Adapalene-Benzoy Peroxide (BPO) Gel in the Treatment of Acne Vulgaris as a 6-month Maintenance: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Adapalene-Benzoy Peroxide (BPO) Gel in the Treatment of Acne Vulgaris as a 6-month Maintenance (NCT00687908), a randomized phase 3 study. The primary outcome is Maintenance Success for Total Lesions at Week 24.

2. Clinical Question

The question concerns maintenance of an earlier improvement rather than the initial response to treatment. This distinction matters: the endpoint is defined in relation to subjects’ prior combination therapy and measures whether a specified amount of the earlier improvement was retained during the maintenance period. It does not describe the amount of improvement from the start of the trial.

The registry also describes maintenance success for inflammatory lesions, non-inflammatory lesions, and Investigator Global Assessment, as well as adverse events. Those outcomes provide additional context for the comparison, but the primary statistical question is the Week 24 total-lesion maintenance outcome. The registry record does not report the prior-treatment response distribution or further eligibility details beyond the stated population description.

3. Trial Design

The registry identifies this as a phase 3, randomized, quadruple-masked, parallel-group study of maintenance treatment for acne. Enrollment was 243. The study is listed as completed, with a start date of 2008-11 and primary completion in 2009-07. Galderma R&D is the sponsor.

Subjects had previously been treated with adapalene-BPO gel or adapalene-BPO vehicle gel, each associated with doxycycline hyclate 100 mg. They were assigned to once-daily adapalene 0.1% / benzoyl peroxide 2.5% gel or once-daily vehicle gel. The registry’s summary describes the study purpose as assessing efficacy for acne maintenance and also assessing the safety of both investigational treatments.

The primary assessment was at Week 24, with maintenance success defined using total lesion counts and the amount of improvement retained from prior combination therapy. The registry lists secondary outcomes for inflammatory lesions, non-inflammatory lesions, Investigator Global Assessment maintenance success, and adverse events. The IGA outcome lists a timeframe of Baseline, Week 24; the lesion outcomes are listed at Week 24.

“Quadruple” masking is the masking category recorded in the registry. Further detail about which roles were masked is not reported in the registry record. The randomization sequence, allocation concealment procedures, treatment adherence, and details of the maintenance visit schedule are also not reported in the registry record. The record identifies the parallel design and the two once-daily treatment arms but does not provide further operational details about how assignment or masking was implemented.

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: ITT - Worst-case (Any missing data at Week 24 is considered as a failure)

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 Maintenance Success for Total Lesions at Week 24, measured over Week 24.

The primary endpoint is the percentage of subjects who achieved maintenance success for total lesions at Week 24. Success means maintaining at least 50 percent of the improvement in total lesion counts obtained with prior combination therapy. It is therefore a binary outcome: each subject is counted as either meeting or not meeting the stated maintenance criterion. The registry specifies an ITT population and a worst-case rule under which any missing Week 24 data are treated as failure.

A maintenance endpoint addresses whether an earlier treatment response is retained during a subsequent treatment period. Total lesion counts provide the measure used to define that retained response. Reporting the percentage meeting the criterion makes the group outcome interpretable as the proportion of subjects classified as successful under the endpoint definition; it does not convey the size of each individual subject’s change in lesion count.

This endpoint is useful for the stated maintenance question because it connects the Week 24 status to improvement obtained before the maintenance comparison. It should not be read as a measure of initial treatment efficacy, nor as a continuous measure of the amount of improvement. The registry record does not report additional endpoint-validation details or a rationale for choosing the threshold.

7. Results Posted in the Registry

• Adapalene-BPO: 78.9% (97/123) versus 45.8% (55/120) on control; risk difference 33.0 percentage points (95% CI 21.6 to 44.5), risk ratio 1.72 (1.39–2.13); 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.

Maintenance Success for Inflamatory Lesions at Week 24

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Adapalene-BPO: 78.0% (96/123) versus 48.3% (58/120) on control; risk difference 29.7 percentage points (95% CI 18.2 to 41.3), risk ratio 1.61 (1.31–1.99); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Adapalene-BPO than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Maintenance Success for Non-inflammatory Lesions at Week 24

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Adapalene-BPO: 78.0% (96/123) versus 43.3% (52/120) on control; risk difference 34.7 percentage points (95% CI 23.2 to 46.2), risk ratio 1.80 (1.44–2.26); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Adapalene-BPO than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Investigator Global Assessment (IGA) Maintenance Success at Week 24

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Adapalene-BPO: 70.7% (87/123) versus 34.2% (41/120) on control; risk difference 36.6 percentage points (95% CI 24.9 to 48.3), risk ratio 2.07 (1.58–2.72); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Adapalene-BPO than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes point in the same general direction as the primary result: the reported maintenance-success percentages are higher for adapalene-BPO than for vehicle for inflammatory lesions, non-inflammatory lesions, and Investigator Global Assessment. Each has an unadjusted p-value reported as <0.001. The shared direction provides descriptive consistency across related outcomes, while the differing definitions mean that these measures are not interchangeable with the primary total-lesion endpoint.

These outcomes relate to the primary result by examining other aspects of maintenance at Week 24. The lesion-specific outcomes divide the assessment by lesion type, while IGA provides a separate investigator assessment. Their pattern is compatible with the primary finding, but it does not establish that every outcome was a separately prespecified confirmatory test, or that the same interpretation applies to each measure.

Unadjusted secondary results carry less inferential weight when multiple outcomes are examined. In general, testing many outcomes without an adjustment can increase the chance of obtaining at least one apparently persuasive result by chance. The registry record does not report a multiplicity adjustment, a hierarchy of secondary hypotheses, or detailed prespecification for these comparisons. The p-values therefore describe each listed comparison without demonstrating that the overall error rate across the outcome set was controlled.

The record lists 4 posted secondary outcomes and no reported analyses. That absence of analysis detail does not erase the posted outcome values, but it limits assessment of how the secondary comparisons were planned and interpreted. They are best treated as supporting descriptive evidence alongside the primary result rather than as independent proof of multiple distinct claims.

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

• Maintenance Success for Inflamatory Lesions at Week 24
• Maintenance Success for Non-inflammatory Lesions at Week 24
• Investigator Global Assessment (IGA) Maintenance Success at Week 24
• Percent of Subjects With Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is this? The primary measure is a binary percentage outcome: subjects are classified according to whether they meet the maintenance-success definition. The reported group percentages are 78.9% for adapalene-BPO and 45.8% for vehicle. Binary outcomes can be described by the proportion with the outcome in each group, and between-group contrasts can be expressed on an absolute scale, such as a risk difference, or a relative scale, such as a risk ratio or odds ratio.

The registry comparison is reported as a risk difference, and the posted statistics also include risk-ratio and odds-ratio summaries. These measures answer related but different questions. The risk difference describes the absolute separation in event probabilities. The risk ratio compares those probabilities multiplicatively. The odds ratio compares the odds, rather than the probabilities, of success. When an outcome is common, the odds ratio can be numerically farther from 1 than the risk ratio; the two measures should not be treated as interchangeable.

How should the p-value be read? The primary unadjusted comparison is reported with p < 0.001. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and test assumptions. A small p-value is evidence against that null model, but it is not a measure of the size of the effect, the probability that the null is true, or the probability that the finding will be replicated. The registry labels the value unadjusted; the exact test used for the sponsor’s analysis is not reported in the registry record.

The recalculated comparison uses posted summary statistics and is a simple unadjusted re-calculation. The registry record does not identify a detailed statistical method for the original primary comparison, such as a particular test or model, nor does it describe covariate adjustment. No discrepancy is flagged between the posted summary and the recalculated comparison. Thus, the recalculation can help readers understand the reported contrast, but it should not be mistaken for a complete account of the trial’s original analysis procedures.

What does the confidence interval add? A confidence interval gives a range of effect estimates compatible with the data under the method used to construct it. Its width conveys statistical precision: wider intervals indicate greater uncertainty about the magnitude, while narrower intervals indicate more precision. For the primary risk ratio, the reported interval is 1.388 to 2.133. It lies above the value representing equal relative success between groups, consistent with the direction of the observed percentages. A confidence interval does not account for every possible source of uncertainty, including unreported analysis choices, measurement limitations, or selection of outcomes after examining results.

What is the role of the analysis population? The registry defines the primary population as ITT with a worst-case rule: any missing Week 24 result is treated as failure. This definition aims to retain subjects in the randomized comparison while specifying how missing primary outcomes are classified. It does not mean the missingness mechanism is known, or that the assumed classification is necessarily the only plausible one. The number of missing outcomes and any sensitivity analyses are not reported in the registry record.

The endpoint definition also matters statistically. A subject must retain at least 50 percent of the improvement obtained with prior combination therapy to count as a success. Converting lesion-count changes into a threshold-based outcome simplifies group comparison into proportions, but it discards information about how far each subject’s result lies above or below the threshold. Two subjects with different lesion-count trajectories can receive the same binary classification if both fall on the same side of the rule.

Why consider over-dispersion? General explanation: over-dispersion occurs when variation in the data is greater than a statistical model expects. It can make model-based uncertainty estimates too optimistic if the extra variation is ignored. For a simple binary group comparison, the relevant uncertainty depends on the observed proportions and group sizes; for more complex clustered or repeated data, dependence and extra variation may require additional modeling. The registry record does not report a model for over-dispersion, clustering, or repeated measurements, and the posted primary comparison should not be interpreted as evidence that such features were assessed.

The registry lists a total of 5 outcome measures and 4 posted secondary outcomes. It reports no detailed statistical analysis plan, analysis population definitions for the secondary outcomes, or procedure for controlling the chance of false-positive findings across multiple outcomes. Those omissions limit how far the unadjusted p-values can support confirmatory conclusions beyond the stated primary comparison.

11. Confidence Intervals and Precision

The reported group percentages are 78.9% for adapalene-BPO and 45.8% for vehicle. The primary risk-ratio estimate is 1.721, with a 95% confidence interval from 1.388 to 2.133. The interval indicates that the data are compatible with a range of relative effects, rather than identifying one exact value. It is entirely above the no-relative-difference value, which aligns with the higher observed success percentage in the adapalene-BPO group.

In general, a confidence interval is a measure of precision for an estimated effect under the statistical method used to calculate it. It is not a guarantee that the true effect lies in the interval, and its coverage interpretation depends on the method and assumptions. A narrower interval would indicate more precision than a wider one; precision is distinct from clinical importance. The interval does not resolve uncertainties caused by missing data, unreported analysis decisions, or potential limitations in how the endpoint was measured.

The registry also reports an unadjusted p-value of <0.001 for the primary comparison. This is evidence against a null model of no group difference under the relevant test assumptions, but it does not communicate the range of plausible effect sizes as directly as an interval does. The risk-ratio interval provides that effect-scale context. The registry record does not report confidence intervals for the individual arm percentages or additional sensitivity intervals for alternative missing-data assumptions.

Precision should also be considered alongside the endpoint’s threshold-based definition. The percentage classifies subjects according to whether they retained the stated share of prior improvement; it does not show the full distribution of lesion-count changes. Consequently, the interval quantifies uncertainty in the group comparison as defined, not uncertainty in every aspect of the maintenance response.

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 event counts. They are illustrations based on the observed primary effect, rather than the trial’s own documented design calculation. The assumptions listed for this illustration are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

For planning based on 100% of the observed effect, the figures are 33 participants per arm for 80% power and 44 participants per arm for 90% power. For 75% of the observed effect, they are 62 and 82 participants per arm, respectively. For 50% of the observed effect, they are 142 and 190 participants per arm, respectively.

In plain terms, 80% power means that a study planned under the stated assumptions would have an 80% chance of detecting an effect of the chosen size at the stated significance level, if that effect were present and the assumptions held. The 90% power column describes the corresponding planning target with a higher chance of detection. Smaller effects require more participants to detect reliably than larger effects under the same assumptions. These figures are planning illustrations, not observed power for this completed trial.

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 = 0.458; treatment proportion p₁ = 0.789; average p̄ = 0.623.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6852 = 1.3430.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6442 = 0.5422.
4. n = (1.3430 + 0.5422)² / (0.3303)² = 32.6, rounded up to 33 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 <- 0.458333333333333                          # control proportion
p1 <- 0.788617886178862                          # 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(687908)
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 = 33 (80% power), 44 (90% power)
 75% of observed effect: n per arm = 62 (80% power), 82 (90% power)
 50% of observed effect: n per arm = 142 (80% power), 190 (90% power)
power.prop.test: 32.6 
Simulated power at n = 33 per arm: 0.823 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and 4 secondary outcomes, but it does not report a statistical analysis plan describing how hypotheses were prioritized or how multiplicity was handled. In general, testing multiple outcomes creates multiple opportunities for a small p-value to occur by chance. A prespecified hierarchy, adjustment procedure, or clear distinction between confirmatory and exploratory outcomes can help readers assess that issue. None of those details is reported in the registry record.

The posted secondary comparisons have unadjusted p-values. Those values should therefore be interpreted as outcome-specific results, not as evidence that the probability of a false-positive conclusion across all outcomes was controlled. The registry record does not report a family-wise error procedure, a false-discovery procedure, or another multiplicity strategy. It also does not report whether the secondary analyses were prespecified in a protocol or analysis plan.

For the primary endpoint, the registry identifies the population as ITT and states that any missing Week 24 data are considered failures. This is an explicit missing-data rule and is important to the interpretation of the primary percentages. However, the number of missing outcomes, reasons for missingness, and timing of withdrawals are not reported in the registry record. No sensitivity analyses using alternative assumptions about missing outcomes are reported.

The registry record does not provide a detailed account of the analysis population for each secondary outcome, whether all randomized subjects contributed to every secondary outcome, or how missing secondary measurements were handled. It also does not report interim analyses, stopping rules, or the full statistical methods for the sponsor’s analyses. These omissions limit independent assessment of the robustness of the outcome set and the extent to which the displayed p-values reflect planned rather than post hoc comparisons.

15. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pilonidal abscess (0.8%), bipolar disorder (0.8%).

The registry reports serious adverse event counts of 1 in the adapalene-BPO group and 1 in the vehicle group. The at-risk group counts are 123 and 120, respectively. The listed serious-event terms are pilonidal abscess and bipolar disorder, each reported as 0.8%. The record does not link those terms to a specific treatment group in the posted summary, so they should not be assigned to one group based on the information available.

Other adverse events are reported for 43 subjects in the adapalene-BPO group and 27 in the vehicle group. These counts are descriptive; the registry extract does not provide event definitions, severity distributions, exposure-adjusted rates, or a comparative statistical analysis. Counts alone do not show whether events were related to treatment or how they were distributed over time.

Deaths are not reported in the registry record. The safety figures should be read as recorded adverse-event summaries, not as a complete account of all possible safety outcomes or as evidence of a causal difference between groups.

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

The posted primary result shows a higher Week 24 maintenance-success percentage in the adapalene-BPO group than in the vehicle group: 78.9% versus 45.8%. The unadjusted comparison has p < 0.001, and the reported risk ratio is 1.721 with a 95% confidence interval from 1.388 to 2.133. These statistics describe the trial’s observed groups and the defined primary outcome: maintaining at least 50 percent of prior improvement in total lesion counts.

The result does not mean that every subject in one group met the endpoint or that no subject in the other group did. It also does not quantify each subject’s change in lesions, because the primary endpoint reduces individual outcomes to success or failure under a threshold. Nor does the Week 24 result establish what happened after that assessment; longer-term outcomes are not reported in the registry record.

The randomized design supports a comparison between the assigned maintenance groups, but interpretation still depends on the trial population, endpoint definition, analysis choices, and completeness of follow-up. The primary analysis uses a stated worst-case rule for missing Week 24 outcomes, but the missing count and sensitivity analyses are not reported. Details of the original analysis plan, multiplicity handling, and the methods behind the sponsor’s comparison are also not reported in the registry record.

The secondary outcomes have a direction consistent with the primary outcome, but their unadjusted status and the lack of reported multiplicity procedures mean they should not be treated as independent confirmatory findings. Safety summaries are also descriptive and do not establish causation. Overall, the registry supports a description of the observed maintenance comparison, not a guarantee of a particular result for every subject or a conclusion about outcomes beyond those recorded.

17. Why This Trial Matters Statistically

This trial raises several useful statistical issues. First, the primary outcome is a maintenance endpoint tied to improvement achieved before the randomized comparison. Its meaning depends on both the prior-treatment context and the threshold used to classify success. Readers need to distinguish this from an endpoint measuring initial response or continuous change in lesion counts.

Second, the result is presented as a percentage and compared between randomized groups. Reading both the absolute group percentages and a relative measure such as the risk ratio helps keep the comparison grounded in the observed outcome while clarifying the relative scale. The confidence interval adds information about precision that a p-value alone cannot provide.

Third, the stated ITT worst-case rule shows how missing Week 24 outcomes were classified for the primary analysis. Such a rule is part of the estimand’s practical interpretation, but assessing its impact requires knowing how much data were missing and whether alternative assumptions change the result. Those details are not reported in the registry record.

Finally, the secondary outcomes share a consistent direction, but multiplicity matters when interpreting several unadjusted comparisons. The registry’s lack of a reported analysis plan makes it important to separate the primary result from supportive secondary patterns and to avoid treating every small p-value as a separate definitive claim. This example illustrates why effect estimates, uncertainty, endpoint definitions, missing-data handling, and analysis transparency all contribute to sound trial interpretation.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations are specific to the information in this registry record. The primary endpoint is threshold-based and refers to improvement obtained during prior combination therapy. The record does not describe the distribution of prior responses, so the starting context for the maintenance classification cannot be characterized further. The binary endpoint also does not preserve the full range of lesion-count changes.

The primary population uses a worst-case rule for missing Week 24 outcomes, but the number of missing observations, reasons for missingness, and sensitivity analyses are not reported. This prevents assessment of how much the result depends on that rule. The registry record also does not report adherence, treatment discontinuation, or details about the completeness of follow-up.

Although the study is described as randomized and quadruple-masked, details of sequence generation, concealment, and the roles included in masking are not reported. The original statistical analysis plan, the exact methods used for the sponsor’s primary comparison, and any covariate adjustment are not reported. The registry record likewise does not describe a multiplicity strategy for the secondary outcomes.

Finally, the available safety summary gives adverse-event counts and selected serious-event terms but not full event narratives, timing, exposure-adjusted analyses, or a group attribution for each listed serious term. The record does not report deaths. These limits constrain interpretation of safety and of the breadth of the result beyond the recorded Week 24 outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Adapalene-Benzoy Peroxide (BPO) Gel in the Treatment of Acne Vulgaris as a 6-month Maintenance — NCT00687908.
• Registry record last updated 2021-02-18; status last verified 2010-09.
• Results first posted 2010-09-24.
• 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

NCT00687908 is a completed phase 3 randomized, quadruple-masked, parallel-group study sponsored by Galderma R&D. Enrollment was 243; the recorded start date is 2008-11 and primary completion is 2009-07. The trial compared once-daily adapalene 0.1% / benzoyl peroxide 2.5% gel with once-daily vehicle gel as acne maintenance treatment following prior combination therapy.

The primary outcome was maintenance success for total lesions at Week 24, defined as maintaining at least 50 percent of prior improvement. The reported percentages were 78.9% with adapalene-BPO and 45.8% with vehicle. The registry also reports secondary maintenance outcomes and adverse-event summaries. Further details on the original analysis plan, multiplicity handling, missing-data counts, and several trial procedures are not reported in the registry record.