Efficacy and the Tolerability of the Sequential Application of Two Marketed Products in Patients With Acne Vulgaris: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and the Tolerability of the Sequential Application of Two Marketed Products in Patients With Acne Vulgaris (NCT01461655), a randomized phase 2 study. The primary outcome is Percentage Change in Inflammatory Lesions From Baseline to End of Treatment.

2. Clinical Question

The clinical question is framed within a split-face design rather than as a conventional comparison of separately described patient groups. The registry labels the study randomized and single-masked, while its model field reads single group. These labels do not fully explain how sides were assigned, who was masked, or how within-person pairing was handled in the analysis. Those design details are not reported in the registry record, so the posted side-specific summaries should be read with that uncertainty in mind.

3. Trial Design

This is a completed Phase 2 study of sequential topical products in patients with acne vulgaris. The registry describes it as an exploratory proof-of-principle study and identifies a split-face model. It records randomized allocation and single masking. The recorded enrollment is 40. The study start is listed as 2011-11, and primary completion as 2012-04.

The two posted primary-result arms are Topical Retinoid - Placebo and Topical Retinoid-NSAID. The listed interventions include a marketed topical retinoid, a marketed topical NSAID, and vehicle gel. The intervention list repeats the marketed topical retinoid. Arm descriptions are blank, so the registry record does not fully spell out which product was applied to each side, the order of application, or the randomization procedure. It also does not state who was masked.

The registry gives an arm-level n of 40 for each primary summary. Because the study is described as split-face while the model field says single group, these arm summaries should not automatically be interpreted as counts from independent patient groups. The record does not explain whether results were paired within each participant or how the analysis accounted for the split-face structure. It lists no reported analyses. The distinction matters: a paired analysis uses the within-person relationship between the two sides, whereas an independent-groups analysis does not.

The study status is completed. The record does not report a sample-size justification or enough information to reconstruct the planned analysis. The separate planning illustrations are based on observed effects and are not the trial's stated design calculation.

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 Percentage Change in Inflammatory Lesions From Baseline to End of Treatment, measured over Baseline to End of treatment (4 weeks).

The primary endpoint is the percentage change in inflammatory lesion count from baseline to end of treatment, with the timeframe specified as 4 weeks. It measures change in the number of inflammatory lesions relative to the baseline count, rather than the absolute number of lesions at a single visit. A negative percentage change corresponds to a lower count at the end of treatment than at baseline under this change-score convention.

Lesion-count change is used to describe how acne lesions vary over the treatment period. The registry specifies the primary summary as a median and lists standard deviation as the measure of dispersion. The posted values are -20.3 for the retinoid-placebo arm and -29.4 for the retinoid-NSAID arm. These are arm-level summaries, not a reported treatment-effect estimate with a confidence interval. No comparative primary analysis or confidence interval is listed in the registry record.

The median describes the central position of the observed changes, while a dispersion measure describes variability. In general, a confidence interval would communicate uncertainty around a comparative estimate; it is not available for this primary endpoint in the posted results. The record does not provide information about how the lesion counts were assessed or how missing end-of-treatment measurements were handled.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

What does the primary summary represent?

The registry reports a median percentage change for the primary endpoint and identifies standard deviation as its dispersion measure. A median is the middle value after observed changes are ordered. A standard deviation describes how spread out observations are around a central value. In general, the median is less affected than the mean by extreme observations, while standard deviation is commonly used to describe dispersion around a mean. The record does not explain why this combination of summary and dispersion was selected.

These are summaries for each listed treatment side. They are not themselves a comparison estimate. To estimate a comparative effect, an analysis would need to define the contrast and account for the study design. For a split-face study, paired observations may be related because both sides are measured within the same participant. General statistical principle: accounting for that pairing can change the uncertainty of a treatment contrast. The registry record does not say whether the primary analysis used paired data.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the observed data under a specified statistical model and analysis procedure. For the recalculated secondary comparisons, the interval is attached to an unadjusted mean difference. If an interval includes zero, the data are compatible with no difference under that calculation, as well as with effects in either direction within the interval. The interval does not assign a probability to a particular true value, and it does not resolve limitations such as unreported pairing or missing-data handling.

The primary endpoint has no confidence interval listed. It is therefore not possible to describe the precision of a primary treatment contrast from the posted primary summaries. A reader should distinguish the spread of individual observations, described by a standard deviation, from the uncertainty around a comparative estimate, which would ordinarily be conveyed by a confidence interval or related inferential result.

What are the recalculated secondary comparisons?

For continuous secondary outcomes, the posted recalculations compare arm means using an unadjusted mean difference and provide confidence limits and an unadjusted p-value. “Unadjusted” means that the calculation does not account for the testing of multiple endpoints. These recalculations are not listed as registry-reported analyses. They use posted summary statistics, and they should be treated as supplementary rather than as a substitute for a prespecified analysis.

General statistical principle: the standard error quantifies the estimated variability of a statistic across repeated samples under the assumed model. The confidence interval is constructed from that uncertainty. In a split-face design, an analysis that treats sides as independent may not represent the true uncertainty if measurements are paired. The calculation details in the record do not resolve that design issue, so the reported recalculated intervals should be read with caution.

A p-value measures how unusual the observed data, or more extreme data, would be under a specified null model. It is not the probability that the null hypothesis is true, nor a direct measure of clinical importance. An unadjusted p-value also does not account for the possibility of false-positive findings across a collection of outcomes. Because the registry lists no reported analyses, the recalculated p-values should not be described as sponsor-reported results.

Why does over-dispersion matter?

General statistical principle: over-dispersion occurs when variability in the data is greater than a chosen model expects. It can make standard errors too small and confidence intervals too narrow if ignored. Lesion counts are counts, and count data can show more variability than a simple model assumes. However, the posted endpoint is a percentage change, and the registry does not report a count-data model, a dispersion assessment, or an adjustment for over-dispersion. It is therefore not possible to say whether over-dispersion was assessed or affected the analysis.

Dispersion of individual changes also affects precision: greater variability generally makes a treatment contrast harder to estimate precisely. The record lists standard deviations for the primary and secondary summaries, but it does not provide a formal primary contrast or its standard error. General explanations of variability do not fill that reporting gap.

How should the planning illustrations be used?

The sample-size illustrations are calculated from an observed effect under stated planning assumptions: two-sided significance level 0.05, equal allocation between arms, and a normal approximation. They show hypothetical participants per arm for 80% and 90% power when planning for 100%, 75%, or 50% of the observed effect. They are planning scenarios, not observed power and not evidence of what the original investigators planned.

General statistical principle: planning calculations depend on the assumed effect, variability, significance threshold, power target, and analysis design. If the assumed effect is uncertain or the analysis should account for paired observations, a different design calculation may be appropriate. The registry does not report the original sample-size justification, and the record does not establish that these hypothetical calculations match the study's design. They should not be used to infer that the study had a particular probability of detecting an effect.

10. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes, including lesion counts, percentage changes, and an investigator global assessment. It does not report a multiplicity adjustment, a hierarchy of hypotheses, or a strategy for deciding which secondary outcomes would be confirmatory. When multiple outcomes are tested, the chance of obtaining at least one apparently unusual result can rise. General statistical principle: adjustment procedures or a prespecified testing hierarchy can help control this issue. Without a reported plan, unadjusted secondary p-values should be regarded as exploratory.

The record lists no reported analyses. It does not state the analysis population for the primary endpoint or secondary outcomes, whether the analysis followed intention-to-treat principles, or whether any participants or observations were excluded. The arm-level summaries report n of 40 for each side, but this does not establish that every enrolled participant had complete data for every endpoint.

Missing-data methods are not reported in the registry record. The record does not explain whether missing lesion counts occurred, how any missing observations were handled, or whether a sensitivity analysis was conducted. Missingness can affect both the estimate and its uncertainty, particularly if the probability of missing data is related to the observed outcome. That is a general concern, not a claim that missing data occurred in this study.

The registry also does not describe how the split-face structure was incorporated into the analysis. It is not clear whether the comparison used paired observations or another method, nor how randomization of sides was performed. These omissions limit assessment of the analysis assumptions and of the precision represented by the secondary recalculations. A protocol, statistical analysis plan, or fuller report might clarify these points, but details beyond the registry record are not stated.

11. 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 adverse-event record combines the two treatment-side labels in one group. It lists 40 at risk for serious adverse events and 0 affected; no serious adverse-event terms are listed. The death value is null, which means deaths are not reported in the registry record, rather than establishing a zero count.

For other adverse events, the combined group lists 40 at risk and 40 affected. These figures should be read as the registry's grouped adverse-event reporting, not as a count of separate event episodes. The record does not give event terms, severity, timing, or an arm-specific breakdown for these other events. It also does not explain how adverse events were attributed between the two sides in the split-face design.

General statistical principle: a recorded count of zero serious events does not establish that the underlying risk is zero, especially when the study is exploratory and the registry record gives limited detail. The safety figures describe what was recorded in this entry; they do not provide a complete comparative safety analysis or establish how the products would perform in other populations or settings.

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

The posted primary summaries describe median percentage changes in inflammatory lesion counts over the specified treatment period. Both arm summaries are negative, and the retinoid-NSAID summary is more negative than the retinoid-placebo summary. These figures describe the observations recorded for each side; they do not, by themselves, establish a statistically reliable or clinically important difference.

No primary comparative estimate, confidence interval, or registry-reported inferential test is listed. The result therefore cannot show how precise the between-side contrast is. Nor does the record explain whether analysis accounted for the paired structure implied by the split-face design. These omissions prevent a complete assessment of the evidence for a difference between the treatment sides.

The secondary summaries provide context across related lesion measures, but their recalculated comparisons are unadjusted and were not listed as registry-reported analyses. Considering multiple outcomes without a reported multiplicity strategy makes individual secondary findings less persuasive as confirmatory evidence. The planning illustrations are hypothetical design calculations based on observed effects and must not be interpreted as observed power.

The registry records a completed exploratory Phase 2 study with enrollment of 40 and describes a proof-of-principle split-face approach. It does not report enough information about eligibility, analysis populations, missing data, treatment sequence, or statistical methods to determine how broadly the results apply. The posted data do not establish efficacy, lack of efficacy, or comparative safety. They describe observed summaries and leave material uncertainty about the treatment contrast and its precision.

In practical statistical terms, the record is most useful as a description of the reported lesion changes and as an example of why design and analysis details matter. It should not be read as a definitive estimate of a treatment effect. Further interpretation would require a clearly specified comparative analysis that accounts for the study structure and reports its uncertainty, together with fuller information on conduct and analysis.

13. Why This Trial Matters Statistically

This study is statistically notable because its split-face description calls attention to pairing. When both sides of a participant are observed, the two measurements may be related. A design can use that relationship to make a comparison more informative, but the analysis needs to reflect the pairing. The registry record does not state whether it did so. This makes the study a useful reminder that arm labels and arm-level summaries do not by themselves reveal the effective comparison or its uncertainty.

The record also illustrates the difference between descriptive summaries and comparative inference. The primary result gives a median for each side, but no registry-reported contrast or confidence interval. Secondary recalculations add mean differences and uncertainty intervals, yet these are unadjusted and not listed as reported analyses. A numerical difference between summaries is not equivalent to evidence that the underlying treatment effects differ.

The planning illustrations have a separate role. They translate observed effects into hypothetical future-study planning scenarios under stated assumptions. They are not retrospective evidence of power, do not show what the investigators planned, and cannot repair missing information about the original statistical plan. Keeping planning calculations distinct from trial results is important for avoiding overconfident interpretation.

Finally, the registry's reporting gaps matter for both efficacy and safety interpretation. Analysis populations, handling of missing data, multiplicity, and details of the split-face analysis are not reported. Recognizing these limits helps keep conclusions proportional to the available statistical evidence rather than treating exploratory results as a complete comparative evaluation.

14. 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.

Several limitations are specific to this record. First, the registry describes a randomized, single-masked split-face study but labels the model single group. It does not explain how treatment sides were assigned or who was masked. The arm descriptions are blank, and the order and application details for the sequential products are not reported in the registry record.

Second, the primary endpoint is presented as arm-level medians with standard deviations, but there is no reported comparative estimate, confidence interval, or test. The record does not say whether the analysis accounted for the paired nature of the split-face design. As a result, the precision of the primary contrast cannot be assessed from the posted primary result.

Third, the record lists no reported analyses and does not describe analysis populations, exclusions, missing-data handling, or sensitivity analyses. It also does not report a multiplicity plan for the several secondary outcomes. The unadjusted recalculations are useful as exploratory summaries, but they cannot establish confirmatory findings or compensate for these omissions.

Fourth, the registry does not report eligibility criteria, baseline lesion counts, or detailed assessment procedures. The adverse-event figures are grouped across the two treatment labels, with no event terms listed for other adverse events and no arm-specific breakdown. The death field is not reported in the registry record. These limitations constrain interpretation of both the lesion outcomes and the safety entries.

15. Related Tutorials

16. Related Statistical Calculators

17. Sources

• ClinicalTrials.gov: Efficacy and the Tolerability of the Sequential Application of Two Marketed Products in Patients With Acne Vulgaris — NCT01461655.
• Registry record last updated 2025-03-10; status last verified 2016-12.
• Results first posted 2013-12-04.
• 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.

18. Record Summary

The registry record describes a completed, randomized, single-masked Phase 2 exploratory study of sequential topical products for acne vulgaris, using a split-face model. It records enrollment of 40 and lists a 4-week primary endpoint: percentage change in inflammatory lesion count from baseline to end of treatment.

The primary summaries are medians for Topical Retinoid - Placebo and Topical Retinoid-NSAID. The record does not list a comparative primary analysis or confidence interval. Secondary outcomes provide additional descriptive summaries, with unadjusted recalculations for some comparisons. The registry does not report a multiplicity plan, analysis populations, missing-data methods, or how the split-face structure was handled statistically.

The adverse-event entry reports no serious adverse events in the combined group, while its death value is not reported in the registry record. Overall, the record supplies descriptive outcome and safety figures but leaves important details of analysis and interpretation unresolved.