysis was defined or connect the posted mean-difference interval to the stated criterion. Consequently, the reported interval around the mean difference should be interpreted on its own scale and not as a direct test of the stated equivalence margin.

What does an unadjusted p-value say?

A p-value describes how compatible the observed result is with a specified null hypothesis under the statistical model used. An unadjusted p-value does not account for the number of outcomes or comparisons considered. It is not the probability that the null hypothesis is true, nor does it quantify the size or importance of an effect. The posted p-values are explicitly unadjusted. The statistical plan, including any planned adjustment or hierarchy among comparisons, is not reported in the registry record.

A non-small p-value does not establish equality or equivalence. Conversely, a small p-value does not show that an effect is large or important. Interpretation should consider the estimated difference, its interval, the analysis population, the endpoint definition, and whether the analysis corresponds to the trial’s intended question.

Why does variation matter?

General explanation: when outcomes vary widely between participants, the arm mean alone can conceal different response patterns. The standard deviations in the posted results describe that variability. They do not explain its causes and do not indicate whether the distribution is symmetric, contains outliers, or has distinct subgroups. Individual-level data and fuller distributional summaries are not reported in the registry record.

General explanation: over-dispersion means that variability is greater than a statistical model expects. It can make model-based uncertainty estimates too small if the model does not allow for that extra variability. The posted endpoint is reported as a mean and standard deviation, and the registry record does not report a model assessment or an over-dispersion analysis. It is therefore not possible to say whether over-dispersion was present or how the investigators addressed it.

What analysis details are missing?

The endpoint description identifies the per-protocol population, but the exact membership rules and exclusions are not reported in the registry record. The record does not report a detailed model, covariate adjustment, missing-data method, or sensitivity analysis. It also does not report a formal analysis entry for the primary endpoint. These details matter because different choices can affect estimates, intervals, and equivalence conclusions. The posted summaries remain useful descriptions of the reported arm means, but they cannot reveal all assumptions behind the trial’s intended analysis.

11. Confidence Intervals and Precision

The primary test-versus-reference mean difference is 3.7, with a posted interval from -1.224 to 8.624. The interval spans values on both sides of zero, so the posted result is compatible with no difference in the arm means as well as with differences in either direction. It also shows that the point estimate alone should not be read as a precise value for the underlying contrast. The confidence level used for this interval is not reported in the registry record.

The interval is a measure of uncertainty in the estimated mean difference, not a range containing a specified proportion of individual participants’ responses. The standard deviations—28.39 in the test arm and 25.98 in the reference arm—describe variation in participant-level changes, while the interval describes uncertainty around the estimated contrast. These quantities answer different questions.

For the reference-versus-placebo primary comparison, the posted mean difference is 19.4, with an interval from 12.63 to 26.17. This interval lies above zero on the reported difference scale. As with the active-arm comparison, the interval does not give the formal bioequivalence result, and its confidence level is not stated in the registry record.

Precision depends on the amount of information and the variability in outcomes. The analysis counts differ between the active and placebo arms, and the standard deviations indicate appreciable variability. The posted intervals summarize uncertainty under the calculation used, but details of that calculation and any model-based adjustments are not reported. Precision should therefore be considered alongside the limitations of the registry’s analysis reporting, rather than taken as a complete account of the trial’s inferential uncertainty.

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 computed from the observed effect, using a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted in each row is the stated fraction of the observed effect. These are planning assumptions for the illustration, not the original trial’s design assumptions; the original sample-size justification is not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation indicates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding number per arm for a 90% chance. Power is a design calculation conditional on the assumed effect, variability, significance level, and analysis; it does not describe the certainty of the result in the completed trial.

The rows planning for smaller fractions of the observed effect require more participants. This follows because a smaller difference is harder to distinguish from random variation, all else equal. The figures are not a reconstruction of the trial’s enrollment plan and are not observed power. The registry record does not report the assumptions used to choose the planned enrollment of 850 subjects, so the illustrative figures should not be used to infer why that enrollment target was selected.

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 = 3.700; pooled standard deviation σ = 27.219.
2. n = 2 × (1.96 + 0.842)² × 27.219² / 3.700² = 849.6, rounded up to 850 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 <- 3.7                      # observed difference in means
sigma <- 27.2194254659806                     # 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(2005666)
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 = 850 (80% power), 1,138 (90% power)
 75% of observed effect: n per arm = 1,511 (80% power), 2,022 (90% power)
 50% of observed effect: n per arm = 3,399 (80% power), 4,550 (90% power)
power.t.test: 850.5 
Simulated power at n = 850 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, comparison, time point, or analysis. If each is interpreted without adjustment, the chance of a false-positive finding across the full set can be greater than for one prespecified test alone. This is a general statistical consideration, not a claim that any particular result in this trial is false.

The registry lists a primary inflammatory-lesion endpoint and secondary outcomes covering non-inflammatory lesion counts and clinical response. The posted comparisons include test versus reference and placebo versus reference. The p-values are unadjusted. A multiplicity plan, a hierarchy of hypotheses, or an adjustment procedure is not reported in the registry record. The original statistical analysis plan is also not reported, so it is unclear which comparisons were intended as confirmatory and how the investigators planned to handle multiple testing.

Missing-data handling is another important uncertainty. The registry record does not report the number of participants with missing week 11 measurements, reasons for missingness, imputation methods, or sensitivity analyses. It does not describe whether participants who discontinued treatment remained in any analysis. Without these details, the effect of missing outcomes on the reported means cannot be assessed.

The primary outcome description names the per-protocol population, but the rules defining that population are not reported. The registry also does not give a complete participant flow or an intention-to-treat analysis for the primary endpoint. The analysis listing contains no reported analyses. This does not establish that no analysis was performed; it means the registry record does not provide those details. These gaps limit assessment of how closely the posted summaries follow the intended analysis and whether the conclusion is robust to other reasonable analytic choices.

The registry describes a 90% confidence-interval criterion for therapeutic equivalence, but the formal comparison applying that criterion is not reported. The record also does not report interim analyses or stopping rules. These are not assumed to have occurred; they are simply not reported in the registry record.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists 0 serious adverse events in the reported serious-event field for each arm, with at-risk counts of 338 for the test arm, 343 for DUAC® Gel, and 169 for placebo. It also records 0 deaths in each arm. The serious adverse event terms list is empty. These entries describe what is recorded in the registry; they do not provide a detailed account of event types, timing, severity grading, or individual cases.

The record also lists other adverse events affecting 59 participants in the test arm, 61 in the reference arm, and 29 in the placebo arm. Those counts are not a substitute for a full safety analysis, and no event-level breakdown is given in the registry information. Safety counts should be interpreted with the at-risk populations and the reporting definitions in mind. The registry does not report additional detail about how events were collected, classified, or assessed for relationship to treatment.

These figures are descriptive. They do not by themselves establish comparative safety, and the absence of recorded serious events in the listed field should not be read as proof that no serious events occurred under every possible definition or reporting process. A fuller safety interpretation would require event definitions, participant follow-up details, and more complete reporting.

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

The posted primary endpoint summaries show substantial average decreases in inflammatory lesion counts in all three arms over the measured period, with the two active-arm means closer to each other than either is to the placebo mean. The test-versus-reference mean difference is accompanied by an interval that includes zero and an unadjusted p-value of 0.141. These results describe the reported per-protocol summaries; they do not establish that the active formulations are identical.

In particular, lack of a statistically established difference is not the same as evidence of equivalence. Equivalence requires an appropriate analysis against a prespecified margin. The registry states a 90% confidence-interval criterion of (0.80, 1.25), but the formal analysis applying that criterion is not reported. The posted mean-difference comparison does not answer that question on its own.

The results also do not show how every participant responded. A mean can mask a range of individual outcomes, and standard deviations indicate that individual changes varied around the arm averages. The registry does not report the distribution of responses, the number meeting a clinical-response definition, or the result for the listed clinical-response secondary outcome.

Interpretation is further limited by missing analysis details. The exact per-protocol rules, treatment of missing measurements, multiplicity approach, and formal statistical plan are not reported in the registry record. The posted data can therefore support a careful description of the recorded averages and comparisons, but not a complete reconstruction of the trial’s inferential process.

These findings are not medical advice and should not be used alone to make treatment decisions. They concern one registry-recorded trial, its specified outcome, and the posted summaries. They do not establish effects in populations or settings not described by the trial, nor do they resolve the unanswered formal bioequivalence question.

17. Why This Trial Matters Statistically

This trial illustrates why equivalence questions need to be separated from ordinary difference testing. A conventional comparison asks whether data provide evidence of a difference under a null hypothesis. Equivalence asks whether uncertainty around the contrast is sufficiently contained within a prespecified acceptable range. A result that does not establish a difference does not, by itself, establish equivalence. The registry’s stated criterion makes that distinction especially relevant, while the formal analysis applying it is not reported.

The case also shows the importance of aligning the endpoint scale with the stated decision rule. The primary results are presented as arm means and mean differences in percent change, while the registry’s equivalence criterion is expressed as an interval of (0.80, 1.25). The record does not provide the formal calculation linking those quantities. Without that analysis, readers should avoid treating a descriptive mean-difference interval as a direct test of the stated equivalence criterion.

Another statistical lesson is that unadjusted results across multiple outcomes and comparisons require context. The trial includes an active reference, placebo, and more than one outcome. The registry does not report a multiplicity strategy or identify which secondary analyses were confirmatory. Reported p-values should therefore be read as unadjusted evidence for their particular comparisons, not as a complete account of the study-wide error rate.

Finally, this record highlights the value of transparent reporting of analysis populations, missing-data handling, and participant flow. Planned enrollment and analyzed outcome counts are not interchangeable, and the record does not explain the difference. These details affect how readers judge precision and generalizability. Statistical interpretation depends not only on the numerical estimate, but also on knowing how the analysis was conducted.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The largest trial-specific limitation is that the registry record does not report the formal bioequivalence analysis, despite describing an equivalence criterion. The posted test-versus-reference result is a mean difference, while the stated criterion is given as a 90% confidence interval within (0.80, 1.25). The connection between these scales and the investigators’ formal conclusion are not reported.

The primary outcome is identified as a per-protocol analysis, but the definition of that population is absent. The planned enrollment was 850, while the primary endpoint summaries report arm counts of 236, 233, and 128. The reasons for the difference and the participant flow are not reported in the registry record. Without that information, it is not possible to assess the extent or consequences of exclusion from the reported analysis.

Detailed statistical methods are also missing: the model, confidence level for the posted mean-difference intervals, missing-data approach, sensitivity analyses, and multiplicity plan are not reported. The registry analysis listing contains no reported analyses. These omissions make it difficult to determine whether the posted comparisons represent the prespecified analysis or to assess robustness to alternative methods.

The secondary evidence is incomplete because the listed clinical-response success outcome has no reported result. Safety information is limited to event counts and does not include an event-level breakdown or fuller definitions. The record describes masking as quadruple in structured information and double-blind in its narrative, without operational detail. These limitations affect interpretation of efficacy, safety, and trial conduct; they do not show that any particular method was or was not used.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: To Compare the Efficacy and Safety of Clindamycin Phosphate 1.2% / Benzoyl Peroxide 5% Gel of CHL Versus DUAC® Gel — NCT02005666.
• Registry record last updated 2020-10-14; status last verified 2017-02.
• Results first posted 2020-09-14.
• 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.

22. Record Summary

NCT02005666 is a completed randomized, parallel-group phase 3 study of clindamycin phosphate 1.2% / benzoyl peroxide 5% gel, DUAC® Gel, and vehicle-gel placebo in patients with acne vulgaris. The planned enrollment was 850, with an intended allocation ratio of 2:2:1. Treatment was once daily for 77 consecutive days.

The primary outcome was mean percent change from baseline to week 11 in inflammatory lesion count. The posted per-protocol summaries report means of -67.6 for the test arm, -71.3 for the reference arm, and -51.9 for placebo. The test-versus-reference mean difference was 3.7, with an interval from -1.224 to 8.624 and an unadjusted p-value of 0.141.

The registry describes a 90% confidence-interval criterion for therapeutic equivalence, but the formal analysis applying that criterion is not reported. Secondary lesion-count results provide context, while the listed clinical-response success result and key analysis details are not reported in the registry record.