Comparative Safety and Efficacy of Two Rosacea Products in the Treatment of Facial Erythema of Rosacea: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparative Safety and Efficacy of Two Rosacea Products in the Treatment of Facial Erythema of Rosacea (NCT02385240), a randomized phase 3 study. The primary outcome is Proportion of Subjects With Composite Success.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-masked, parallel-group trial sponsored by Padagis LLC. The registry lists Rosacea as the condition and an enrollment of 552. The study began in 2015-03, had primary completion in 2015-12, and is recorded as completed. The trial compared Brimonidine Topical Gel, 0.33 percent (Perrigo), with Brimonidine Topical Gel, 0.33 percent (Reference), and placebo gel.

Random assignment means treatment groups are formed through an allocation process intended to reduce systematic differences between groups. Double masking generally means that treatment assignment is concealed from two categories of people involved in the study, but which people were masked and how masking was maintained are not reported in the registry record. A parallel design means participants are assigned to a group and the groups are compared, rather than participants crossing between treatments; the registry does not report further details of the schedule or procedures.

The primary outcome is reported at Day 15, hour 6, for the per protocol population. The posted counts are 60 of 168 for the test product, 58 of 170 for the reference product, and 23 of 179 for placebo gel. Those outcome denominators are not the same as the reported overall enrollment, and the reasons for the difference are not reported in the registry record. Safety outcomes use separate group sizes at risk.

The registry does not report the original sample-size justification, allocation ratio, randomization method, or planned statistical analysis in the information. The study’s own design assumptions, including whether and when interim analyses were planned, are not reported in the registry record. Those details should not be inferred from the sample-size illustrations or from the analyses posted after the trial.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Per protocol population

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 Proportion of Subjects With Composite Success, measured over Day 15 at hour 6.

The primary endpoint is the proportion of participants achieving composite success at Day 15, hour 6, in the per protocol population. Success requires a 2-grade improvement on both the Clinician’s Erythema Assessment (CEA) and the Patient Self Assessment (PSA) scales. The outcome is reported as a count of participants meeting that combined criterion in each group.

A composite endpoint combines multiple measures into one success definition. Here, requiring improvement on both scales makes the endpoint reflect agreement between a clinician assessment and a participant assessment, rather than success on either scale alone. The endpoint does not show how much either scale changed among participants who did not meet the joint threshold, nor does it report each scale’s separate result. Those component results are not reported in the registry record.

Using a binary outcome makes the group comparison a comparison of the proportions meeting the specified criterion. The resulting counts are straightforward to interpret, but they do not describe the size or distribution of changes in erythema among all participants. The endpoint’s interpretation also depends on the specified 2-grade threshold and the per protocol population; other thresholds or analysis populations are not reported in the registry record.

7. Results Posted in the Registry

• Test Product: 35.7% (60/168) versus 34.1% (58/170) on control; risk difference 1.6 percentage points (95% CI -8.6 to 11.8), risk ratio 1.05 (0.78–1.40); unadjusted two-proportion z-test p = 0.758.
• Placebo Gel: 12.8% (23/179) versus 34.1% (58/170) on control; risk difference -21.3 percentage points (95% CI -29.9 to -12.6), risk ratio 0.38 (0.24–0.58); 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.

Proportion of Subjects With Composite Success

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Test Product: 36.3% (61/168) versus 34.1% (58/170) on control; risk difference 2.2 percentage points (95% CI -8.0 to 12.4), risk ratio 1.06 (0.80–1.42); unadjusted two-proportion z-test p = 0.673.
  • Placebo Gel: 10.6% (19/179) versus 34.1% (58/170) on control; risk difference -23.5 percentage points (95% CI -31.9 to -15.1), risk ratio 0.31 (0.19–0.50); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Product and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo Gel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcome is composite success at Day 15, hour 3, using the same stated two-scale improvement criterion. Across the secondary comparisons, the overall pattern resembles the primary results: the test and reference groups have close observed success counts, while the placebo group has fewer. The test-versus-reference recalculation is imprecise and its unadjusted p-value is not small; the placebo comparison’s recalculated interval lies below zero and its unadjusted p-value is reported as < 0.001. The detailed estimates are reported with the outcome results and are not repeated.

This pattern is consistent across the two assessment times in the limited sense that the direction of the observed comparisons is similar. It does not establish that the effects are identical at the two times, nor does it show how each assessment scale behaved separately. The registry lists the same composite-success outcome wording more than once among its secondary outcomes; the posted results identify the hour 3 assessment. Other secondary endpoint details are not reported in the registry record.

Secondary findings generally carry less inferential weight than a prespecified primary finding, particularly when many comparisons or outcomes are examined. Each additional analysis creates more opportunity for a chance finding. The registry does not report whether secondary comparisons were prespecified in a hierarchy, whether multiplicity adjustments were planned, or how the sponsor interpreted these results within such a plan. The reported secondary p-values are unadjusted, so they should be viewed as descriptive evidence rather than as independently conclusive tests.

The hour 3 result also does not replace the primary result at hour 6. They are distinct assessment times and are reported as separate outcomes. No formal comparison between times or analysis of the pattern over time is reported in the registry record.

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

• Proportion of Subjects With Composite Success
• Proportion of Subjects With Composite Success

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary: each participant either met the composite-success definition or did not. The counts are reported by group, and the recalculations compare groups using the risk difference. A risk difference is the difference between two group proportions. General interpretation: a value of zero corresponds to equal observed proportions, while a positive or negative value indicates the direction of the subtraction used for that comparison. For the primary active-product comparison, the reported recalculation is 0.016; for placebo relative to reference, it is -0.213.

What does a confidence interval describe?

General explanation: a confidence interval describes a range of values compatible with the data and the statistical method used, while reflecting sampling uncertainty. It is not a guarantee that the true value lies in the interval, and it does not describe the range of individual participant outcomes. For the primary test-versus-reference risk difference, the interval runs from -0.086 to 0.118. Because it includes zero and also covers values on either side, the posted summary is compatible with a range of differences, including little or no difference and effects in either direction. The placebo-versus-reference interval runs from -0.299 to -0.126, which lies below zero for that stated comparison.

Why are the other effect measures different?

The posted recalculations also include relative risk and odds ratio summaries. A relative risk compares proportions as a ratio; an odds ratio compares the odds of success between groups. These measures express the same binary outcome on different scales, so their numerical values are not directly interchangeable with a risk difference. For the primary test-versus-reference comparison, the posted relative risk is 1.047 with a confidence interval from 0.782 to 1.401, and the odds ratio is 1.073 with a confidence interval from 0.686 to 1.678. For placebo relative to reference, the relative risk is 0.377 with a confidence interval from 0.244 to 0.582, and the odds ratio is 0.285 with a confidence interval from 0.166 to 0.489. These are unadjusted re-calculations from posted summary statistics.

What does an unadjusted p-value tell the reader?

General explanation: a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The primary test-versus-reference recalculation has p = 0.758; the primary placebo comparison has p < 0.001. The secondary recalculations report p = 0.673 for test versus reference and p < 0.001 for placebo versus reference. The p-values are unadjusted, and the registry record does not report a multiplicity plan.

How does the sponsor analysis differ?

The registry reports a sponsor analysis of equivalence for the test and reference products using Wald’s method. The primary result is an equivalence ratio of 1.034 with a 90% confidence interval from -7.52 to 10.72. The hour 3 result is an equivalence ratio of 1.05 with a 90% confidence interval from -6.94 to 11.33. No p-values are reported for these equivalence analyses. Equivalence asks whether the data are sufficiently compatible with a difference contained within prespecified bounds. The bounds and the sponsor’s full analysis plan are not reported in the registry record, so the posted equivalence estimates cannot be independently assessed against those criteria from this information alone.

Why might over-dispersion matter in other outcomes?

General explanation: over-dispersion occurs when observed variability is greater than a model assumes. It can lead to uncertainty estimates that are too narrow if the model does not account for that extra variation. The primary and secondary endpoints in this trial are reported as binary participant counts, not as a rate or continuous measurement with a dispersion estimate. Dispersion is not reported for these outcomes; over-dispersion is therefore not a feature to infer from the posted counts.

These methods describe group-level summaries. They do not adjust for unreported baseline characteristics, missing outcomes, or other factors. Whether adjusted models were used in other sponsor analyses, how missing data were handled, and whether analyses followed a prospectively specified plan are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a group difference. The primary test-versus-reference recalculation has a risk difference of 0.016 and a confidence interval from -0.086 to 0.118. The interval is wide enough to include zero as well as differences in both directions. This means the posted summary does not locate the test-versus-reference difference precisely, even though it gives a point estimate.

The placebo comparison has a risk difference of -0.213 and a confidence interval from -0.299 to -0.126, using placebo relative to reference. This interval is also a measure of uncertainty, not a range of participant-level responses. Its location below zero indicates that the compatible values under this recalculation are in the direction of a lower success proportion for placebo than reference.

General explanation: interval width depends on the amount of information and on the variability inherent in the outcome. A binary outcome’s precision is influenced by the numbers of participants and successes in the groups. A confidence interval does not account for design or analysis limitations that are not included in the calculation. The registry does not report enough detail to assess every potential source of uncertainty, including missing-data handling and any covariate adjustment.

The sponsor-reported equivalence intervals use a different analysis and are reported at 90%, whereas the unadjusted recalculated intervals are not identified with that sponsor analysis. They should not be treated as the same estimand or method. The registry’s equivalence limits are not reported, preventing an assessment of whether the sponsor interval meets the prespecified equivalence criterion.

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 outcomes in this trial, not total events. They are illustrations calculated from the observed effect, not a record of the trial’s original design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and those assumptions were true. The 90% power column gives the corresponding illustration for a 90% chance. Power is a design property under specified assumptions, not a measure of whether an observed result is true or clinically important.

The rows use the full observed effect and smaller fractions of that effect. Smaller effects need more participants to detect under the same assumptions, so the illustrated sample sizes increase as the target effect becomes smaller. The active-product comparison has a small observed difference, and the planning illustrations for that comparison are correspondingly much larger than those for the placebo comparison. These figures should not be interpreted as recommended enrollment targets because they are based on observed effects and simplified assumptions.

This is not observed power. The figures are planning illustrations and do not change the interpretation of the trial’s confidence intervals or p-values. The registry record does not report the original sample-size justification, the effect size used to plan the actual study, or whether the trial’s original calculation used these 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.341; treatment proportion p₁ = 0.357; average p̄ = 0.349.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6742 = 1.3213.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6741 = 0.5673.
4. n = (1.3213 + 0.5673)² / (0.0160)² = 13,992.2, rounded up to 13,993 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 <- 0.341176470588235                          # control proportion
p1 <- 0.357142857142857                          # 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(2385240)
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 = 13,993 (80% power), 18,732 (90% power)
 75% of observed effect: n per arm = 24,810 (80% power), 33,213 (90% power)
 50% of observed effect: n per arm = 55,672 (80% power), 74,529 (90% power)
power.prop.test: 13992.2 
Simulated power at n = 13,993 per arm: 0.798 (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 registry reports the sponsor’s test-versus-reference analysis as an equivalence analysis using Wald’s method. For the primary endpoint, the reported equivalence ratio is 1.034, with a 90% confidence interval from -7.52 to 10.72. For the Day 15, hour 3 secondary outcome, the reported equivalence ratio is 1.05, with a 90% confidence interval from -6.94 to 11.33. The registry does not report p-values for these analyses.

The recalculation uses posted group counts to estimate an unadjusted risk difference. For the primary outcome, that estimate is 0.016, with a confidence interval from -0.086 to 0.118 and p = 0.758. It answers a different statistical question and uses a different effect scale from an equivalence ratio. It is useful as a transparent summary of the posted counts, but it does not replace the sponsor’s own analysis.

Equivalence is assessed against prespecified margins, and the registry record does not report those margins or the full sponsor analysis plan. Consequently, the sponsor result can be described as reported, but the information available does not permit a check of the equivalence criterion. The recalculated comparison should not be used to infer whether the sponsor’s formal criterion was met.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses are tested, because the chance of at least one apparently unusual result can increase as the number of tests grows. This study reports comparisons of the test product and placebo with the reference product, along with primary and secondary assessment times. The posted recalculated p-values are unadjusted. Whether the original plan specified a testing hierarchy, adjusted significance thresholds, or another multiplicity strategy is not reported in the registry record.

The primary endpoint population is identified as the per protocol population. The registry does not report the criteria used to define that population, the number of participants excluded from it, or the reasons for any exclusions. It also does not identify whether an intention-to-treat population or other analysis populations were used for the reported outcomes.

Missing-data handling is not reported in the registry record. The posted denominators differ by outcome group and are distinct from overall enrollment, but the reasons for these denominators and whether missing outcomes occurred cannot be established from the counts alone. The record does not describe imputation, a missing-equals-failure rule, sensitivity analyses, or other approaches to missing observations.

These omissions matter because the analysis population, outcome availability, and multiplicity approach can affect how estimates and p-values should be interpreted. The registry record also does not report the complete prespecified statistical analysis plan, interim analyses, or rules for stopping analyses. No assumptions about these procedures should be inferred from the posted results.

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

Serious events with the highest arm-level rate: diabetic ketoacidosis (0.5%).

Safety counts are reported for groups at risk of 183 in the test-product group, 184 in the reference-product group, and 185 in the placebo group. One serious adverse event is recorded in the test-product group, and none in the reference or placebo groups. The registry lists Diabetic Ketoacidosis at 0.5% among the serious-event terms. The record reports no deaths in any group.

No other adverse events are recorded in the posted counts for the three groups. These figures are counts from the safety summary, not estimates of comparative risk adjusted for exposure or other factors. The group sizes at risk are not the same as the primary endpoint denominators, and the registry does not report further details about event timing, duration, severity beyond serious-event status, relatedness, or participant-level exposure.

Rare-event counts can provide limited information about comparative safety, especially when the numbers are small. The posted record does not establish whether an event was caused by a product. The counts should therefore be read as reported events during the study, not as proof for or against a causal relationship.

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

The primary outcome records whether participants met a specific combined threshold: a 2-grade improvement on both the clinician and patient assessment scales at Day 15, hour 6. The observed counts were close for the test and reference products, and the unadjusted recalculation has a confidence interval that includes zero. The posted summary therefore leaves uncertainty about the size and direction of the difference between those groups on this endpoint.

The placebo comparison shows fewer posted composite successes in the placebo group than in the reference group, with an unadjusted recalculated risk-difference interval below zero. This describes the observed trial data for the registered outcome and assessment time. It does not by itself establish how results would generalize to other populations, assessment schedules, or definitions of success.

The sponsor’s equivalence analysis is distinct from the unadjusted risk-difference calculation. Because the equivalence margins and full analysis plan are not reported in the registry record, the reported ratio and interval cannot be checked against the formal criterion from the available information. Statistical significance in an unadjusted comparison is not the same as equivalence, and a lack of a small p-value is not proof that groups are identical.

These results do not describe change on each assessment scale separately, the distribution of responses among participants who did not meet the composite threshold, or outcomes beyond those posted. Missing-data procedures, multiplicity handling, and details of the per protocol population are also not reported. Accordingly, the findings are best understood as group-level summaries with the precision and limitations stated, rather than as a complete account of every aspect of treatment effect or safety.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of estimand matters. A risk difference expresses the absolute separation in composite-success proportions, while a relative risk, odds ratio, and equivalence ratio use different scales and answer different questions. The unadjusted risk-difference recalculation and sponsor-reported equivalence analysis can therefore coexist without being interchangeable.

It also illustrates how precision qualifies a point estimate. The active-product primary estimate is close to zero, but its confidence interval covers values on either side. Reading only the point estimate or a p-value would obscure that uncertainty. For the placebo comparison, the interval’s position conveys the direction and range of the unadjusted estimate, while still leaving sampling uncertainty.

The primary outcome combines clinician and participant assessments, requiring both to meet a threshold. That makes the endpoint’s interpretation specific: it concerns joint threshold success, not every kind of improvement or the separate behavior of the two scales. The assessment time and per protocol population further define what the result represents.

Finally, the record shows why statistical interpretation depends on reporting beyond headline estimates. The original planning assumptions, equivalence margins, multiplicity strategy, missing-data handling, and definitions of analysis populations are not reported. Without those details, readers can describe the posted counts and recalculations, but should not infer the complete prespecified analysis or claim that an equivalence criterion was met.

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.

The registry information available for this analysis does not report participant characteristics, detailed eligibility criteria, baseline balance, or reasons for exclusion from the per protocol population. These omissions limit assessment of who contributed to the primary result and how representative the analysis population was of all enrolled participants.

The primary and secondary results are counts for a composite endpoint, without the separate CEA and PSA results. The posted data therefore do not show which component drove success or non-success, nor how much participants changed when they did not cross the 2-grade threshold. The record also does not report outcomes beyond the stated Day 15 assessment times.

Important analysis details are not reported: the original sample-size justification, equivalence margins, multiplicity strategy, handling of missing data, interim analysis plans, and complete statistical analysis plan. The sponsor-reported equivalence intervals cannot be evaluated against formal margins from the information available. Recalculated estimates are unadjusted summaries from posted group counts and do not account for unreported design or analysis features.

The safety summary contains few serious events and does not include further detail about timing, duration, relatedness, or exposure. These counts are descriptive and cannot establish causation. The registry record also does not report additional safety analyses needed to assess patterns beyond the posted counts.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparative Safety and Efficacy of Two Rosacea Products in the Treatment of Facial Erythema of Rosacea — NCT02385240.
• Registry record last updated 2021-10-22; status last verified 2021-10.
• Results first posted 2020-12-14.
• 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 records a completed phase 3 randomized, double-masked, parallel trial sponsored by Padagis LLC, with enrollment of 552 and a study period from 2015-03 to primary completion in 2015-12. The groups received Perrigo brimonidine topical gel, reference brimonidine topical gel, or placebo gel.

The primary endpoint was composite success at Day 15, hour 6, in the per protocol population, defined as a 2-grade improvement on both the CEA and PSA scales. The posted active-product counts were close; the unadjusted recalculation was imprecise. The placebo comparison showed fewer posted successes than reference in the recalculation. The registry also reports sponsor equivalence analyses, but the equivalence margins are not reported.

Secondary results at Day 15, hour 3 follow a similar broad pattern. Safety reporting records one serious adverse event in the test-product group, none in the other groups, and no deaths. Details of missing-data handling, multiplicity, and the original statistical design assumptions are not reported in the registry record.