A Study to Assess the Safety, Efficacy and Tolerability of Oral DFD-29 Capsules for the Treatment of Rosacea (MVOR-2): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess the Safety, Efficacy and Tolerability of Oral DFD-29 Capsules for the Treatment of Rosacea (MVOR-2) (NCT05343455), a randomized phase 3 study. The primary outcome is Investigator's Global Assessment (IGA) Treatment Success Compared to Placebo..

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, multicenter, parallel-group study with active and placebo controls. The registry record identifies quadruple masking, while the brief summary describes the study as double-blind. The record does not explain the difference between those masking descriptions, so the exact roles covered by the quadruple-masking designation are not reported in the registry record. The trial is listed as completed. Its recorded start date is 2022-03-29, and its primary completion date is 2023-06-30.

The treatment period was 16 weeks, following an eligibility screening period of up to 30 days. The brief summary describes adults at least 18 years old with moderate to severe papulopustular rosacea. Participants were assigned to DFD-29 40 mg, doxycycline 40 mg, or placebo, taken once daily. The planned allocation ratio in that summary was 3:3:2. The summary also describes planned enrollment at sites in the US and EU: approximately 160 participants at 15 US sites, with the remaining planned participants at 14 EU sites. These are planning statements in the summary, not a description of the final regional enrollment.

The registry enrollment field reports 330, while the brief summary describes approximately 320 planned participants. Those figures refer to different record entries and should not be treated as a reconciled final count. The posted primary outcome denominators are 123 for DFD-29 and 82 for placebo; the active-comparator outcome denominators are 125 for doxycycline and 123 for DFD-29. The registry record does not report why outcome denominators differ from the enrollment figure. The stated primary outcome timeframe is baseline to Week 16, and the primary population is identified as Intent-to-Treat Subjects.

The record lists five outcome measures and three posted secondary outcomes. It reports no sponsor analyses in the analysis listings. Details of the original sample-size justification, the trial's prespecified statistical analysis plan, interim analyses, and any protocol amendments are not reported in the registry record. The posted planning illustrations are separate from the original design rationale.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat Subjects

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: Intent-to-Treat (ITT) Subjects

6. Primary Endpoint

The registry lists the primary outcome as Investigator's Global Assessment (IGA) Treatment Success Compared to Placebo., measured over Baseline to Week 16.

The primary endpoint is Investigator's Global Assessment treatment success compared with placebo, measured from baseline to Week 16. It counts participants who reached Grade 0 or Grade 1 at Week 16 on a modified IGA scale that excludes erythema, and who also had at least 2 grade reduction from baseline. The scale ranges from Grade 0, Clear, to Grade 4, Severe Rosacea, with Grade 1 Near Clear, Grade 2 Mild, and Grade 3 Moderate. A lower score indicates improvement on this scale.

This endpoint turns a clinician-rated severity assessment into a binary outcome. A participant either satisfies the full success definition or does not. Requiring both a low Week 16 grade and a specified improvement from baseline means that the definition includes a final severity criterion as well as a change criterion. It is therefore more specific than simply asking whether the score fell.

A responder-type endpoint can be clinically interpretable because it expresses the result as the proportion of participants meeting a stated threshold. It also depends on the selected scale, threshold, assessment process, and handling of participants without a Week 16 value. The record gives the endpoint definition and labels its population Intent-to-Treat Subjects, but details of missing-outcome handling and the assessment procedures are not reported in the registry record. The posted counts describe how many participants met the definition in each reported group; they do not indicate the degree of improvement among participants who did not qualify as successes.

7. Results Posted in the Registry

• DFD-29: 60.2% (74/123) versus 26.8% (22/82) on control; risk difference 33.3 percentage points (95% CI 20.4 to 46.2), risk ratio 2.24 (1.53–3.30); 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.

IGA Treatment Success Compared to Doxycycline.

• 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:
  • Doxycycline 40 mg: 31.2% (39/125) versus 60.2% (74/123) on control; risk difference -29.0 percentage points (95% CI -40.8 to -17.1), risk ratio 0.52 (0.39–0.70); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Doxycycline 40 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Total Inflammatory Lesion Count Compared to Doxycycline.

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Doxycycline 40 mg: mean -14.60 versus -18.10 on control; difference 3.50 (95% CI 1.53 to 5.47), standardized effect d = 0.44; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Doxycycline 40 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Clinician's Erythema Assessment (CEA) Change Compared to Placebo.

• 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:
  • DFD-29: 24.4% (30/123) versus 12.2% (10/82) on control; risk difference 12.2 percentage points (95% CI 1.8 to 22.6), risk ratio 2.00 (1.03–3.87); unadjusted two-proportion z-test p = 0.031.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DFD-29 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary question in two directions. One repeats the IGA treatment-success concept but compares DFD-29 with doxycycline rather than placebo. Another compares change in total inflammatory lesion count with doxycycline. The erythema assessment uses a separate clinician-rated measure and compares DFD-29 with placebo. Together, these outcomes provide different views of rosacea severity and response, but they are not interchangeable with the primary endpoint.

The posted secondary comparisons have estimates in directions that favor DFD-29 on the outcomes as defined, and each has an unadjusted p-value below 0.05. The IGA comparison with doxycycline and the lesion-count comparison have p < 0.001; the erythema comparison has p = 0.031. These findings are broadly consistent with the primary result in the sense that the posted estimates favor DFD-29 across the listed measures. That consistency does not make the outcomes independent confirmation: they were measured in the same trial, and their definitions and comparators differ.

Unadjusted secondary results carry less inferential weight when multiple outcomes are examined. The chance of at least one apparently notable result can increase across a family of tests, while a p-value calculated for one comparison does not account for the full set. The registry record does not report a multiplicity strategy, a hierarchy of testing, or sponsor-reported analyses for these endpoints. Therefore, the secondary p-values should be treated as descriptive evidence rather than as definitive standalone tests.

The secondary outcomes also have distinct scales and properties. A responder count depends on a threshold, while lesion-count change retains information about magnitude. The erythema assessment addresses a feature excluded from the modified IGA scale used for primary success. Agreement across measures can be informative, but differences in scale, endpoint definition, and comparison group limit direct ranking or pooling of their results. The primary endpoint remains the central prespecified question identified in the registry record.

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

• IGA Treatment Success Compared to Doxycycline.
• Change in Total Inflammatory Lesion Count Compared to Doxycycline.
• Clinician's Erythema Assessment (CEA) Change Compared to Placebo.

9. Statistical Interpretation

10. Statistical Methods Explained

Binary outcomes and the risk difference

The primary endpoint is binary because each participant is classified as a treatment success or not a treatment success. For this type of outcome, a proportion is the number meeting the definition divided by the group denominator. The registry record posts 74 of 123 for DFD-29 and 22 of 82 for placebo, along with proportions of 0.602 and 0.268. The risk difference compares those proportions by subtraction; the posted estimate is 0.333. A positive risk difference in this comparison means that the success proportion was higher in the DFD-29 group than in the placebo group.

The risk difference is an absolute measure. It describes the size of the gap on the proportion scale, while a risk ratio compares proportions multiplicatively and an odds ratio compares odds. Those relative measures can look numerically different from the absolute difference because they use different scales. The posted risk ratio and odds ratio are supplementary descriptions of the same binary comparison, not independent trial outcomes.

Confidence intervals and hypothesis tests

A confidence interval gives a range of values compatible with the observed data under the method's assumptions. It shows the uncertainty around an estimate and helps readers consider both direction and plausible magnitude. A narrower interval indicates greater precision than a wider one, but an interval does not account for every source of uncertainty, such as bias from missing data or deviations from the intended analysis.

The reported p-value is unadjusted. In general, a p-value measures how unusual data at least as incompatible with a null hypothesis would be if that null hypothesis and the test assumptions held. It is not a measure of the probability that a treatment has no effect, nor does it tell readers whether an effect is important in practice. Because several outcomes and comparisons are listed, an unadjusted p-value should not be treated as if it accounts for all testing in the trial.

Interpreting the continuous secondary outcome

The lesion-count secondary outcome is reported as a least-squares mean change, with standard error. A change of -18.1 is posted for DFD-29 and -14.6 for doxycycline; the comparison estimate is 3.5 lesions, with a confidence interval from 1.532 to 5.468 and p < 0.001. Since the outcome is change from baseline, a more negative change represents a larger reduction in lesion count. The posted difference is labeled as a mean difference and its sign reflects the order of groups used in the comparison.

A standard error describes the estimated precision of a mean, not the spread of individual participants' outcomes. The posted comparison includes an approximate pooled standard deviation of 7.906 and a standardized effect estimate of 0.443. The record marks that standard deviation as approximate, because it is derived from the posted summary information rather than reported as an original trial analysis. The registry record does not report the model specification or covariates behind the least-squares means.

Planning illustrations

The planning values are illustrations based on stated fractions of observed effects, not a record of the trial's original design justification. For the binary endpoint, the values are participants per arm. The planning assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. Smaller target effects require more participants under these assumptions. These illustrations do not establish that the trial was designed with these assumptions or that its results have a particular probability of being statistically significant.

What is not documented

The registry record reports no sponsor analyses in its analysis listings. The posted comparison statistics are therefore not accompanied by a detailed account of the sponsor's model, test choice, covariate adjustment, missing-data method, or multiplicity procedure. The original sample-size justification, stopping rules, interim analyses, and planned analysis populations beyond the primary population label are not reported in the registry record. Without those details, the posted calculations can describe the observed summaries and their estimated uncertainty, but cannot answer whether every part of the prespecified trial analysis has been reproduced.

General statistical interpretation also depends on design and conduct. Randomization supports comparison of groups, but does not by itself eliminate problems from missing outcomes, departures from assigned treatment, or selective reporting. Masking can limit some forms of bias, but the registry record's differing masking descriptions are not reconciled. These limitations are reasons to keep conclusions tied to the information documented in the record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.333, with a 95% confidence interval from 0.204 to 0.463. The interval lies above zero, supporting the direction of the posted comparison, while its width indicates that the exact size of the difference remains uncertain. The interval is compatible with a range of positive differences rather than one precisely known value. It does not include uncertainty from unreported aspects of trial conduct or analysis.

For the same primary comparison, the posted risk-ratio confidence interval is 1.525 to 3.296, and the odds-ratio confidence interval is 2.244 to 7.561. These intervals are on relative scales and should not be read as though they were proportions or percentage-point differences. The point estimates and intervals answer related but distinct questions about the observed binary outcome.

Precision depends in part on the amount of information in the comparison, including the number of participants and the frequency of the outcome. The reported denominators differ between the treatment groups, and the confidence interval reflects the posted analysis and its assumptions. The registry record does not report an interval method, adjustment details, or sensitivity analyses. As a result, the interval should be interpreted as the uncertainty estimated by the posted comparison, not as a complete measure of uncertainty from every possible source.

The secondary erythema comparison has a risk-difference interval from 0.018 to 0.226, with p = 0.031. Its lower limit is closer to zero than the primary interval's lower limit, so the estimate is less separated from the null on the absolute-difference scale. The lesion-count comparison has an interval from 1.532 to 5.468 lesions. These intervals describe endpoint-specific precision and should not be compared as if they shared one scale.

A confidence interval is not a guarantee that the true value lies within its particular limits. In general, it is a procedure that would capture the true value at its stated rate over repeated studies under the method's assumptions. It also does not establish clinical importance; that requires context about the outcome and threshold, which is not quantified in the registry record.

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 illustrations give participants per arm for 80% power and participants per arm for 90% power. They do not give total events. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. Rows describe planning for 100%, 75%, or 50% of the observed effect.

In plain terms, the 80% power column gives the estimated number of participants per arm under which the specified design would have an 80% chance of detecting the selected effect at the stated significance level, if the assumptions hold. The 90% column uses a higher chance of detection under the same framework and therefore generally calls for more participants per arm. These are design calculations, not estimates of the chance that the completed trial's result is correct.

The listed requirements increase as the assumed effect becomes smaller. For the primary comparison, planning for 100% of the observed effect gives 34 participants per arm for 80% power and 45 for 90% power; planning for 75% gives 59 and 79, and planning for 50% gives 128 and 171. This pattern reflects the general principle that a smaller difference is harder to distinguish from random variation and requires more information.

These figures are planning illustrations computed from the observed effect, not the trial's original sample-size rationale. The original design assumptions are not reported in the registry record. This is not observed power: it does not retrospectively measure the probability that the completed study detected an effect, and it should not be used as a substitute for reading the estimates and confidence 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 = 0.268; treatment proportion p₁ = 0.602; average p̄ = 0.435.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7011 = 1.3741.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6603 = 0.5557.
4. n = (1.3741 + 0.5557)² / (0.3333)² = 33.5, rounded up to 34 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 <- 0.268292682926829                          # control proportion
p1 <- 0.601626016260163                          # 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(5343455)
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 = 34 (80% power), 45 (90% power)
 75% of observed effect: n per arm = 59 (80% power), 79 (90% power)
 50% of observed effect: n per arm = 128 (80% power), 171 (90% power)
power.prop.test: 33.5 
Simulated power at n = 34 per arm: 0.807 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary outcome and three posted secondary outcomes, with several treatment comparisons. It does not report whether the trial used a formal multiplicity adjustment, a gatekeeping sequence, a hierarchy among secondary endpoints, or another strategy for controlling the chance of false-positive findings across tests. The posted p-values are unadjusted. They should therefore be read as results for their individual comparisons, not as evidence that the full family of outcomes was tested with an overall error rate controlled at a stated level.

The analysis listings report no sponsor analyses. The record consequently does not provide the full statistical analysis plan, details of model selection, covariate adjustment, sensitivity analyses, or a rationale for the analysis population used for each secondary endpoint. The primary outcome identifies the population as Intent-to-Treat Subjects, but the registry record does not give a definition of that population or explain how participants who discontinued, deviated from assigned treatment, or lacked an endpoint measurement were handled.

Missing-data methods are not reported in the registry record. This matters because a Week 16 responder outcome requires an observed or otherwise defined endpoint status. If some outcomes were unavailable, different rules for classifying or imputing those values could affect the estimated proportions. The posted denominators describe the reported outcome groups, but do not by themselves show how those denominators arose or whether every randomized participant contributed an endpoint result.

The record also does not report interim analyses, stopping rules, or whether any planned analyses changed during the trial. It is not possible from the registry record to determine whether the posted comparisons match a prespecified analysis in every respect. These absences do not invalidate the reported summaries; they limit assessment of selective testing, analytic flexibility, and robustness. A complete interpretation would ordinarily use the protocol and statistical analysis plan alongside the registry results, but those details are not reported in the registry record.

15. 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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cholelithiasis (1.2%), ankle fracture (0.8%), mouth injury (0.8%).

Serious adverse events are reported for the safety groups with denominators of 122 for DFD-29, 121 for doxycycline 40 mg, and 82 for placebo. The registry record reports 2 serious adverse events in the DFD-29 group, 0 in the doxycycline group, and 1 in the placebo group. Deaths are reported as 0 in each group. These counts describe the reported safety data; they do not establish that the treatments have equivalent safety or that uncommon harms are absent.

The record also reports other adverse events in 48 participants in the DFD-29 group, 37 in the doxycycline group, and 27 in the placebo group, using the respective safety denominators above. Those are counts of participants affected, not a measure of event severity or duration. The listed serious-event terms include Cholelithiasis at 1.2%, Ankle fracture at 0.8%, and Mouth injury at 0.8%. The record does not explain the denominator used for these term percentages.

Safety comparisons depend on definitions, ascertainment, follow-up, and the number of participants observed. The registry record does not provide detailed event narratives, exposure-adjusted rates, timing, relatedness assessments, or statistical comparisons. The serious-event counts should therefore be read descriptively and alongside the efficacy findings, not as a complete characterization of safety.

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

The posted primary result indicates that, under the registry's treatment-success definition, a greater proportion of the DFD-29 group met the Week 16 IGA success criteria than the placebo group. The estimated absolute difference is 0.333, and its 95% confidence interval is 0.204 to 0.463. The unadjusted p-value is p < 0.001. This is a statistical description of the reported groups and endpoint, not a guarantee about an individual participant's outcome.

The endpoint combines a final severity threshold with improvement from baseline. It does not describe every change in symptoms, every rosacea feature, or the experience of participants who did not meet the response threshold. The modified IGA excludes erythema, which is assessed separately in a secondary outcome. The primary result also covers the 16-week period; follow-up beyond that period is not reported in the registry record.

The study included doxycycline as an active comparator, but the primary question specified in the registry record is DFD-29 compared with placebo. The secondary comparisons add information, yet their unadjusted status and the absence of a reported multiplicity plan mean they should not be treated as equally strong confirmatory evidence. The registry record does not report the sponsor's complete analysis plan, the method for handling missing outcomes, or sensitivity analyses. Those omissions limit how fully the robustness of the posted results can be assessed.

Statistical significance does not by itself establish how important the observed difference is to patients or clinicians. The record provides no threshold for a clinically meaningful difference in the primary endpoint, and no patient-reported outcome is described in the listed results. The reported estimates also do not establish effects for populations not represented in the trial, or outcomes beyond the stated timeframe.

Finally, efficacy and safety are different parts of the evidence. The serious adverse event and death counts are descriptive, and the registry record does not supply enough detail to make a comprehensive benefit-harm assessment. The findings support a focused conclusion about the posted Week 16 endpoint comparison, while broader claims require evidence and context not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates how a binary clinical endpoint can make a treatment comparison easy to state while still requiring careful statistical interpretation. The IGA definition is not simply a score change: it requires both a Week 16 grade of 0 or 1 and at least 2 grade reduction from baseline. That combination affects who qualifies as a success and therefore determines the proportions being compared. Readers need the endpoint definition, group denominators, absolute effect estimate, and uncertainty interval to understand what the headline contrast represents.

It also demonstrates why effect scales matter. The risk difference describes an absolute gap in success proportions; the risk ratio and odds ratio describe relative contrasts. These measures answer related questions but are not interchangeable. Reporting the confidence interval alongside the point estimate helps convey that the observed effect is estimated with uncertainty, even when the p-value is small.

The presence of an active comparator and multiple secondary outcomes makes the distinction between a primary question and exploratory or secondary evidence particularly important. Results that point in a similar direction can strengthen the descriptive story, but unadjusted tests across multiple outcomes do not automatically provide independent confirmation. The registry record's lack of a reported multiplicity strategy and full analysis plan is therefore relevant to the weight given to secondary findings.

Finally, planning illustrations based on the observed effect can be useful for understanding how target effect size relates to sample requirements, but they are not the original trial justification and are not observed power. Keeping planning calculations separate from the trial's own design assumptions prevents retrospective calculations from being mistaken for evidence about the design or the certainty of the result.

18. 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 leaves important operational and analytic details undocumented. It does not report the full protocol or statistical analysis plan, the original sample-size justification, the approach to missing endpoint data, or sensitivity analyses. The primary population is labeled Intent-to-Treat Subjects, but the record does not define how that population was constructed or how participants with unavailable Week 16 assessments were treated. These gaps limit independent assessment of whether the posted outcome denominators and analysis rules fully reflect the randomized groups.

There is also a difference between the registry enrollment field of 330 and the brief summary's approximate plan of 320 participants. The record does not reconcile the figures or provide a final participant-flow account. The outcome denominators are specific to the posted endpoint comparisons and should not be assumed to explain the overall enrollment. Regional enrollment is described as a plan, but final enrollment by region is not reported in the registry record.

The registry record identifies quadruple masking, while the brief summary calls the study double-blind. It does not explain which people were masked or how those descriptions relate. The record also does not report the exact analysis model for least-squares means, multiplicity handling, or whether any interim analysis took place. Without those details, the posted estimates can be interpreted, but a full audit of the planned analysis is not possible.

Finally, the primary endpoint is a clinician-rated threshold outcome over 16 weeks. The registry record does not report longer-term results, detailed patient-reported outcomes, or a prespecified threshold for clinical importance. Serious adverse event counts are small and are not accompanied by detailed narratives or exposure-adjusted analyses. These limitations constrain conclusions about durability, broader patient experience, and uncommon harms.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Assess the Safety, Efficacy and Tolerability of Oral DFD-29 Capsules for the Treatment of Rosacea (MVOR-2) — NCT05343455.
• Registry record last updated 2024-12-03; status last verified 2024-11.
• Results first posted 2024-12-03.
• 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.

22. Record Summary

The registry record describes a completed Phase 3 randomized parallel-group study of oral DFD-29 for moderate to severe papulopustular rosacea. The primary outcome was IGA treatment success at Week 16 compared with placebo, defined by a Week 16 grade of 0 or 1 and at least 2 grade reduction from baseline on a modified scale without erythema. The posted comparison reports 74 successes among 123 DFD-29 participants and 22 among 82 placebo participants, with a risk difference of 0.333 and a 95% confidence interval from 0.204 to 0.463.

The trial also included doxycycline and posted secondary comparisons involving IGA success, lesion-count change, and erythema. Those comparisons are unadjusted. The registry record does not report the full analysis plan, multiplicity procedure, or missing-data methods. Serious adverse events were reported in 2 DFD-29 participants, 0 doxycycline participants, and 1 placebo participant; deaths were 0 in each group. The results describe the posted outcomes and should be interpreted in light of the record's undocumented design and analysis details.