A Study to Compare the Efficacy and Safety of Topical Administration of FMX-101 for Treatment of Moderate-to-Severe Acne: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Compare the Efficacy and Safety of Topical Administration of FMX-101 for Treatment of Moderate-to-Severe Acne (NCT02815280), a randomized phase 3 study. The primary outcome is Absolute Change From Baseline in the Inflammatory Lesion Count at Week 12.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, parallel-group Phase 3 study of topical FMX-101, 4% minocycline foam, compared with vehicle foam in moderate-to-severe acne vulgaris. The registry record lists total enrollment as 495. The primary completion date was 2017-10-13, and the study status is completed. The record lists a start date of 2016-05.

Both study arms are described as applying their assigned foam topically once daily for 12 weeks. The primary efficacy timeframe was baseline to Week 12. The active-treatment and vehicle groups in the primary result included 333 and 162 participants, respectively. The record identifies the primary analysis population as the intention-to-treat population, defined there as all randomized participants.

The official title describes evaluation of efficacy, safety, and long-term safety over 1 Year. The treatment descriptions specify once-daily use for 12 weeks. The registry record also lists an open-label FMX-101 group in its adverse-event information, but the detailed procedures and timing for that group are not reported in the registry record. The study's original allocation ratio, eligibility criteria beyond the acne condition, site details, and adherence procedures are not reported in the registry record.

Randomization helps create comparable groups at the point of assignment, while double blinding is intended to limit differences in expectations or assessment associated with knowing the assigned treatment. These are general design principles; the registry record does not describe how randomization was implemented or how masking was maintained. The parallel-group structure means the listed groups received their assigned treatment during the study rather than being described as crossing over between treatments. Further design details 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.

Before assignment: The study consisted of a varied screening period. All participants underwent inclusion and exclusion criteria assessment and all eligible participants signed the informed consent before undergoing any study related procedures. All assessments at screening were done as per the schedule of assessment.

Double-Blind Phase

Reasons for not completing this period:

Open-Label Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: An ITT population: included all randomized participants.

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.

Population: Double-blind participants (Intent-to-Treat population \[ITT\]) were moved to open-label (safety population). An ITT population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Absolute Change From Baseline in the Inflammatory Lesion Count at Week 12, measured over Baseline and Week 12.

The primary endpoint was absolute change from baseline in inflammatory lesion count at Week 12. It concerns the number of inflammatory acne lesions, specifically papules, pustules, and nodules. The registry record defines change as baseline value minus post-baseline value. Under that direction, a positive change indicates fewer lesions at the later assessment than at baseline, while a negative change would indicate a higher count at the later assessment.

Lesion count is a continuous measure: it can take a range of numerical values rather than recording only whether a participant did or did not meet a threshold. Comparing the average change between randomized groups can describe the difference in their measured changes over the stated follow-up. The registry reports least-squares means with standard errors for the group results and an ANCOVA analysis for the between-group comparison.

As a general statistical rationale, a continuous endpoint can preserve information about the amount of change rather than reducing participants to categories such as success or no success. The endpoint is clinically interpretable as a change in the count of specified lesions, but the registry result alone does not describe participants' experience, the importance of a given count change, or how the measure relates to outcomes beyond the stated assessment. Details of the endpoint's assessment procedures and any threshold for meaningful change are not reported in the registry record.

7. Results Posted in the Registry

• FMX-101, 4% Minocycline Foam: mean 13.78 versus 10.64 on control; difference 3.14 (95% CI 0.89 to 5.39), standardized effect d = 0.26; z-test p = 0.006.

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.

Percent Change From Baseline in the Non-inflammatory Lesion Count at Week 12

• 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 errors.
• Result:
  • FMX-101, 4% Minocycline Foam: mean 26.33 versus 13.49 on control; difference 12.84 (95% CI 2.10 to 23.58), standardized effect d = 0.23; z-test p = 0.019.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FMX-101, 4% Minocycline Foam than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists several secondary outcomes, including non-inflammatory lesion-count change, inflammatory lesion-count change at earlier visits, treatment success, and adverse-event outcomes. The detailed numerical secondary efficacy result available for comparison concerns percent change in non-inflammatory lesion count at Week 12. Its reported pattern is in the same direction as the primary endpoint: the FMX-101 group has a larger average reduction than the vehicle group, and the reported ANCOVA comparison is a superiority analysis. The registry also reports a recalculated unadjusted comparison for that outcome.

This general alignment offers context: the posted Week 12 result for a different lesion category points in a direction consistent with the primary inflammatory lesion-count result. It does not establish that all secondary outcomes had the same pattern. Detailed numeric results for the other listed secondary outcomes are not reported in the registry record described for these results, so no broader claim about their findings is warranted.

Secondary outcomes are generally interpreted with more caution when many outcomes, time points, or comparisons are examined. As a general statistical principle, testing multiple hypotheses increases the chance that some results will appear statistically notable by chance if no adjustment is made. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary analyses. The unadjusted secondary results therefore carry less weight than the designated primary endpoint, particularly when considered separately from a prespecified testing strategy.

The secondary findings can support context around the primary endpoint, but they should not be treated as independent confirmation without considering how they were selected and analysed. Their interpretation is also limited by the lack of detail about missing data and model specifications. The registry record does not report a complete multiplicity plan or the numerical results for every listed secondary outcome.

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

• Percent Change From Baseline in the Non-inflammatory Lesion Count at Week 12
• Absolute Change From Baseline in the Inflammatory Lesion Count at Week 6 and Week 9
• Percentage of Participants Achieving IGA Treatment Success at Week 6 and Week 9
• Number of Participants With Treatment-emergent Adverse Events (TEAEs) and Treatment-emergent Serious Adverse Events (TESAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, the registry reports least-squares mean changes and standard errors by randomized group, followed by an ANCOVA comparison. These are two related but distinct summaries. A group mean describes the average outcome in a group, while the between-group estimate addresses how far apart the groups are on the chosen outcome scale. The reported primary group means are 13.78 for FMX-101 and 10.64 for vehicle, and the sponsor's ANCOVA mean difference is 3.15.

What does ANCOVA contribute?

ANCOVA is a general statistical method for comparing groups on an outcome while accounting for one or more covariates. In clinical trials, baseline outcome values are commonly relevant covariates because participants may begin with different measurements. Adjusting for a covariate can improve precision when the adjustment is appropriate and specified in the analysis. The registry names ANCOVA but does not report which covariates were included, the model specification, or other implementation details. It is therefore not possible to describe the exact adjustment beyond identifying the reported method.

The sponsor's reported comparison is labelled a mean difference in final values and is reported with a 95% confidence interval and p-value. The endpoint description frames the outcome as change from baseline, while the analysis label refers to final values. The registry does not provide enough model detail to resolve how the analysis label and endpoint description were operationalized. The reported analysis should be read as the sponsor's stated ANCOVA result, rather than reconstructed into a different model.

What is a standard error?

A standard error describes the sampling uncertainty of an estimated quantity, such as a group mean. In general, smaller standard errors indicate more precise estimates, while larger standard errors indicate greater sampling uncertainty. The posted standard errors for the primary group means are 0.66 for FMX-101 and 0.94 for vehicle. They are not standard deviations of individual participants' outcomes. A standard deviation describes variation among observations; a standard error describes uncertainty in an estimate.

The recalculated comparison uses the posted group summary statistics and is labelled unadjusted. It estimates a mean difference of 3.14 and an unadjusted p-value of 0.006. This is a simple comparison based on the available summaries, not a reproduction of the sponsor's ANCOVA. The pooled standard deviation used for an effect-size illustration is listed as 12.02, and the standardized effect estimate is 0.261. These quantities help describe the result on different scales, but they do not replace the primary analysis or establish clinical importance.

Why can adjusted and unadjusted estimates differ?

An adjusted analysis can account for covariates, whereas an unadjusted comparison does not. The estimates may consequently differ because they rely on different information and assumptions. Even close estimates should not be treated as proof that the methods are interchangeable. In this trial, the sponsor's ANCOVA estimate is 3.15 and the recalculated unadjusted estimate is 3.14. The registry discrepancy flag is false, but the sponsor's analysis remains the primary reported analysis.

The reported p-value tests the data against a null comparison of no group difference under the model and assumptions used. In general, a small p-value indicates that data at least as incompatible with that null result would be unusual under the null model. It does not show the probability that treatment has no effect, quantify the chance that the finding is due to bias, or measure how important the difference is. Interpretation should consider the estimate and its confidence interval as well as the p-value.

Why can count outcomes need careful modelling?

As a general statistical point, counts often have distributions that are not well described by a normal model, especially when the counts are skewed or their variability exceeds what a simple count model expects. Over-dispersion means greater variability than the model allows; if ignored, uncertainty estimates can be too small and tests can be misleading. Methods for count outcomes may address these features directly, while ANCOVA can be used in some settings depending on the outcome distribution and model assumptions. The registry record does not report diagnostic checks, distributional assumptions, or any alternative count model. No conclusion about those modelling choices can be drawn from the method label alone.

The registry's endpoint description specifies the intention-to-treat population as all randomized participants. This identifies the intended population for the primary outcome but does not state how missing Week 12 measurements were handled, whether all randomized participants contributed observed endpoint data, or whether any imputation was used. Those details are not reported in the registry record. In general, the treatment of missing outcome data can affect an estimate and its uncertainty, so the analysis population label alone is not a complete description of the analysis.

11. Confidence Intervals and Precision

A confidence interval communicates uncertainty around an estimated difference. The sponsor-reported primary estimate is 3.15, with a 95% confidence interval from 0.95 to 5.35. The interval is centered around an estimate of the group difference and gives a range of values compatible with the observed data under the analysis assumptions. It is not a guarantee that the true difference lies in that particular interval, nor does it describe the range of individual participants' responses.

The interval does not include zero, which is consistent with the reported p-value of 0.005 for a test of no difference under the ANCOVA analysis. This relationship is a general feature of two-sided tests and confidence intervals constructed using corresponding methods. The interval's width also matters: a narrow interval indicates greater precision than a wide interval, all else equal. The registry gives the confidence limits but does not define a threshold for a difference considered important to patients or investigators.

The unadjusted recalculation also gives an estimate close to the sponsor's reported estimate. Its interval is not repeated because the recalculation is not the sponsor's primary analysis. The sponsor-reported interval should guide interpretation of the registry analysis, and the recalculated result is a supplementary check based on summary statistics. Neither interval resolves uncertainty about generalizability, missing data, model assumptions, or outcomes beyond Week 12.

The standard errors accompanying the group means are 0.66 for FMX-101 and 0.94 for vehicle. These quantify uncertainty around the group estimates, rather than the spread of individual lesion-count changes. Precision of the group difference is more directly conveyed by the confidence interval for the between-group estimate. The reported confidence interval should be considered together with the effect estimate and the limitations of the registry's analysis detail.

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 illustrate the approximate group size that would be needed under stated assumptions to detect specified fractions of the observed primary effect. For the full observed effect, the illustration gives 230 participants per arm for 80% power and 308 participants per arm for 90% power. For 75% of the observed effect, the figures are 409 and 548 participants per arm. For 50% of the observed effect, they are 920 and 1,232 participants per arm.

Power is the probability, under a particular assumed effect and statistical model, of detecting a difference at the selected significance level. The 80% column means the illustrated design would have an 80% chance of detecting the specified effect if the assumptions hold; the 90% column means a 90% chance under those assumptions. These are planning illustrations, not observed power.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the stated fraction of the observed effect as the effect to detect. The assumptions used for the trial's original design and sample-size justification are not reported in the registry record; these figures do not establish what planning assumptions the trial actually used.

Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants. The illustrated requirements rise as the assumed effect is reduced from the full observed effect to 75% and then 50%. These values are conditional planning calculations, not a forecast of what a future study would necessarily observe. They also do not address changes in allocation, dropout, missing outcome data, or analysis methods beyond the stated assumptions.

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 = 3.140; pooled standard deviation σ = 12.018.
2. n = 2 × (1.96 + 0.842)² × 12.018² / 3.140² = 230.0, rounded up to 230 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 <- 3.14                      # observed difference in means
sigma <- 12.0179251515929                     # 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(2815280)
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 = 230 (80% power), 308 (90% power)
 75% of observed effect: n per arm = 409 (80% power), 548 (90% power)
 50% of observed effect: n per arm = 920 (80% power), 1,232 (90% power)
power.t.test: 230.9 
Simulated power at n = 230 per arm: 0.796 (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's sponsor-reported primary analysis is an ANCOVA comparison. It gives a mean difference of 3.15, a 95% confidence interval from 0.95 to 5.35, and p = 0.005. The registry labels this analysis as a superiority analysis. Its direction is consistent with the endpoint definition, under which positive change means a reduction in inflammatory lesion count.

The unadjusted recalculation from the posted group summaries gives a mean difference of 3.14 and p = 0.006. This is a straightforward calculation from summary statistics and does not reproduce the sponsor's ANCOVA adjustment. Small differences between the recalculation and the sponsor result are expected when the methods or information used are not identical. The registry record does not flag a discrepancy between them.

The sponsor's own analysis takes precedence for describing the trial's reported primary result. The recalculation can serve as a transparent cross-check of the general magnitude and direction, but it should not replace the reported adjusted analysis. Because the registry does not describe the ANCOVA covariates or full model specification, the precise source of the small difference between estimates is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis considers more than one outcome, time point, subgroup, or statistical comparison. As a general principle, the more hypotheses tested, the greater the opportunity for at least one apparently notable finding to occur by chance under a set of null hypotheses. Common approaches include prespecifying a primary outcome, controlling the overall error rate across a family of tests, or treating secondary results as exploratory. The registry identifies a primary endpoint and lists secondary outcomes, but a multiplicity adjustment or formal testing hierarchy is not reported in the registry record.

The primary result is therefore the clearest focal comparison in the posted results. Secondary results can add context, but their p-values should not automatically be read as if they were the only tests conducted. The registry reports a Week 12 non-inflammatory lesion result and lists other secondary outcomes, but does not report the complete statistical plan needed to determine how the full set of comparisons was intended to be interpreted.

The primary endpoint description identifies the intention-to-treat population as all randomized participants. This is a useful definition of the target analysis population, but it does not explain whether every randomized participant had a Week 12 measurement or how missing measurements were treated. Methods such as complete-case analysis, imputation, or sensitivity analysis are not reported in the registry record. The number of participants included in each specific endpoint analysis beyond the group summaries is also not fully described.

Missing outcome data can affect both the estimate and its uncertainty, particularly if the probability of missingness is related to treatment or outcome. That is a general concern, not evidence that a particular missing-data problem occurred in this trial. The record does not report reasons for missing assessments, dropout patterns, or sensitivity analyses. The effect of any missing data on the result cannot be assessed from the reported information.

Further details about the analysis plan, covariates, model checks, handling of protocol deviations, and interim analyses are not reported in the registry record. No assumptions about these procedures can be made from the stated ANCOVA method or the intention-to-treat label alone. These omissions limit how fully the analysis can be independently evaluated.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: biliary dyskinesia (0.6%), cholecystitis (0.6%), pneumonia (0.6%), intestinal obstruction (0.3%), intestinal perforation (0.3%).

The registry lists safety counts for double-blind and open-label groups. In the double-blind FMX-101 group, 4 of 333 participants were affected by serious adverse events, and 40 of 333 were affected by other treatment-emergent adverse events. In the double-blind vehicle group, 2 of 162 participants were affected by serious adverse events, and 15 of 162 were affected by other treatment-emergent adverse events. The listed death count was 0 in each of these groups.

The open-label FMX-101 group lists 1 of 373 participants affected by a serious adverse event and 38 of 373 affected by other treatment-emergent adverse events; the listed death count was 0. The open-label group should be kept distinct from the randomized, double-blind comparison when reading these counts. The registry record does not report enough detail to establish how the open-label participants relate to the randomized groups or the timing of their exposure.

These are participant counts, not evidence that an event was caused by treatment. The record lists serious-event terms and their reported percentages, but the counts alone do not establish comparative risk or causality. Differences in group size and study context matter, and the safety figures should not be interpreted as a complete assessment of long-term safety. Further details about event definitions, exposure time, and attribution are not reported in the registry record.

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

The primary result describes an average between-group difference in change in inflammatory lesion count at Week 12. Under the registry's definition, positive changes indicate decreases from baseline. The sponsor-reported ANCOVA estimate is 3.15, with a 95% confidence interval from 0.95 to 5.35. This supports a statistical distinction between the group averages under the reported analysis and its assumptions.

The estimate does not mean that every participant had a reduction of that amount, nor does it describe the distribution of individual responses. A group average can combine participants with larger reductions, smaller reductions, no change, or increases. The registry record does not report response distributions or a threshold for a change considered meaningful, so the practical meaning for an individual cannot be determined from the average alone.

The result is specific to the primary outcome and Week 12 comparison. It does not by itself establish an effect on every secondary outcome, outcomes at other time points, or longer-term outcomes. Although the official title refers to long-term safety over 1 Year, the primary endpoint is a Week 12 efficacy measure, and the record does not provide detailed long-term safety analyses in the registry record for this result.

Statistical evidence is not the same as evidence of clinical importance. A confidence interval excluding zero is evidence against a zero average difference under the analysis assumptions, but the interval does not indicate whether the estimated difference crosses a clinically important threshold. Such a threshold is not reported in the registry record. Similarly, the p-value does not state the probability that the result is true or quantify the chance of bias.

The comparison should also be read in light of the design and reporting information available. The study was randomized and double-blind, but details of randomization, missing-data handling, and the full analysis plan are not reported in the registry record. The results describe this trial's reported groups and timeframe; they do not on their own establish how broadly the findings apply to people or settings not described in the record.

18. Why This Trial Matters Statistically

This trial illustrates how a clinical endpoint can be translated into a direct group comparison. The primary measure was a count of specified inflammatory lesions, and the change convention made decreases positive. That definition is important: without knowing its direction, the sign of a mean difference could be misread. Statistical interpretation begins with the measurement and its scale, not just the p-value.

The results also show why adjusted and unadjusted estimates should be distinguished. The sponsor's ANCOVA analysis reports a mean difference of 3.15, while the summary-statistic recalculation gives 3.14. Their proximity offers a useful check, but the methods are not identical. The adjusted analysis remains the trial's reported primary result, and the recalculation does not replace it.

Precision is another central part of interpretation. The sponsor-reported confidence interval runs from 0.95 to 5.35, which conveys a range of uncertainty around the estimated group difference rather than a single certain value. Considering the interval alongside the point estimate and the endpoint's meaning is more informative than relying on a p-value alone.

The trial also demonstrates the distinction between evidence for a primary outcome and evidence across multiple outcomes. A secondary result in the same general direction can provide context, but a registry record without a reported multiplicity plan cannot establish how all secondary comparisons were intended to contribute to a single conclusion. Likewise, safety counts require careful reading by group and study context rather than simple causal attribution.

Finally, the record makes clear that an analysis label is not a full statistical plan. Knowing that an ANCOVA was used and that the primary population was intention-to-treat does not reveal covariates, missing-data procedures, model checks, or sensitivity analyses. Those details matter for judging reproducibility and robustness, and they are not reported in the registry record.

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.

Several trial-specific details needed for a fuller assessment are not reported in the registry record. The randomization method, allocation concealment, masking procedures, study sites, and adherence information are not described in the registry record. The record identifies a randomized, double-blind, parallel design, but those labels do not specify how each procedure was carried out.

The primary endpoint is described as a baseline-to-Week 12 change, but the reported analysis is labelled ANCOVA for mean difference in final values. The registry does not give the covariates or model specification, so the precise adjustment cannot be assessed. It also does not report model diagnostics or the distributional assumptions used for the lesion-count outcome.

The record identifies the intention-to-treat population as all randomized participants, but it does not report the handling of missing Week 12 measurements, reasons for missingness, or sensitivity analyses. Details about protocol deviations and endpoint-specific analysis populations are also not reported in the registry record. These omissions prevent a complete assessment of whether the findings are robust to alternative missing-data assumptions.

The registry lists multiple outcomes and time points, but a multiplicity plan is not reported. Numerical details for all listed secondary outcomes are not available in the registry record for these results. The interpretation of secondary evidence is therefore limited, and the total pattern of results cannot be fully evaluated from the reported information.

Safety information includes counts in double-blind and open-label groups, but the open-label group's relation to the randomized participants, event attribution, exposure time, and detailed follow-up are not reported in the registry record. The official title mentions long-term safety over 1 Year, but detailed long-term outcome information is not included. The original sample-size justification and design assumptions are also not reported; the planning illustrations based on the observed effect do not reveal the original design rationale.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Compare the Efficacy and Safety of Topical Administration of FMX-101 for Treatment of Moderate-to-Severe Acne — NCT02815280.
• Registry record last updated 2022-01-18; status last verified 2022-01.
• Results first posted 2020-11-24.
• 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.

23. Record Summary

NCT02815280 is a completed randomized, double-blind, parallel-group Phase 3 study of FMX-101, 4% minocycline foam versus vehicle foam for moderate-to-severe acne vulgaris. The registry lists 495 participants enrolled. Both treatment descriptions specify once-daily topical use for 12 weeks.

The primary endpoint was change from baseline in inflammatory lesion count at Week 12, with positive changes defined as decreases. The sponsor-reported ANCOVA comparison was a mean difference of 3.15, with a 95% confidence interval from 0.95 to 5.35 and p = 0.005. The registry describes the primary population as all randomized participants.

One detailed secondary efficacy comparison is reported for non-inflammatory lesion-count change at Week 12. Safety counts are listed for double-blind and open-label groups. Details on multiplicity, missing-data handling, the full statistical model, and the original sample-size justification are not reported in the registry record.