Safety and Efficacy of Azelaic Acid Foam, 15 % in Papulopustular Rosacea: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Azelaic Acid Foam, 15 % in Papulopustular Rosacea (NCT01555463), a randomized phase 3 study. The primary outcome is Percentage of Participants With Investigator's Global Assessment (IGA) Based Therapeutic Success at End of Treatment (LOCF: Last Observation Carried Forward).

2. Clinical Question

3. Trial Design

This was a Phase 3 randomized, double-blind, vehicle-controlled, multicenter, parallel-group clinical trial of azelaic acid foam, 15%, for papulopustular rosacea. The registry record lists an enrollment of 961. The study is marked completed; the listed start was 2012-09 and primary completion was 2014-01. The sponsor was LEO Pharma.

The active-treatment group received 0.5 g azelaic acid foam applied topically and nonocclusively to facial skin twice daily for 12 weeks. The comparator group received 0.5 g vehicle foam in the same manner and for the same duration. The primary endpoint was assessed at end of treatment, with the outcome timeframe described as up to 12 weeks. Double masking and random allocation are recorded, but further details about implementation of randomization, allocation concealment, or masking procedures are not reported in the registry record.

The primary analysis population comprised randomized participants who were dispensed any study medication. For a missing end-of-treatment observation, the last non-missing observation was carried forward, including baseline. The registry record lists 483 participants in the azelaic acid group and 478 in the vehicle group for the primary outcome. It also lists 18 outcome measures and 2 analyses. A full protocol, detailed eligibility criteria, and the original trial-specific sample-size assumptions 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.

Treatment

Reasons for not completing this period:

Follow up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All subjects who were randomized and who were dispensed any study medication. For subjects with missing end of treatment observation the last non-missing observation was carried forward, including baseline.

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 of Participants With Investigator's Global Assessment (IGA) Based Therapeutic Success at End of Treatment (LOCF: Last Observation Carried Forward), measured over At end of treatment (LOCF), up to 12 weeks.

The primary endpoint is the percentage of participants with Investigator's Global Assessment (IGA)-based therapeutic success at end of treatment, using last observation carried forward (LOCF). IGA is a static assessment of overall papulopustular rosacea severity. The endpoint defines success as an IGA score of clear or minimal. In the registry's scale description, clear means no papules or pustules and no erythema; minimal means rare papules or pustules and faint erythema that is below mild.

A global severity assessment complements lesion counts by giving a clinician-rated overall classification rather than measuring only the number of inflammatory lesions. It is therefore a categorical endpoint: each participant either meets the defined success criterion or does not. The reported percentage describes the proportion meeting that criterion in each group, not the average change in an individual participant's score.

General statistical context: a prespecified, clinically interpretable endpoint can focus a trial's principal comparison and reduce the temptation to select a favorable result from many outcomes. The registry identifies this measure as primary. Whether it was designated as primary in the original protocol, and the rationale for selecting it over other outcomes, are not reported in the registry record. LOCF is the stated approach to missing end-of-treatment observations; it replaces a missing value with the participant's last non-missing observation, which could be baseline. This makes the outcome available for the stated analysis population, but does not establish what the missing outcome would actually have been.

7. Results Posted in the Registry

• Azelaic Acid Foam, 15% (BAY39-6251): 32.1% (155/483) versus 23.4% (112/478) on control; risk difference 8.7 percentage points (95% CI 3.0 to 14.3), risk ratio 1.37 (1.11–1.69); unadjusted two-proportion z-test p = 0.003.

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 Inflammatory Lesion Count at End of Treatment (LOCF)

• 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:
  • Azelaic Acid Foam, 15% (BAY39-6251): mean -61.60 versus -50.80 on control; difference -10.80 (95% CI -15.47 to -6.13), standardized effect d = -0.29; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Azelaic Acid Foam, 15% (BAY39-6251) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Investigator's Global Assessment (IGA) Based Therapeutic Response at End of Treatment (LOCF)

• 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:
  • Azelaic Acid Foam, 15% (BAY39-6251): 66.3% (320/483) versus 54.4% (260/478) on control; risk difference 11.9 percentage points (95% CI 5.7 to 18.0), risk ratio 1.22 (1.10–1.35); 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 Azelaic Acid Foam, 15% (BAY39-6251) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Nominal Value of Inflammatory Lesion Count at End of Treatment (LOCF)

• 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:
  • Azelaic Acid Foam, 15% (BAY39-6251): mean 8.50 versus 10.80 on control; difference -2.30 (95% CI -3.59 to -1.01), standardized effect d = -0.23; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Azelaic Acid Foam, 15% (BAY39-6251) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists a broad set of secondary outcomes covering inflammatory lesion counts and changes, IGA-based response and scores, erythema, telangiectasia, and facial skin color. The detailed numerical comparisons available for interpretation include both binary outcomes and continuous summaries. Collectively, these outcomes examine related aspects of rosacea severity and appearance, but they are not repetitions of the primary endpoint: each uses a different measure, scale, or success definition.

The available comparisons show a generally favorable direction for the azelaic acid group across the posted lesion-count and IGA-response summaries. This broad pattern is compatible with the primary result, but it does not make the secondary outcomes equivalent to the primary measure or independently establish the primary conclusion. Their interpretation is best considered supportive and exploratory, particularly because multiple outcomes were examined.

Unadjusted secondary p-values do not account for the fact that numerous outcomes may be tested. General statistical context: when many hypotheses are tested, the chance of at least one apparently notable result can increase, even if none of the underlying effects is real. Methods to control multiplicity can address that issue, but whether a multiplicity procedure was planned or used is not reported in the registry record. The registry lists 16 secondary outcomes; detailed multiplicity handling is not reported.

The registry also does not provide enough information to determine whether all secondary measures were prespecified, whether there was a hierarchy among them, or whether the sponsor applied analysis adjustments not shown in the record. Consequently, the pattern across outcomes can add context, but isolated secondary findings should carry less weight than the designated primary outcome and the sponsor's reported primary analysis.

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

• Percent Change From Baseline in Inflammatory Lesion Count at End of Treatment (LOCF)
• Percentage of Participants With Investigator's Global Assessment (IGA) Based Therapeutic Response at End of Treatment (LOCF)
• Grouped Changes From Baseline in Erythema Intensity Score at End of Treatment (LOCF)
• Percentage of Participants With Investigator's Global Assessment (IGA) Scores at End of Treatment (LOCF)
• Nominal Value of Inflammatory Lesion Count at End of Treatment (LOCF)
• Percentage of Participants With Erythema Intensity Score at End of Treatment (LOCF)
• Grouped Changes From Baseline in Telangiectasia Intensity Score at End of Treatment (LOCF)
• Percentage of Participants With Facial Skin Color Rating at End of Treatment (LOCF)

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical context: the primary endpoint is binary at the participant level. A participant is counted as a success if the end-of-treatment IGA is clear or minimal; otherwise the participant is not counted as a success. The arm-level percentage is the proportion meeting that definition. Comparing two proportions is a direct way to describe how often the endpoint occurred in the randomized groups. The registry gives the outcome counts and percentages, and the recalculated comparison uses those posted summary data without adjustment.

What does a risk difference describe?

A risk difference is the success proportion in one group minus the success proportion in the comparator group. It is expressed on the probability scale, so its sign indicates which group has the larger observed proportion. The recalculated confidence interval for the primary risk difference lies above zero, which is consistent with a positive difference under that unadjusted calculation. No conversion to a number needed to treat or other derived measure is presented, because such a calculation would require an additional transformation and assumptions beyond the direct comparison.

The unadjusted p-value for the recalculated primary comparison is 0.003. This value comes from a simple comparison of the posted group results and is not the sponsor's reported analysis. It is useful as a transparent check of the contrast, but the registry's own analysis should be the main reference for the trial's inferential result. The registry reports a Cochran-Mantel-Haenszel analysis and p < .001. It does not report a corresponding treatment-effect estimate, confidence interval, stratification variables, or further details of the test in the posted analysis entry.

What does the Cochran-Mantel-Haenszel method do?

General statistical context: the Cochran-Mantel-Haenszel method can combine information across strata to assess an association or treatment contrast while accounting for the stratification structure. Its interpretation depends on how strata were defined and how the method was implemented. Although the registry names this method for the reported primary analysis, the record does not specify the strata or provide the other details needed to reproduce the analysis. It is therefore not possible to establish from the registry entry whether or how stratification affected the reported result.

How should the confidence interval be read?

General statistical context: a confidence interval presents a range of effect estimates that are compatible with the data under the method's assumptions. It conveys precision as well as direction; a narrower interval indicates less sampling uncertainty than a wider interval for the same type of estimate. The recalculated interval is for an unadjusted comparison. It should not be mistaken for a confidence interval from the sponsor's Cochran-Mantel-Haenszel analysis, because the latter interval is not reported in the registry record.

A confidence interval does not represent the range of outcomes for individual participants, and it does not mean that the true effect has a specified probability of lying in the particular interval after the data are observed. General statistical context: its usual repeated-sampling interpretation concerns the performance of the interval procedure across repeated studies under its assumptions. For this trial, the interval is subject to the limitations of the posted summary data and the specified LOCF outcome definition.

Why does over-dispersion matter for count outcomes?

General statistical context: count outcomes can vary more widely than a simple count model expects, a feature often called over-dispersion. If that extra variability is ignored, standard errors may be too small and confidence intervals too narrow. The registry includes inflammatory lesion counts and their changes among the secondary outcomes. The posted summary statistics do not establish whether a count model was used, whether over-dispersion was assessed, or what model-based adjustment, if any, was applied. The unadjusted calculations for continuous secondary summaries should therefore be understood as comparisons of posted means, rather than as a reconstruction of a more elaborate analysis.

The secondary continuous comparisons include mean differences and standard deviations, while binary secondary outcomes are expressed as percentages. Such measures answer different questions. A mean difference describes an average contrast on the outcome scale; a proportion comparison describes the frequency of an event or category. The registry posts 16 secondary outcomes, but only a subset of their detailed numerical results is represented in the comparison data available for interpretation. The analysis method for each secondary outcome is not reported in the registry record.

In general, randomization supports comparison of groups by assigned treatment, but it does not eliminate uncertainty or missing data. The primary population is described as randomized participants dispensed any study medication, and LOCF is specified for missing end-of-treatment values. Details about adherence, actual treatment received, additional analysis populations, sensitivity analyses, or model adjustments are not reported in the registry record. These omissions limit how completely an independent reader can reproduce the sponsor's analysis.

11. Confidence Intervals and Precision

The primary arm-level success percentages are 32.1% for azelaic acid foam and 23.4% for vehicle foam. The recalculated risk-difference confidence interval lies entirely above zero. This indicates that, under the unadjusted calculation, the data are compatible with a positive difference in the proportion meeting the success definition. The interval is not the sponsor's confidence interval: the registry does not report an effect estimate or interval for the Cochran-Mantel-Haenszel analysis.

A confidence interval is useful because a point estimate alone does not show how much sampling uncertainty surrounds the contrast. A relatively broad interval would leave more uncertainty about the magnitude; a narrower interval would indicate greater precision, given the method and assumptions. The recalculated interval's positive lower bound gives information about direction, while the distance between its bounds conveys uncertainty about the size of the difference. The interval does not describe individual outcomes or account automatically for uncertainty caused by missing data, outcome measurement, or analysis choices.

General statistical context: confidence intervals are conditional on the analysis model and the data used. Here, the re-calculation is unadjusted and uses the posted primary group results. The registry's analysis has a different named method and reports a p-value, but the absence of its treatment-effect estimate and confidence interval prevents a direct comparison of precision between the sponsor analysis and the simple re-calculation. The trial's own analysis therefore should not be reconstructed from the unadjusted interval.

The registry does not report a clinically important difference threshold for the primary endpoint. Statistical precision and clinical importance are distinct: an interval can indicate that an effect is estimated with some degree of precision without determining whether the effect is important in practice. Interpretation should also account for the LOCF rule, which means the endpoint result depends in part on the method used to handle missing end-of-treatment observations.

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 sample-size figures are planning illustrations based on the observed effect, not the original design calculations for this trial. For the binary primary endpoint, the figures are participants per arm. The underlying assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm under those assumptions for a design intended to have an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column uses a higher target chance of detection and therefore generally requires more participants. These are forward-looking planning quantities, not a measure of how much power the completed trial had.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The smaller the effect a future study is designed to detect, the more participants it needs under the same assumptions. For example, the displayed participant requirements rise as the target effect is reduced. This illustrates why sample-size planning depends not only on the chosen power and significance level but also on the effect size the study is intended to detect.

These illustrations do not reproduce the original trial design, and the observed effect may not be the effect a future study should target. They are not observed power.

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 = 0.234; treatment proportion p₁ = 0.321; average p̄ = 0.278.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6333 = 1.2413.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6303 = 0.5305.
4. n = (1.2413 + 0.5305)² / (0.0866)² = 418.6, rounded up to 419 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 <- 0.234309623430962                          # control proportion
p1 <- 0.320910973084886                          # 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(1555463)
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 = 419 (80% power), 560 (90% power)
 75% of observed effect: n per arm = 727 (80% power), 973 (90% power)
 50% of observed effect: n per arm = 1,594 (80% power), 2,133 (90% power)
power.prop.test: 418.6 
Simulated power at n = 419 per arm: 0.799 (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. Analyses Reported by the Sponsor

The sponsor's own primary analysis is reported as a Cochran-Mantel-Haenszel analysis with p < .001. The registry does not give the sponsor's effect estimate, confidence interval, test statistic, or analysis details beyond the method name and p-value. That reported analysis is the appropriate reference for what the trial's own analysis concluded statistically.

The separate recalculation is an unadjusted comparison based on the posted group outcome summaries. It gives an unadjusted p-value of 0.003 and a confidence interval for the risk difference that lies above zero. It is a transparent comparison of the reported group results, but it does not replicate the sponsor's method. The registry record does not report enough detail to determine exactly why the p-values differ or to reconstruct the Cochran-Mantel-Haenszel result.

The discrepancy flag is false, so there is no flagged conflict between the posted sponsor result and the recalculated result. The results nonetheless should not be collapsed into a single analysis: they use different methods and have different reporting detail. The sponsor's analysis takes precedence as the trial's own analysis, while the unadjusted recalculation is an additional descriptive check. Neither p-value by itself quantifies the size or practical importance of the contrast.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and lists 16 secondary outcomes. It does not report whether the sponsor adjusted for multiple comparisons, used a hierarchy or gatekeeping procedure, or treated secondary analyses as exploratory. Without that information, the degree to which the overall false-positive risk was controlled cannot be established from the registry record. General statistical context: testing many outcomes without adjustment can make nominal p-values less persuasive as confirmatory evidence, because a noteworthy result may arise by chance among a larger set of tests.

The primary endpoint uses last observation carried forward for missing end-of-treatment observations. The stated population includes all randomized participants who were dispensed any study medication. LOCF carries each participant's last non-missing observation forward, including baseline, when the end-of-treatment observation is missing. This is the rule recorded for the endpoint; the registry does not report the number of missing observations or how many outcomes were carried forward.

General statistical context: LOCF makes an analysis possible when follow-up data are missing, but it does not recover the unobserved outcome. It implicitly substitutes an earlier measurement for a later one and can misrepresent change if participants' outcomes would have changed after their last observation. Its effects depend on the pattern and reasons for missingness. The registry does not report sensitivity analyses comparing LOCF with other missing-data approaches, reasons for missing assessments, or assumptions about missingness.

The registry describes the primary analysis population, but additional details about analysis populations, protocol deviations, adherence, and exclusions are not reported in the registry record. The original protocol, detailed statistical analysis plan, and trial-specific sample-size rationale are also not reported. These gaps limit assessment of prespecification and robustness, rather than proving that the corresponding procedures were absent from the conduct of the trial.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: accidental death (0.2%), gastroenteritis viral (0.2%), bipolar disorder (0.2%), haemorrhage (0.2%), cardiac failure congestive (0.2%).

The registry reports serious adverse events affecting 3 of 483 participants in the azelaic acid foam group and 4 of 478 participants in the vehicle group. Other adverse events are reported for 148 participants in the azelaic acid group and 117 in the vehicle group. These are participant counts, not treatment-effect estimates, and the registry entry does not provide a comparative statistical analysis for these safety summaries.

The listed serious-event terms each appear with a reported value of 0.2%: accidental death, viral gastroenteritis, bipolar disorder, haemorrhage, congestive cardiac failure, and hepatotoxicity. The registry record does not give further event-level descriptions or attribute each listed term to a particular treatment group in this summary. Death counts for the two groups are not reported in the registry record.

General statistical context: serious adverse events are important to describe, but small counts can yield imprecise comparisons. These summaries alone do not establish whether an event was caused by treatment, nor do they establish a difference in risk between groups. The registry does not report exposure-adjusted event rates or detailed follow-up information for these safety data, so interpretation is limited to the posted counts and terms.

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

The primary result describes the proportion of participants in each randomized group who met a defined IGA success criterion at end of treatment. The posted percentages were higher in the azelaic acid foam group than in the vehicle foam group, and the recalculated unadjusted confidence interval for the risk difference lies above zero. The sponsor's own analysis reports p < .001 using the Cochran-Mantel-Haenszel method. These findings describe the posted trial results under the recorded analysis and outcome definition.

They do not show that every participant benefited, identify the outcome an individual would have had under another assignment, or establish what happens after the 12-week treatment period. The primary endpoint is a clinician-rated categorical assessment, and therapeutic success is specifically defined as clear or minimal. It is not a direct measure of every symptom, quality-of-life outcome, or longer-term course.

The trial compared azelaic acid foam with vehicle foam. The observed contrast therefore addresses the difference between those assigned groups in this trial, not a comparison with every other treatment or with no care. The registry's LOCF approach also matters: missing end-of-treatment observations were represented by the last non-missing observation, potentially baseline. The result should be understood in light of that rule and the fact that missing-data counts and sensitivity analyses are not reported.

Statistical evidence and clinical importance are separate considerations. The registry does not report a clinically important threshold for the primary endpoint, and the sponsor's analysis effect estimate and confidence interval are not reported. The posted data therefore support a description of the between-group statistical result, but do not by themselves establish how important the magnitude is in clinical practice. No treatment recommendation follows from these trial statistics alone.

18. Why This Trial Matters Statistically

This trial provides a clear example of how a binary clinical endpoint can be framed as a difference in the proportion meeting a defined success criterion. The IGA threshold is stated explicitly: scores of clear or minimal count as therapeutic success. That definition makes the primary outcome interpretable as a responder proportion rather than as a change in an average score, while also making clear that participants just on opposite sides of the threshold are classified differently.

The record also illustrates why the analysis method and the reported effect estimate both matter. The sponsor reports a Cochran-Mantel-Haenszel p-value, while a simple recalculation from posted group summaries gives an unadjusted comparison. These results are not interchangeable. The sponsor analysis is the trial's own reported analysis, and the simple recalculation offers a check based on less information. The absence of the sponsor's estimate and interval limits evaluation of the size and precision of its result.

Missing-data handling is another important part of interpreting an endpoint. LOCF is explicitly used, including baseline as a possible carried-forward observation. That choice affects what the analyzed outcome represents, yet the registry does not report the amount of missingness or sensitivity analyses. The record also lists numerous secondary outcomes, underscoring the need to distinguish a designated primary endpoint from a wider set of related analyses and to consider multiplicity.

Finally, the sample-size illustrations show the dependence of planning requirements on the target effect and power, but they are not the trial's original design rationale. The original assumptions are not reported in the registry record. Taken together, these features demonstrate how endpoint definition, analysis method, missing-data handling, multiplicity, and precision shape interpretation beyond a p-value alone.

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

The registry record does not report the protocol, detailed eligibility criteria, or the original sample-size justification. It also does not include the sponsor's primary effect estimate or confidence interval, so the sponsor's reported p-value cannot be paired with its own measure of magnitude and precision. The reported Cochran-Mantel-Haenszel method is not accompanied by the strata or implementation details needed for independent reproduction.

LOCF is specified for missing end-of-treatment observations, but the number and pattern of missing observations, reasons for missingness, and sensitivity analyses are not reported. The robustness of the primary result to alternative missing-data assumptions therefore cannot be assessed from the registry record. Details about adherence, treatment discontinuation, protocol deviations, and additional analysis populations are also not reported.

The registry lists many secondary outcomes, but does not report a multiplicity strategy, outcome hierarchy, or which analyses were considered confirmatory. The detailed analysis methods for the secondary outcomes are not reported. This limits the strength with which multiple secondary findings can be treated as confirmatory evidence.

The safety summaries give counts and selected serious-event terms but do not provide a comparative analysis, event-level narratives, or exposure-adjusted rates. Death counts are not reported in the registry record. The outcome timeframe is up to 12 weeks, so these results do not establish outcomes beyond the recorded treatment period. These are limitations of what the registry record makes available; they do not establish that procedures or data were absent from the full trial documentation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of Azelaic Acid Foam, 15 % in Papulopustular Rosacea — NCT01555463.
• Registry record last updated 2023-06-09; status last verified 2015-12.
• Results first posted 2015-01-27.
• 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

NCT01555463 is a completed Phase 3 randomized, double-blind, vehicle-controlled, multicenter, parallel-group trial sponsored by LEO Pharma. It enrolled 961 participants with papulopustular rosacea and compared azelaic acid foam, 15%, with vehicle foam, both applied twice daily for 12 weeks.

The primary endpoint was IGA-based therapeutic success at end of treatment, defined as a score of clear or minimal, with LOCF for missing observations. The posted success percentages were 32.1% for azelaic acid foam and 23.4% for vehicle foam. The sponsor reported a Cochran-Mantel-Haenszel analysis with p < .001; a separate unadjusted recalculation gives p = 0.003.

Secondary outcomes cover lesion counts, IGA, erythema, telangiectasia, and facial skin color. The registry also reports serious and other adverse-event counts. Several details needed to assess multiplicity, missing-data robustness, and the sponsor's effect estimate are not reported in the registry record.