Phase 3 Papulopustular Rosacea Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 3 Papulopustular Rosacea Study (NCT01493687), a randomized phase 3 study. The primary outcome is Success Rate.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, triple-masked, phase 3 study. Its official title identifies a 12-week vehicle-controlled phase followed by a 40-week investigator-blinded extension. In the initial phase, the comparison was CD5024 1% cream versus CD5024 Vehicle Cream. The extension compared CD5024 1% cream with azelaic acid 15% gel for long-term safety. The registry record lists Galderma R&D as the sponsor and the study status as completed.

Total enrollment was 683. The primary Week 12 outcome is reported for an ITT-LOCF population, with 451 participants in the CD5024 1% Cream group and 232 in the vehicle group. The record’s study summary describes once-daily bedtime application during the 12-week period. It does not provide enough detail to explain how the stated triple masking was implemented or which individuals were masked in each phase.

The distinction between the initial efficacy comparison and the extension matters when interpreting results. The primary endpoint is a Week 12 response compared with vehicle; it is not a result from the full extension period. The extension is described as a long-term safety comparison involving azelaic acid, but the record does not give a primary endpoint or detailed analysis plan for that phase. Original sample-size assumptions, the rationale for the selected enrollment, and any interim-analysis plan 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.

Part A Vehicle Control (12 Weeks)

Reasons for not completing this period:

Part B Long Term Active Control 40 Weeks

Reasons for not completing this period:

Part C Safety Follow up (4 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: LOCF, ITT

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: ITT population

6. Primary Endpoint

The registry lists the primary outcome as Success Rate, measured over Week 12.

The primary endpoint is the percentage of participants who achieved an Investigator Global Assessment (IGA) score of Clear or Almost Clear at Week 12. The IGA is a five-point scale: Clear is score 0, Almost Clear is score 1, Mild is score 2, Moderate is score 3, and Severe is score 4. The record describes the scale in terms of inflammatory lesions and erythema. For example, Clear corresponds to no inflammatory lesions and no erythema, while Almost Clear allows very few small papules or pustules and very mild erythema.

The endpoint turns this ordered clinical assessment into a binary success outcome: scores 0 or 1 count as success, while scores 2, 3, or 4 do not. A binary responder outcome is useful for communicating the proportion reaching a defined state, rather than only describing average change across all participants. It also makes the treatment groups’ success rates directly comparable. That simplification has a trade-off: it does not distinguish between the two success categories, nor does it show how participants who are not classified as successes are distributed across the remaining IGA scores.

The registry specifies Week 12 and an ITT-LOCF population for this endpoint. Further detail about missing observations and the handling of individual assessment records is not reported in the registry record.

7. Results Posted in the Registry

• CD5024 1% Cream: 38.4% (173/451) versus 11.6% (27/232) on control; risk difference 26.7 percentage points (95% CI 20.6 to 32.8), risk ratio 3.30 (2.27–4.79); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percent Change in Inflammatory Lesion Count From Baseline to Week 12 (ITT-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:
  • CD5024 1% Cream: mean -64.90 versus -41.60 on control; difference -23.30 (95% CI -29.51 to -17.09), standardized effect d = -0.59; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for CD5024 1% Cream than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary outcome: percentage change in inflammatory lesion count from baseline to Week 12. The posted group means indicate decreases in both groups, with a larger decrease in the CD5024 group. The recalculated comparison and sponsor-reported p-value are consistent with a difference between group summaries. This broadly aligns with the primary result, which compares the proportions reaching the defined IGA success threshold.

The outcomes are related but not redundant. The IGA endpoint classifies participants according to a prespecified category threshold, whereas the lesion-count endpoint summarizes change in counts as a group mean. A participant’s lesion-count change and IGA category need not correspond exactly, and the record does not report individual-level relationships between these outcomes. The secondary result therefore provides supporting context rather than a direct replication of the primary endpoint.

Secondary findings generally carry less confirmatory weight when a trial evaluates multiple outcomes, because repeated testing can increase the chance of at least one apparently strong result arising by chance. In general, statistical plans may control this through a prespecified testing hierarchy or multiplicity adjustment. Whether either approach was used is not reported in the registry record. The record also does not describe a confirmatory status for this secondary outcome, so its p-value should not be interpreted as though an adjustment were known to have been applied.

The registry indicates three outcome measures and three analyses overall, while only one secondary outcome is posted in the record. Additional outcome details and the relationship among all analyses are not reported in the registry record. The secondary evidence is thus best treated as a complementary description of the Week 12 findings, with less weight than a clearly prespecified, multiplicity-controlled confirmatory analysis.

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

• Percent Change in Inflammatory Lesion Count From Baseline to Week 12 (ITT-LOCF)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as a Week 12 IGA success or not, using the record’s threshold of Clear or Almost Clear. For a binary outcome, the success rate is the proportion in a group who meet the definition. Comparing those proportions keeps the clinical definition visible and avoids treating the distance between the IGA categories as though it were necessarily equal. The endpoint does, however, compress a five-category assessment into two groups, so the success rates do not describe all shifts across the original scale.

How the risk difference reads

The unadjusted recalculation expresses the comparison as a risk difference. It subtracts the vehicle success proportion from the CD5024 success proportion, with a positive estimate indicating a higher observed success proportion in the CD5024 group. The reported estimate is 0.267, and its interval runs from 0.206 to 0.328. These are proportions on the risk-difference scale, not a ratio of probabilities. A difference is often straightforward to interpret because it describes the separation between group rates in the same units as the outcome.

Other relative measures can also describe binary outcomes, but they answer a different question. A risk ratio compares the group probabilities as a ratio, while an odds ratio compares odds. Relative measures may look more or less pronounced depending on the outcome frequency and scale. The primary interpretation gives priority to the posted group rates and the recalculated risk difference rather than substituting a relative measure for the observed percentages.

What a confidence interval communicates

A confidence interval gives a range of effect estimates compatible with the observed data under the method used and its assumptions. It helps readers assess precision: a narrower interval indicates less statistical uncertainty on that scale than a wider interval. It is not a range containing individual participant outcomes, and it is not a guarantee that a future trial’s estimate will fall within it. The interval also does not address biases or differences in study conduct that are not represented by the calculation.

The registry record lists a sponsor analysis using the Cochran-Mantel-Haenszel method and reports p < 0.001. In general, this method compares categorical outcomes across strata, combining information while accounting for stratification. The strata and implementation details for the sponsor’s analysis are not reported in the registry record. The unadjusted recalculation is a separate, simple comparison from posted summary statistics; it should not be mistaken for a reconstruction of the sponsor’s full analysis.

Interpreting the lesion-count outcome

The secondary outcome is continuous: it reports percentage change in inflammatory lesion count from baseline to Week 12, with a mean and standard deviation for each group. The recalculated mean difference is -23.3, with an interval from -29.51 to -17.09. A mean difference compares group averages. It does not imply that every participant experienced a change near the group mean, which is why the standard deviations are also relevant descriptions of variation among participants.

In general, standard deviation describes the spread of individual observations around a group mean. It is not the same as the standard error, which describes uncertainty in an estimated mean. A treatment-group average can be estimated more precisely when there is more information and less variability, but averages alone do not describe the full distribution of participant outcomes. The registry’s posted standard deviations are 39.91 for CD5024 and 38.83 for vehicle.

The registry also lists a Cochran-Mantel-Haenszel result for this secondary endpoint with p < 0.001, but no corresponding sponsor estimate or interval. Because the endpoint is continuous and the record does not explain how the reported method relates to its analysis, its exact implementation is not reported in the registry record. The recalculated continuous comparison is an unadjusted mean-difference analysis and should be understood separately.

Over-dispersion and model choice

In general, over-dispersion occurs when observed variation is greater than a statistical model expects. It can make standard errors too small and confidence intervals too narrow if the model does not account for the extra variation. This is a general issue in statistical modelling, not a finding established by the posted summaries. The registry record does not report a model-based assessment of over-dispersion for these outcomes.

Likewise, the posted summary statistics do not identify all assumptions behind the sponsor’s analysis, such as the handling of strata, covariates, or missing observations. The record states ITT-LOCF for the primary endpoint and the secondary lesion-count outcome, but detailed implementation and sensitivity analyses are not reported in the registry record. The recalculations are consequently best read as transparent, unadjusted summaries rather than as replacements for a fully specified trial analysis.

11. Confidence Intervals and Precision

For the primary binary outcome, the recalculated risk difference is 0.267, with an interval from 0.206 to 0.328. This interval describes uncertainty about the difference between the observed success proportions on the risk-difference scale. Its endpoints are both above zero, which is consistent with the direction of the reported group rates. The interval does not account for every possible source of uncertainty, including limitations in outcome measurement, missing-data handling, or generalizability.

The observed group proportions are 38.4% for CD5024 1% cream and 11.6% for vehicle. The confidence interval is for the difference, not an interval for either group’s rate. The interval’s width gives a sense of the statistical precision of the difference estimate, but precision should not be confused with clinical importance. Whether a particular difference is meaningful depends on context not established by the statistical interval alone.

For the secondary lesion-count outcome, the recalculated mean difference is -23.3, with an interval from -29.51 to -17.09. That interval describes uncertainty on the mean-change scale and is separate from the primary risk-difference interval. The secondary outcome’s standard deviations, 39.91 and 38.83, describe participant-level spread and should not be read as confidence limits for the group means.

The record does not state the confidence level for the recalculated intervals in the posted results. Neither interval resolves uncertainty about the study’s missing-data assumptions, analysis choices, or applicability beyond the trial population. The sponsor reports p < 0.001 for both comparisons, but p-values alone do not indicate precision or quantify the range of plausible effect sizes.

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 for the binary primary outcome and for the continuous lesion-count outcome; they are not total event counts. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The registry record does not report the assumptions used for the trial’s original design or its original sample-size justification.

The 80% power column gives the number of participants per arm in the planning illustration for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding number for a 90% chance. These are planning calculations, not guarantees about a future study’s result. The values are derived from the observed effect in this trial, rather than from an independently established target effect.

Rows using a smaller fraction of the observed effect require more participants per arm than rows based on the full observed effect. That is a general feature of study planning: smaller differences are harder to distinguish from random variation when other assumptions stay fixed. The estimates are illustrations and should not be treated as the trial’s intended enrollment target or as proof that the study had a particular probability of success.

This is not observed power. Observed power is not a useful substitute for interpreting the effect estimate and its uncertainty after results are available. The planning figures answer a hypothetical design question under explicit assumptions; the trial’s actual results are described by the posted group outcomes, effect estimates, and intervals.

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 = 0.116; treatment proportion p₁ = 0.384; average p̄ = 0.250.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6124 = 1.2002.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5825 = 0.4902.
4. n = (1.2002 + 0.4902)² / (0.2672)² = 40.0, rounded up to 41 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 <- 0.116379310344828                          # control proportion
p1 <- 0.383592017738359                          # 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(1493687)
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 = 41 (80% power), 54 (90% power)
 75% of observed effect: n per arm = 66 (80% power), 87 (90% power)
 50% of observed effect: n per arm = 131 (80% power), 175 (90% power)
power.prop.test: 40 
Simulated power at n = 41 per arm: 0.830 (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

For the primary outcome, the registry reports a sponsor analysis using the Cochran-Mantel-Haenszel method and gives p < 0.001. The unadjusted recalculation from the posted group counts also gives p < 0.001 and estimates a risk difference of 0.267, with an interval from 0.206 to 0.328. The sponsor’s analysis and the simple recalculation therefore agree in the reported direction and in the reported threshold for the p-value.

The methods are not identical descriptions of an analysis. Cochran-Mantel-Haenszel is the sponsor-reported method, while the recalculation is an unadjusted comparison from summary statistics. Details of the sponsor’s strata and other implementation choices are not reported in the registry record. The sponsor’s own analysis takes precedence as the trial’s reported analysis; the recalculation is supplementary and helps express the result in an interpretable effect scale.

For the secondary lesion-count endpoint, the registry also reports p < 0.001 from a Cochran-Mantel-Haenszel analysis, without posting a sponsor estimate or interval. The separate unadjusted recalculation reports a mean difference of -23.3, with an interval from -29.51 to -17.09. The registry record does not explain the relationship between the sponsor’s listed method and this continuous outcome, so the two analyses should not be conflated.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses are tested in the same study. Even when each test uses a conventional significance threshold, repeated testing can increase the overall chance of a false-positive finding. Common approaches include adjusting thresholds, controlling an overall error rate, or specifying an ordered testing strategy. These are general statistical options; the registry record does not report whether multiplicity was addressed, which outcomes were included in any adjustment, or whether the primary and secondary outcomes followed a formal hierarchy.

The record identifies the primary endpoint and one posted secondary endpoint, but also reports three outcome measures and three analyses overall. The complete set of analyses and their prespecified status are not described in enough detail to establish how many hypotheses were tested or how the reported results should be ordered inferentially. The p-values should therefore be read as reported, without assuming a multiplicity adjustment.

The primary population is described as ITT-LOCF. In general, intention-to-treat analysis seeks to retain participants in their randomized groups, while last observation carried forward fills a missing endpoint using an earlier recorded observation. LOCF relies on assumptions about what would have happened after the last recorded assessment; those assumptions may not fit every participant’s course. The registry record does not state how many observations were missing, why they were missing, when the carried-forward values were taken, or whether other missing-data methods were used in sensitivity analyses.

Missing-data methods can affect both estimated group rates and their uncertainty. An analysis population label alone does not show whether missingness was balanced between groups or whether the results would be robust to alternative assumptions. The record’s use of ITT-LOCF is important context, but detailed participant flow, missingness patterns, sensitivity analyses, and the full statistical plan are not reported in the registry record. Interim analyses and stopping rules are also not reported in the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: atrial fibrillation (1.0%), transient ischaemic attack (1.0%), renal failure acute (1.0%), pancreatic carcinoma (0.6%), ascites (0.6%).

The registry separates adverse-event summaries into Part A, Part B, Part C, and overall groups. For the overall summaries, serious adverse events were reported for 10 of 452 participants in the CD5024 1% Cream group and 9 of 232 in the CD5024 Vehicle Cream/Azelaic Acid 15% Gel group. Other adverse events were reported for 110 of 452 and 52 of 232 participants, respectively. These are counts and group denominators as posted, not adjusted comparisons.

The combined vehicle/azelaic-acid label and the different part labels matter: the overall safety groups are not simply the same comparison as the randomized vehicle-controlled primary efficacy phase. The registry record does not provide enough detail in these summaries to align each participant’s exposure duration or treatment sequence. Event counts should not be summed across parts, since the record does not establish that the groups are independent or that the same participant could not contribute to more than one part.

Deaths are not reported in the registry record. Serious adverse-event counts summarize events meeting the registry’s serious-event category; they do not by themselves establish whether an event was caused by treatment. The listed serious-event terms are descriptive and do not establish causality.

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

The results describe a Week 12 comparison in a randomized, vehicle-controlled study of participants with papulopustular rosacea. The posted IGA success proportion was higher in the CD5024 1% Cream group than in the vehicle group, and the unadjusted risk-difference interval is consistent with a positive difference in this trial. The sponsor-reported primary analysis gives p < 0.001. The lesion-count outcome also shows a larger mean decrease in the CD5024 group, with a recalculated mean difference whose interval does not include zero.

These findings do not, by themselves, establish the size or importance of an effect in every patient or setting. The primary endpoint reduces the five-point IGA scale to a binary success classification, so it does not describe the full range of scores or the distribution of responses. The mean lesion-count result likewise does not show how much individual participants varied. Statistical evidence for a group difference is not the same as a judgment about clinical importance.

The registry record does not report the full statistical analysis plan, multiplicity procedures, detailed missing-data patterns, or sensitivity analyses. Those omissions limit assessment of how robust the reported results are to analysis choices. The trial’s extension is described as a long-term safety comparison with azelaic acid 15% gel, but the primary Week 12 efficacy result is not an extension-period efficacy comparison.

The adverse-event summaries are descriptive counts. They do not establish that a treatment caused or prevented an event, and differing treatment phases and group labels complicate direct comparisons. These statistics are not individualized predictions and do not replace a broader assessment of benefits and risks. They should be interpreted as the posted findings for the populations, outcomes, and timeframes recorded, with the reporting limitations kept in view.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation benefits from separating an endpoint’s clinical definition from the statistical scale used to compare groups. The primary endpoint is an IGA responder threshold, while the reported effect can be expressed as a risk difference. That difference directly describes how far apart the observed group success proportions are, and an interval adds information about uncertainty that a p-value alone cannot provide.

The record also shows how sponsor analyses and transparent recalculations can serve different purposes. The sponsor reports a Cochran-Mantel-Haenszel p-value, while an unadjusted calculation from posted counts provides an interpretable risk-difference estimate and interval. Agreement in the direction and reported p-value threshold is useful context, but it does not make the methods interchangeable. The sponsor analysis remains the trial’s reported analysis; the simple recalculation is a supplementary summary.

A further statistical lesson is that outcomes can be related without measuring the same thing. The IGA success rate and mean lesion-count change point in a similar broad direction, yet one captures a threshold-based classification and the other an average change. Their interpretation depends on their definitions, analysis populations, uncertainty, and place in the testing plan. The registry record does not report enough about multiplicity or missing-data sensitivity to treat every result as equally confirmatory.

Finally, planning illustrations based on an observed effect are not evidence of the study’s original design assumptions or its probability of success. Distinguishing hypothetical sample-size planning from observed results prevents a common interpretive error. Together, these considerations support a reading that attends to effect magnitude, precision, outcome definition, and reporting gaps rather than relying on statistical significance 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.

Several limitations are specific to the available record. The primary endpoint is reported for an ITT-LOCF population, but the record does not give missing-observation counts, reasons for missingness, or sensitivity analyses using alternative assumptions. The impact of carrying forward earlier measurements therefore cannot be assessed from the posted summaries.

The registry identifies a sponsor-reported Cochran-Mantel-Haenszel analysis but does not describe its strata or implementation. For the secondary continuous outcome, it lists the same method without an associated sponsor estimate or interval, leaving the relationship between that analysis and the outcome’s scale unclear. The unadjusted recalculations do not resolve those reporting gaps.

The record does not report whether results were adjusted for multiplicity, the full prespecified outcome hierarchy, interim analyses, or original sample-size assumptions. These omissions limit assessment of confirmatory status and of whether the reported tests reflect the planned analysis. The trial’s enrollment and posted analysis denominators are known, but participant flow and reasons for any difference between them are not reported in the registry record.

The long-term extension is described as an investigator-blinded safety comparison with azelaic acid 15% gel, yet detailed exposure durations, treatment sequences, and extension analyses are not included in the posted summaries. Safety groups carry different part labels, including a combined vehicle/azelaic-acid group, which limits simple comparisons across phases. The record also does not report death counts. These constraints mean that the Week 12 efficacy statistics and the safety summaries should be interpreted as distinct, limited views of the study rather than a complete account of all trial analyses.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase 3 Papulopustular Rosacea Study — NCT01493687.
• Registry record last updated 2021-02-18; status last verified 2015-01.
• Results first posted 2015-01-16.
• 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

The registry record describes a completed randomized, parallel-group, triple-masked phase 3 study in papulopustular rosacea, sponsored by Galderma R&D. It reports total enrollment of 683 and a 12-week comparison of CD5024 1% cream with CD5024 Vehicle Cream, followed by a 40-week investigator-blinded extension comparing CD5024 1% cream with azelaic acid 15% gel for long-term safety.

The primary Week 12 endpoint was the percentage achieving an IGA score of Clear or Almost Clear in the ITT-LOCF population. Posted rates were 38.4% and 11.6%, respectively; the unadjusted recalculation reports a risk difference of 0.267, with an interval from 0.206 to 0.328. The sponsor reports p < 0.001. One secondary outcome, percentage change in inflammatory lesion count, is also posted. Details of multiplicity, missing-data sensitivity analyses, and the full statistical plan are not reported in the registry record.