A Study to Evaluate Safety and Equivalence of Generic Azelaic Acid Foam and Finacea® Foam in Participants With Rosacea: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate Safety and Equivalence of Generic Azelaic Acid Foam and Finacea® Foam in Participants With Rosacea (NCT03287791), a randomized phase 3 study. The primary outcome is Percent Change From Baseline in the Inflammatory Lesions (Papules and Pustules) Counts at Week 12.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, vehicle-controlled Phase 3 study sponsored by Actavis Inc. The registry lists the study as completed and records enrollment of 924. The recorded study start was 2016-07-19, and the primary completion date was 2017-06-22. Its official title describes a multicenter, double-blind study; the registry’s masking field says quadruple. These descriptions are not identical, and the registry record does not explain the difference. The allocation field identifies the study as randomized.

Participants were assigned to generic azelaic acid foam, 15%, Finacea® (azelaic acid) foam, 15%, or vehicle foam. The arm descriptions specify twice-daily facial application for 12 weeks. The primary endpoint uses the PP Population, not the full enrollment figure. The reported endpoint arm sizes are 262.0 for generic foam, 259.0 for Finacea foam, and 245.0 for vehicle. The registry record does not give a complete account of participant flow or explain the difference between enrollment and these endpoint analysis sizes.

The registry states that the study aimed to compare the safety and efficacy profiles of the active foams, demonstrate therapeutic equivalence and safety between them, and demonstrate superiority of the reference and test products over vehicle. These are distinct questions: equivalence concerns whether the active treatments differ by no more than a prespecified acceptable margin, whereas superiority concerns whether an active treatment performs better than a comparator under a specified analysis. The equivalence margin and the original design assumptions are not reported in the registry record. Therefore, the study objective alone cannot establish which decision criteria were used.

Other listed interventions include cleanser, sunscreen, towel, and moisturizing lotion. Their specific allocation and role are not reported in the registry record. The primary analysis description says that participants who discontinued between 8 and 12 weeks because of lack of treatment had their lesion counts imputed using last observation carried forward. Participants missing the Week 12 assessment for another reason were excluded from this endpoint analysis. That handling is relevant when interpreting the PP results because the analyzed group and endpoint values depend on the stated population and missing-data rules.

4. Participant Flow and Accounting

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

Before assignment: If participant failed to return diary card and had no evidence of study drug use, then •participant was included in Safety population if there was some participant safety or efficacy data after Baseline •participant considered lost to follow up and excluded from Safety Population if there was no participant safety or efficacy data after Baseline

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants in the PP Population. If participant discontinued between 8 and 12 weeks of treatment due to lack of treatment, last observation carried forward (LOCF) was used to impute the number of lesions. If participant was missing Week 12 assessment for any other reason, participant was excluded.

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: Randomized participants with evidence in diary card of using ≥1 dose of study drug (Safety Population).

6. Primary Endpoint

The registry lists the primary outcome as Percent Change From Baseline in the Inflammatory Lesions (Papules and Pustules) Counts at Week 12, measured over Baseline, 12 weeks.

The primary endpoint measures percent change from baseline in facial inflammatory lesion counts at Week 12. The registry describes counting papules and pustules across the face above the jaw line to the hairline, including lesions on the nose. A papule with a pustule on its apex was counted as a pustule. Nodules and cysts were recorded separately and excluded from the inflammatory count. The endpoint is a continuous measure, summarized as a mean with a standard deviation.

Change from baseline expresses how the lesion count at follow-up relates to the participant’s starting count. A negative mean percent change indicates a reduction from baseline on the scale used for the endpoint. Comparing the arm means describes the average changes observed in the analyzed groups; it does not show how every individual participant changed, nor does a group mean describe the range of individual responses.

Lesion counts are used because they provide a defined clinical measure of inflammatory lesions, while the percentage-change scale relates follow-up counts to baseline. The registry’s population rule is also part of the endpoint definition: it uses the PP Population, applies last observation carried forward for a specified discontinuation circumstance, and excludes participants missing Week 12 for other reasons. These choices shape which observations contribute to the reported endpoint.

The registry also lists treatment success based on IGE score as a secondary outcome. That is a separate, binary outcome rather than another measure of mean lesion-count change. It should therefore be interpreted as complementary information, not as an interchangeable version of the primary endpoint.

7. Results Posted in the Registry

• Generic Azelaic Acid Foam: mean -64.28 versus -57.84 on control; difference -6.44 (95% CI -11.33 to -1.55), standardized effect d = -0.23; z-test p = 0.010.
• Finacea (Azelaic Acid) Foam: mean -65.15 versus -57.84 on control; difference -7.31 (95% CI -12.32 to -2.30), standardized effect d = -0.26; z-test p = 0.004.

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.

Percentage of Participants With Treatment Success Based on IGE Score

• 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:
  • Generic Azelaic Acid Foam: 39.7% (104/262) versus 33.5% (82/245) on control; risk difference 6.2 percentage points (95% CI -2.1 to 14.6), risk ratio 1.19 (0.94–1.49); unadjusted two-proportion z-test p = 0.146.
  • Finacea (Azelaic Acid) Foam: 48.3% (125/259) versus 33.5% (82/245) on control; risk difference 14.8 percentage points (95% CI 6.3 to 23.3), risk ratio 1.44 (1.16–1.79); 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 Generic Azelaic Acid Foam 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 higher for Finacea (Azelaic Acid) Foam than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcome concerns treatment success based on IGE score. The overall pattern is that the recorded success percentage is higher in each active-treatment arm than in the vehicle arm, with a more pronounced separation for Finacea than for generic foam. The unadjusted interval for the generic comparison includes no difference, while the interval for Finacea does not. This gives a less consistent pattern across the two active-versus-vehicle comparisons than the sponsor-reported primary superiority results.

This binary outcome complements the primary continuous outcome but measures something different. The primary endpoint summarizes percent change in inflammatory lesion counts; the secondary endpoint classifies treatment success based on IGE score. Agreement in broad direction does not make the outcomes equivalent or establish that they measure the same clinical construct. Differences between them can arise because they use different definitions and scales.

The secondary analyses are unadjusted. When multiple outcomes or comparisons are examined, the chance of at least one apparently notable result can increase unless a testing strategy accounts for multiplicity. The registry record does not report multiplicity adjustment, a prespecified testing hierarchy, or confirmatory status for this secondary analysis. Consequently, these results carry less confirmatory weight than a prespecified primary analysis with a documented testing plan. They should be treated as supportive descriptive evidence rather than as independent proof of the study’s stated objectives.

The registry record does not report a sponsor analysis for this secondary endpoint. The posted percentages and unadjusted comparisons therefore offer the available summary for interpreting the outcome, but they do not provide a basis to infer an undisclosed analysis plan or claim that the secondary finding confirms equivalence between active products.

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

• Percentage of Participants With Treatment Success Based on IGE Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean percent change from baseline in inflammatory lesion counts. A mean summarizes the average endpoint value within an arm, while the standard deviation describes variability among observations around that mean. The mean and standard deviation are different quantities. A standard deviation is not a confidence interval, and it does not indicate how precisely the arm mean itself has been estimated.

What does a mean difference describe?

General statistical explanation: a difference between two arm means expresses the separation of their average outcomes on the endpoint scale. Here, the recalculated comparisons subtract the vehicle mean from an active-arm mean. A negative value corresponds to a more negative mean percent change in the active arm. The difference is a group-level contrast; it does not say that every participant in one arm had a greater reduction than every participant in another arm.

The recalculations use the posted arm means, standard deviations, and analysis sizes to estimate unadjusted contrasts. They are described as unadjusted because they do not incorporate a reported covariate-adjusted model or a reported multiplicity correction. The registry record does not report an adjustment set for these recalculations. They should not be mistaken for the sponsor’s full analysis, which is reported separately and uses final-value analyses.

What does the confidence interval add?

General statistical explanation: a confidence interval expresses uncertainty around an estimated effect under the assumptions of the method used. A narrower interval indicates greater precision than a wider interval on the same scale. An interval that includes zero is compatible with no difference under the interval’s model, while an interval that excludes zero indicates that zero is outside that interval. Neither feature, by itself, establishes clinical importance or equivalence. Clinical importance requires context, and equivalence requires a prespecified margin and a suitable formal analysis.

The recalculated confidence intervals are 95% intervals. They describe uncertainty for the unadjusted mean differences, not the full distribution of participant outcomes. Their interpretation depends on the calculation’s assumptions and the posted summary statistics. The sponsor-reported intervals belong to different analyses, so their estimates and intervals should be read with their stated outcome parameter and method rather than treated as direct replacements for the recalculated intervals.

Why do the analyses differ?

The registry-reported sponsor analyses compare final values and identify the generic comparison as a mean difference and the Finacea comparison as a median difference. The recalculations compare mean percent changes from baseline. A comparison of final values is not the same estimand as a comparison of change from baseline, and a median difference is not the same summary as a mean difference. The registry flags a discrepancy. Accordingly, the sponsor’s own analysis takes precedence; the recalculations are descriptive checks based on posted summaries, not a correction of the sponsor’s result.

ANOVA is the method named for the sponsor’s reported comparisons. General statistical explanation: analysis of variance models outcome means across groups and can be used to test group differences. Its exact implementation, covariates, and assumptions for this trial are not reported in the registry record. It would therefore be inappropriate to infer an adjusted model or a particular analysis plan beyond the method and parameters explicitly reported.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when data vary more than a statistical model expects. If a model assumes less variability than is present, standard errors may be too small and intervals may be too narrow. This is a general concern for some count-data models. The primary result is reported as percent change summarized by a mean and standard deviation, and the registry does not report a count-model analysis or an over-dispersion assessment. Over-dispersion should therefore not be asserted as a feature of this trial’s primary analysis.

How does missing-data handling affect the endpoint?

The registry says that a participant who discontinued between 8 and 12 weeks because of lack of treatment had the number of lesions imputed using last observation carried forward. A participant missing the Week 12 assessment for another reason was excluded. General statistical explanation: carrying the last observed value forward assumes that this value is an acceptable stand-in for the missing follow-up value under the analysis rule. Excluding observations for other missingness reasons can also affect the analyzed population. The registry record does not report sensitivity analyses testing alternative missing-data assumptions, so the robustness of results to other approaches is not reported.

The endpoint uses the PP Population, and the arm analysis sizes are reported separately from the overall enrollment. A per-protocol population can differ from the randomized population, but the registry record does not give a full participant-flow account or detailed criteria defining PP membership. The reported sample sizes should therefore be understood as the endpoint analysis sizes, not as a complete account of randomization, follow-up, or exclusions.

What is the role of the secondary outcome?

Treatment success based on IGE score is binary: participants are classified as having or not having treatment success. A risk difference compares the proportions in two arms, with the sign depending on the order of subtraction. General statistical explanation: a confidence interval for a risk difference conveys uncertainty in the difference between proportions, while a p-value evaluates compatibility with a null comparison under the test’s assumptions. The secondary comparison values are unadjusted. The registry record does not report a multiplicity adjustment or a hierarchy that would make these secondary tests confirmatory.

Multiplicity refers to the risk of false-positive findings when multiple outcomes or comparisons are tested. General statistical explanation: a prespecified adjustment or testing hierarchy can control how evidence is judged across multiple tests. The registry lists two outcome measures and two analyses, but a multiplicity procedure is not reported in the registry record. The unadjusted secondary p-values should therefore be interpreted cautiously and should not be treated as if they account for all testing.

11. Confidence Intervals and Precision

The recalculated mean-difference estimates are accompanied by 95% confidence intervals. For generic foam versus vehicle, the estimate is -6.44 and the interval extends from -11.33 to -1.551. For Finacea versus vehicle, the estimate is -7.31 and the interval extends from -12.32 to -2.304. Both intervals lie below zero, meaning zero is outside these particular recalculated intervals. This describes the unadjusted calculations from posted summary statistics; it does not replace the sponsor’s own analysis, which takes precedence because the registry flags a discrepancy.

General statistical explanation: an interval’s width is a practical indication of precision. It reflects uncertainty in the estimated group contrast under the method’s assumptions, not uncertainty about every participant’s outcome. A confidence interval does not give the probability that the true effect lies within the specific calculated interval. Nor does an interval alone establish whether an effect is important or whether two treatments are equivalent. For equivalence, the interval must be assessed against a prespecified equivalence margin, which is not reported in the registry record.

The sponsor-reported intervals are for different analyses: an ANOVA mean difference in final values for generic foam and an ANOVA median difference in final values for Finacea. Their estimates and intervals cannot be interpreted as the same quantity as the recalculated percent-change mean differences. The registry’s discrepancy flag means the sponsor’s own analysis should be given precedence in describing the trial’s reported result.

The secondary risk-difference interval for generic foam versus vehicle extends from -0.021 to 0.146, while the Finacea-versus-vehicle interval extends from 0.063 to 0.233. These are unadjusted secondary comparisons. Their precision and direction do not resolve the primary equivalence question, and the registry record does not report multiplicity control. The intervals also should not be read as evidence about outcomes beyond the defined treatment-success measure.

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 estimates are participants per arm for 80% power and participants per arm for 90% power. They are not total trial enrollment figures. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a fraction of the observed effect. For example, the row for planning for 75% of the observed effect means the calculation uses a smaller target effect than the row based on the full observed effect. The registry’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm under those assumptions for a design with an 80% chance of detecting the stated effect if that effect is the true one and the planning model holds. The 90% power column gives the corresponding per-arm estimate for a design targeting 90% power. Higher target power generally requires more participants under the same assumptions. These values are planning illustrations calculated from the observed effect, not observed power.

The estimates depend on the observed effect used as the starting point. If the effect to be detected is smaller, the planning calculation requires more participants. This is why the rows based on smaller fractions of the observed effect produce larger per-arm estimates. The calculations are illustrative rather than a reconstruction of the trial’s original design, and the registry record does not report whether the original planning used these assumptions.

The planning estimates are given for pairwise comparisons and should be read alongside the relevant endpoint and contrast. They do not account for a trial-wide multiplicity strategy unless such an adjustment is specified; none is reported in the registry record. They also do not turn an observed result into a prospective design target. A planning value is not evidence that a study had a particular probability of success after the results were observed.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -6.440; pooled standard deviation σ = 27.884.
2. n = 2 × (1.96 + 0.842)² × 27.884² / -6.440² = 294.3, rounded up to 295 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -6.44                      # observed difference in means
sigma <- 27.8837193082875                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3287791)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 295 (80% power), 394 (90% power)
 75% of observed effect: n per arm = 524 (80% power), 701 (90% power)
 50% of observed effect: n per arm = 1,178 (80% power), 1,576 (90% power)
power.t.test: 295.2 
Simulated power at n = 295 per arm: 0.804 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses of active foam against vehicle, both classified as superiority analyses. The generic comparison is an ANOVA of mean difference in final values, with estimate -11.27, 95% confidence interval -16.80 to -5.73, and p < 0.001. The Finacea comparison is an ANOVA of median difference in final values, with estimate -9.71, 95% confidence interval -15.28 to -4.14, and p < 0.001.

The recalculated comparisons instead use posted means and standard deviations for percent change from baseline. Those calculations are unadjusted and are not the same analysis parameter as the sponsor’s final-value results; the reported Finacea parameter also uses a median difference rather than a mean difference. The values should not be treated as interchangeable or used to overwrite one another.

The registry marks a discrepancy. In that circumstance, the sponsor’s own analysis takes precedence. The recalculations can help readers understand what follows from the posted summary statistics, but they are not a replacement for the sponsor’s analysis or evidence that its result is erroneous. The registry record does not report enough detail to reconcile the differing estimates or fully describe the sponsor’s implementation beyond the stated method and parameter.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is defined as percent change from baseline in inflammatory lesion counts at Week 12, and the registry also lists treatment success based on IGE score as a secondary outcome. Multiple arms, outcomes, and pairwise comparisons create a multiplicity question: repeated testing can increase the chance of a statistically notable result even when there is no corresponding underlying effect. General statistical explanation: researchers may address this through a prespecified testing hierarchy or an adjustment to significance thresholds. The registry record does not report a multiplicity procedure, so the unadjusted comparisons should not be interpreted as multiplicity-controlled findings.

The registry describes the study as designed to evaluate therapeutic equivalence between the active foams and superiority of both active products over vehicle. These are different statistical claims and may require different hypotheses and decision rules. An equivalence assessment requires a prespecified margin defining how much difference is acceptable. That margin, the original sample-size justification, and the original statistical plan are not reported in the registry record. Without those details, the posted summaries cannot establish how the study was intended to make a formal equivalence decision.

The primary analysis population is the PP Population. For participants who discontinued between 8 and 12 weeks because of lack of treatment, the registry says last observation carried forward was used to impute lesion counts. Participants missing the Week 12 assessment for another reason were excluded. The record does not report sensitivity analyses using other missing-data methods, nor does it give detailed reasons for all exclusions or a full participant-flow account. These omissions limit assessment of how dependent the endpoint result is on the analysis population and missing-data choices.

The registry record does not report whether interim analyses were planned or conducted, how any interim looks would have been handled, or whether the reported analyses were prespecified in a dated statistical analysis plan. These details should not be inferred from the presence of reported results. Similarly, the record does not provide a complete explanation for the discrepancy between the recalculated summaries and the sponsor’s reported analyses. The sponsor’s own analysis takes precedence, but the available record does not resolve the methodological difference.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypocalcaemia (0.3%), prostate cancer (0.3%), cellulitis (0.3%).

The registry reports serious adverse events affecting 0 of 306 participants in the generic foam group, 2 of 297 in the Finacea group, and 1 of 291 in the vehicle group. It also reports other adverse events affecting 129 of 306, 128 of 297, and 125 of 291 participants in those respective groups. These are arm-specific counts and denominators; they should be read as safety summaries rather than as proof that an event was caused by a study product.

The registry lists hypocalcaemia, prostate cancer, and cellulitis among the top serious adverse event terms, each recorded as 0.3%. Deaths are reported as 0 in each arm. The record does not provide detailed case narratives or enough information to assess the relationship of individual events to treatment. The adverse-event counts are not an efficacy comparison, and the observed counts alone do not establish that the treatments have identical safety profiles.

Safety findings are best interpreted with attention to the reported denominator, event definition, and period of observation. The registry record does not provide additional detail about event timing or a formal comparative safety analysis in the information. The figures describe the recorded events in this study and should not be extended beyond those data.

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

The posted primary summaries show negative mean percent changes in inflammatory lesion counts in all three arms. The sponsor reports superiority analyses for each active foam against vehicle, with estimates and confidence intervals in the direction of a greater reduction in the active arms under the stated final-value analyses. The secondary treatment-success summaries also show a higher recorded percentage in the active arms than in vehicle, although the unadjusted secondary comparisons differ in their precision.

These results do not, by themselves, establish therapeutic equivalence between generic azelaic acid foam and Finacea foam. Equivalence requires a prespecified margin and a formal analysis against that margin; the margin and original statistical decision rules are not reported in the registry record. Similar-looking arm means or evidence of active-versus-vehicle differences are not substitutes for an equivalence analysis.

The primary endpoint result is specific to the PP Population, the lesion-count definition, Week 12, and the registry’s missing-data rules. It is a group-level result and does not describe the response of every participant. The registry also reports different analyses for the sponsor’s superiority comparisons and for the simple recalculations from posted summaries. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence, while the recalculations should be understood as unadjusted descriptive checks.

The results also do not settle questions that the registry record does not report, including the original sample-size justification, equivalence margin, multiplicity procedure, interim analyses, and sensitivity analyses for missing data. The safety counts describe recorded events and do not establish causality or rule out events not observed in this study. Interpretation should therefore remain tied to the stated outcomes, analysis populations, and reported comparisons.

In short, the registry contains evidence of observed differences in this trial and reports sponsor analyses classified as superiority against vehicle. It does not provide enough information to determine whether the prespecified formal criteria for equivalence were met, or how robust all findings are to alternative analysis choices. Statistical significance, precision, clinical relevance, and equivalence are related but distinct considerations.

18. Why This Trial Matters Statistically

This trial illustrates why a study objective and a statistical conclusion are not the same thing. The registry states both equivalence and superiority aims, but those aims call for different forms of evidence. Superiority asks whether one group differs in a specified direction from a comparator; equivalence asks whether the difference is contained within an acceptable range defined in advance. The equivalence margin and its decision rule are not reported in the registry record, so the equivalence objective cannot be verified from the posted means alone.

It also demonstrates the importance of matching an estimate to the quantity being analyzed. A mean difference in percent change, a mean difference in final values, and a median difference in final values do not describe the same estimand. The recalculations from summary statistics can be useful for understanding the posted data, but they should not be substituted for the sponsor’s own analyses. The discrepancy flag makes that distinction especially important.

Precision matters alongside the estimated direction. Confidence intervals show the uncertainty around particular comparisons, while p-values address a separate question about compatibility with a null hypothesis under a test’s assumptions. Neither establishes clinical importance, and neither supplies an equivalence margin. For the secondary outcome, unadjusted testing adds another reason to avoid treating every comparison as equally confirmatory.

Finally, the PP Population and the stated missing-data handling affect which observations contribute to the primary result. Without detailed participant flow, alternative missing-data analyses, and the original analysis plan, readers cannot fully assess the robustness of the result. These are not merely reporting details: they are part of understanding what the estimates represent and what conclusions they can support.

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 record does not report the equivalence margin, original sample-size justification, or complete statistical analysis plan. As a result, the formal basis for evaluating the stated equivalence objective cannot be reconstructed from the posted summaries. The record also does not report whether interim analyses were planned or conducted, or how multiplicity was handled across outcomes and comparisons.

The primary endpoint is analyzed in the PP Population, but the registry does not provide a complete participant-flow account or detailed criteria for membership in that population. The missing-data rule carries the last observation forward for a specified discontinuation circumstance and excludes participants missing Week 12 for other reasons. No sensitivity analyses under alternative missing-data assumptions are reported in the registry record. These features limit evaluation of how changes in analysis population or imputation method might affect the result.

The sponsor-reported superiority comparisons use final values, and the Finacea comparison is described as a median difference, whereas the recalculations use mean percent change. The registry marks a discrepancy, but the record does not explain the difference in sufficient detail to reconcile the estimates. The sponsor’s own analysis takes precedence; the recalculations remain unadjusted and descriptive.

The record lists additional interventions, including cleanser, sunscreen, towel, and moisturizing lotion, without enough detail to characterize their allocation or role. It also does not provide detailed safety narratives or enough information to attribute individual events to study treatment. Finally, the reported results concern the specified population, endpoint definitions, and study period; generalization beyond those conditions is not established by the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate Safety and Equivalence of Generic Azelaic Acid Foam and Finacea® Foam in Participants With Rosacea — NCT03287791.
• Registry record last updated 2019-07-31; status last verified 2019-07.
• Results first posted 2019-07-17.
• 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

NCT03287791 is a completed randomized, parallel-group, vehicle-controlled Phase 3 study sponsored by Actavis Inc. It compared generic azelaic acid foam, 15%, Finacea® foam, 15%, and vehicle foam in participants with moderate facial rosacea. The registry records enrollment of 924 and describes twice-daily application over 12 weeks.

The primary outcome was percent change from baseline in inflammatory lesion counts at Week 12, analyzed in the PP Population. Sponsor-reported analyses are classified as superiority comparisons against vehicle. The registry also records a secondary treatment-success outcome based on IGE score and arm-specific adverse-event counts.

Simple unadjusted recalculations from the posted primary summaries differ from the sponsor’s reported analyses. The registry flags a discrepancy, so the sponsor’s own analysis takes precedence. The equivalence margin, original design assumptions, multiplicity procedure, and several analysis details are not reported in the registry record; the posted results therefore do not by themselves establish a formal equivalence conclusion.