A Controlled Study to Assess the Efficacy, Safety and Tolerability of Oral DFD-29 Extended Release Capsules: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Controlled Study to Assess the Efficacy, Safety and Tolerability of Oral DFD-29 Extended Release Capsules (NCT03340961), a randomized phase 2 study. The primary outcome is Investigator Global Assessment (IGA) 0=Clear, 1=Near Clear, 2=Mild, 3=Moderate, 4=Severe.

2. Clinical Question

The clinical question concerns whether participants assigned to either dose of DFD-29 or to Oraycea® had different Week 16 Investigator Global Assessment (IGA) treatment-success counts from participants assigned to placebo. The registry describes a study of inflammatory lesions of rosacea, with clinical assessments planned across the 16-week treatment period. The posted primary endpoint focuses on an IGA result rather than on a single lesion-count change.

The registry record describes randomized assignment, quadruple masking and a parallel-group design. The posted comparisons contrast each active-treatment group separately with placebo. They do not establish a direct statistical comparison between the active-treatment groups. The endpoint is a threshold-based outcome: it counts participants who meet the stated IGA criteria, rather than describing the full distribution of IGA grades or the average change in grade.

3. Trial Design

This completed phase 2 study (NCT03340961) was described as a multi-center, randomized, double-blind, parallel-group, controlled study of oral DFD-29 Extended Release Capsules for inflammatory lesions of rosacea over 16 weeks. The registry lists quadruple masking. Enrollment was 205. The study started on 2017-10-01, and primary completion was recorded as 2018-11-07.

Participants were assigned to one of four once-daily regimens for 16 weeks: DFD-29 40 mg, DFD-29 20 mg, Oraycea® (doxycycline) 40 mg, or placebo. The posted primary outcome reports the number of participants meeting the IGA treatment-success definition at 16 weeks. The efficacy counts are 35 of 53 for DFD-29 40 mg, 15 of 47 for DFD-29 20 mg, 16 of 48 for Oraycea®, and 6 of 52 for placebo. These are counts with the endpoint, not percentages.

The brief summary says clinical assessments were to use the Investigator’s Global Assessment (IGA, modified scale without erythema), Clinician’s Erythema Assessment (CEA), and inflammatory lesion counts at Weeks 4, 8, 12 and 16 in comparison with Baseline. The posted primary result concerns the Week 16 IGA criterion. The secondary outcome listed is median change in RosaQoL (Rosacea Quality of Life) score from Baseline to Week 16.

The registry lists the study as completed and identifies Dr. Reddy's Laboratories Limited as sponsor. It does not report the original sample-size justification, detailed allocation procedures, or operational details of masking beyond the recorded design description. The registry record also does not report the protocol’s full statistical plan.

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: The FAS (full analysis set) included all subjects that had at least one post Baseline efficacy assessment.

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: The FAS (full analysis set) had all subjects who had at least one post Baseline efficacy assessment.

6. Primary Endpoint

The registry lists the primary outcome as Investigator Global Assessment (IGA) 0=Clear, 1=Near Clear, 2=Mild, 3=Moderate, 4=Severe, measured over 16 weeks.

The primary endpoint counts participants whose IGA result met a prespecified treatment-success definition at the end of the study. Success required an IGA grade of 0 or 1, described as clear or near clear, together with at least 2 grade reduction from Baseline to Week 16. The IGA scale is listed as 0=Clear, 1=Near Clear, 2=Mild, 3=Moderate and 4=Severe; the assessment is identified as a modified scale without erythema.

A threshold outcome can be useful because it gives a direct count of participants who crossed a defined clinical assessment threshold, rather than only reporting an average score change. It also makes the endpoint interpretable as a proportion in each trial group. The trade-off is that a binary success count does not show how far apart participants were from the threshold, or how the full range of IGA grades changed. Participants just short of the criteria and participants with substantially different outcomes are both counted as not meeting success.

The registry identifies the analysis population as the FAS: all subjects with at least one post-Baseline efficacy assessment. The primary outcome timeframe is 16 weeks. Although the brief summary mentions repeated assessments and other clinical measures, the posted primary endpoint is specifically the Week 16 IGA treatment-success count.

7. Results Posted in the Registry

• DFD-29 Extended Release Capsules (40 mg): 66.0% (35/53) versus 11.5% (6/52) on control; risk difference 54.5 percentage points (95% CI 39.1 to 69.9), risk ratio 5.72 (2.63–12.45); unadjusted two-proportion z-test p = <0.001.
• DFD-29 Extended Release Capsules (20 mg): 31.9% (15/47) versus 11.5% (6/52) on control; risk difference 20.4 percentage points (95% CI 4.5 to 36.3), risk ratio 2.77 (1.17–6.54); unadjusted two-proportion z-test p = 0.013.
• Oraycea® (Doxycycline) Capsules: 33.3% (16/48) versus 11.5% (6/52) on control; risk difference 21.8 percentage points (95% CI 5.9 to 37.7), risk ratio 2.89 (1.23–6.77); unadjusted two-proportion z-test p = 0.009.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary: each participant either met the Week 16 IGA treatment-success definition or did not. The posted arm results therefore give counts of participants with success and the group denominators. The success definition combines an IGA grade requirement, Grade 0 or 1, with at least 2 grade reduction from Baseline to Week 16. The reported analysis population is the FAS, defined as subjects with at least one post-Baseline efficacy assessment.

The main effect measure in the posted comparisons is the risk difference. In general, a risk difference is the difference between the proportions experiencing the defined outcome in two groups. It is expressed on the probability scale, so a value of zero represents equal proportions and a positive value means the first group’s proportion is higher in that comparison. The registry gives risk differences of 0.545 for DFD-29 40 mg versus placebo, 0.204 for DFD-29 20 mg versus placebo, and 0.218 for Oraycea® versus placebo. These are unadjusted estimates derived from the posted counts.

Confidence intervals accompany those estimates. In general, a confidence interval describes the range of effect estimates reasonably compatible with the observed data under the method used; it reflects sampling uncertainty and is not a guarantee that the true effect lies within the interval. The registry reports 95% intervals for each risk difference. Their interpretation depends on the analysis method and assumptions, which are not fully described in the registry record. The intervals are useful for judging the range of plausible contrasts, not only whether the estimate is above or below the null value.

Each active-treatment arm is compared with placebo separately. The associated unadjusted p-values are p < 0.001 for DFD-29 40 mg, p = 0.013 for DFD-29 20 mg and p = 0.009 for Oraycea®. A p-value, in general, measures how unusual data at least this discrepant from a null hypothesis would be if that null hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The reported p-values are explicitly unadjusted. The registry record does not report a multiplicity procedure or the original inferential strategy.

The posted comparison summaries also include relative risks and odds ratios. A relative risk compares the outcome proportions as a ratio, while an odds ratio compares the odds of the outcome. Both are relative measures, unlike the risk difference, which is absolute. They can be useful complementary descriptions, but their values have different interpretations and should not be treated as interchangeable. The registry’s posted measures are calculated for each active group against placebo; they are not evidence of direct comparisons among the active groups.

In general, over-dispersion is a concern when observed variability exceeds what a statistical model assumes. It is particularly relevant to count outcomes or clustered observations. The primary outcome is posted as a participant count for a binary endpoint, and the record does not report an over-dispersion assessment or a model specification. It also does not report whether site effects, baseline factors, or other covariates were included in the sponsor’s analysis. The posted results therefore do not support claims about adjusted estimates or modeling choices.

The brief summary mentions IGA, CEA and inflammatory lesion counts at Weeks 4, 8, 12 and 16 relative to Baseline. The primary endpoint reported for analysis is the Week 16 IGA success count. The secondary outcome listed is median change in RosaQoL score from Baseline to Week 16. The registry record does not report the detailed analysis methods for those other outcomes in the material describing posted results.

The record identifies the FAS, but does not report how missing Week 16 assessments were handled, how participants without a post-Baseline assessment were treated, or whether sensitivity analyses were conducted. It also does not report the original sample-size justification, interim-analysis plan, or complete sponsor statistical analysis plan. The posted comparisons should thus be understood as the available unadjusted summaries, not as a reconstruction of every part of the trial’s prespecified analysis.

10. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: narrower intervals indicate less sampling uncertainty under the analysis method, while wider intervals indicate more. The Week 16 risk-difference intervals are 0.391 to 0.699 for DFD-29 40 mg versus placebo, 0.045 to 0.363 for DFD-29 20 mg versus placebo, and 0.059 to 0.377 for Oraycea® versus placebo. All three intervals extend above zero, but their ranges also show that the exact size of each difference is not known with certainty.

The DFD-29 40 mg estimate has an interval that is separated from zero by a larger margin than the intervals for the other active-versus-placebo comparisons. That observation describes the posted estimates and their precision; it is not a statistical test comparing the treatment effects with one another. The registry does not report a direct contrast between the active groups, so differences in their point estimates should not be treated as evidence of a difference between those groups.

Group size and the number of observed endpoint events contribute to precision, but confidence intervals also depend on the method used to calculate them. The registry gives the interval limits without reporting the detailed interval procedure. The event counts are 35 of 53, 15 of 47, 16 of 48 and 6 of 52 across the four efficacy arms. These denominators are not identical, and the interval estimates should be interpreted in their reported form rather than recalculated using an assumed method.

Confidence intervals do not address all uncertainty. They do not resolve questions about missing outcome data, the definition of the analysis population, multiplicity, or the choice of analysis method. Those details are not fully reported in the registry record. The intervals quantify sampling uncertainty for the posted comparisons under their underlying methods; they do not quantify every possible source of bias or uncertainty.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design justification. For these binary comparisons, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The effect being planned for is a stated fraction of the observed effect.

The scenarios describe planning for 100%, 75% or 50% of the observed effect. The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the selected effect under the stated assumptions, if the assumptions and effect are correct. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. Power is a design property calculated before a hypothetical study; it is not a statement about whether the observed trial result is true.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants per arm. The figures are calculated separately for each active-treatment comparison against placebo and will differ because the observed effects differ. They should not be read as a recommendation or as evidence that the completed trial was designed to those sample sizes.

This is not observed power. The registry record does not report the trial’s own sample-size assumptions or original justification. The displayed planning values are illustrations under the stated assumptions, not a retrospective measure of the probability that the completed study detected an effect.

12. 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 = 0.115; treatment proportion p₁ = 0.660; average p̄ = 0.388.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6891 = 1.3506.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5713 = 0.4808.
4. n = (1.3506 + 0.4808)² / (0.5450)² = 11.3, rounded up to 12 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 <- 0.115384615384615                          # control proportion
p1 <- 0.660377358490566                          # 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(3340961)
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 = 12 (80% power), 15 (90% power)
 75% of observed effect: n per arm = 20 (80% power), 26 (90% power)
 50% of observed effect: n per arm = 39 (80% power), 52 (90% power)
power.prop.test: 11.3 
Simulated power at n = 12 per arm: 0.850 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry posts three active-versus-placebo comparisons for the primary binary outcome. Their p-values are unadjusted: p < 0.001 for DFD-29 40 mg, p = 0.013 for DFD-29 20 mg and p = 0.009 for Oraycea®. When several hypotheses are examined, the chance of at least one false-positive result can increase if each is assessed without adjustment. In general, multiplicity procedures address that issue by changing the testing threshold or otherwise accounting for the family of comparisons. The registry record does not report whether the sponsor used such a procedure, or which comparisons were intended to form a testing family. The posted p-values should therefore be read as unadjusted, not as evidence of a reported multiplicity-controlled analysis.

The record identifies the FAS as all subjects with at least one post-Baseline efficacy assessment. It does not state how participants without a post-Baseline assessment were handled, how missing Week 16 IGA results were treated, or whether imputation or sensitivity analyses were used. The registry’s primary endpoint counts and denominators are reported by arm, but the record does not explain whether the denominators reflect all randomized participants, the endpoint-evaluable population, or other analysis-set rules beyond the FAS description.

There are 0 posted analysis records, although the registry displays outcome counts and comparison summaries. The sponsor’s full analysis plan, including model specification, covariate adjustment, interim analyses and handling of protocol deviations, is not reported in the registry record. These omissions limit assessment of whether the posted results correspond to a prespecified analysis and how robust they are to alternative missing-data or multiplicity choices.

The secondary outcome listed is median change in RosaQoL score from Baseline to Week 16. The record also describes planned clinical assessments involving IGA, CEA and inflammatory lesion counts at several visits. It does not report how the full set of outcomes and time points was handled statistically. Consequently, the posted primary comparisons can be described, but a complete accounting of the trial’s analysis hierarchy is not available from the registry record.

14. 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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: atrial fibrillation (2.1%), lymphoma (2.1%), papilloma (2.1%), retinal detachment (2.1%), coronary artery disease (1.9%).

The registry reports serious adverse event counts by arm, with denominators that differ from the efficacy endpoint denominators. Serious adverse events were reported for 1 of 52 participants assigned to DFD-29 40 mg, 2 of 48 assigned to DFD-29 20 mg, 2 of 48 assigned to Oraycea®, and 0 of 53 assigned to placebo. Deaths were reported as 0 in each group.

These are counts of participants affected, not rates calculated for comparison or evidence of a causal relationship. The record does not provide event-level narratives or explain attribution, duration, or the sponsor’s assessment of relatedness in this summary. The listed serious-event terms include Atrial fibrillation, Lymphoma, Papilloma and Retinal detachment at 2.1% each, and Coronary artery disease at 1.9%. The record does not identify these terms by treatment group in the listed summary, so they should not be assigned to a particular arm.

The registry also reports other adverse events for 37 of 52 participants receiving DFD-29 40 mg, 33 of 48 receiving DFD-29 20 mg, 27 of 48 receiving Oraycea®, and 35 of 53 receiving placebo. These broader counts are distinct from the serious adverse event counts. The available summaries do not provide enough detail to compare safety profiles or determine the clinical significance of individual events.

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

The posted data show the number of participants meeting the registry’s Week 16 IGA success definition in each arm and provide unadjusted comparisons of each active-treatment group with placebo. The reported risk differences are positive for all three comparisons, and their confidence intervals are reported zero. The associated unadjusted p-values are p < 0.001, p = 0.013 and p = 0.009 for DFD-29 40 mg, DFD-29 20 mg and Oraycea®, respectively. These findings describe the endpoint and comparisons as recorded; they are not a complete assessment of every efficacy or safety outcome.

The estimates do not establish which active regimen has the largest effect relative to another. Each comparison uses placebo as the reference, and no direct active-versus-active comparison is listed. Comparing the point estimates across separate contrasts is not a substitute for a direct statistical test. The results also do not show the full pattern of IGA grades, CEA measurements, lesion-count changes or RosaQoL outcomes.

The binary endpoint is specific: IGA Grade 0 or 1 plus at least 2 grade reduction from Baseline at Week 16. It captures whether participants met that criterion, not every possible aspect of change. The endpoint’s interpretation is therefore tied to its definition and assessment time. The registry does not provide the detailed analysis plan, missing-data approach or multiplicity handling needed to resolve all analytical uncertainties.

Confidence intervals describe sampling uncertainty around the posted effect estimates under the methods used, but do not account for every source of uncertainty. The available record should not be taken as proof of an individual participant’s likely outcome or as a substitute for broader clinical evidence. The study is a randomized phase 2 trial with enrollment of 205; the registry record alone does not establish how these estimates generalize beyond the trial population or setting.

16. Why This Trial Matters Statistically

This trial illustrates why a binary endpoint should be read through both its definition and its denominator. “Treatment success” is not simply a favorable IGA grade: it requires Grade 0 or 1 and at least 2 grade reduction from Baseline at Week 16. Reporting counts alongside a risk difference makes the comparison more interpretable than a p-value alone, while confidence intervals communicate uncertainty about the size of the difference.

The three active-versus-placebo risk differences are not identical, and their confidence intervals have different widths. That is statistically informative about the observed estimates, but it does not answer whether one active regimen differs from another. A direct comparison requires an analysis designed for that contrast. This distinction matters whenever multiple arms are compared with a shared control.

The unadjusted p-values also highlight the importance of multiplicity. Several comparisons are posted, but the registry does not report a multiplicity strategy. Without that information, the p-values are best described as unadjusted rather than treated as a complete family-wise inferential conclusion. Similarly, the FAS definition is available, but handling of missing Week 16 measurements and the full sponsor analysis plan are not.

Finally, the sample-size illustrations use fractions of observed effects and explicit planning assumptions; they do not reveal the trial’s original design rationale or its probability of success after completion. Separating a planning calculation from an observed result helps prevent overinterpretation. Together, these issues show how endpoint definition, effect scale, precision, multiplicity and analysis-population rules shape what can be concluded from a registry result.

17. 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.

Interpretation is limited by incomplete reporting of the statistical plan. The registry record does not report the original sample-size justification, the planned multiplicity approach, interim analyses, detailed model specification or covariate adjustment. It also does not report how missing Week 16 assessments were handled or whether sensitivity analyses were performed. These omissions prevent a full evaluation of whether the posted estimates reflect the complete prespecified analysis.

The outcome is a threshold-based IGA endpoint at Week 16. It does not summarize the full distribution of IGA grades or the trajectory of response across the visits named in the brief summary. While CEA, lesion counts and RosaQoL are mentioned as assessments or outcomes, the registry record does not provide detailed results for all of them in the posted primary comparison summaries.

The efficacy and safety group denominators are not identical. The record provides the FAS definition and arm-specific denominators, but does not explain the relationship between all randomized participants, participants with efficacy assessments and safety populations. The displayed summaries should therefore be interpreted using their stated denominators rather than assuming a common population across outcomes.

All posted primary comparisons are against placebo, and there is no listed direct comparison between DFD-29 doses or between DFD-29 and Oraycea®. The p-values are unadjusted, and the record does not explain whether other outcomes or time points were included in a broader testing strategy. The safety summaries provide counts and selected event terms but limited information about attribution or event details. These limitations restrict the conclusions that can be drawn from the registry record alone.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Controlled Study to Assess the Efficacy, Safety and Tolerability of Oral DFD-29 Extended Release Capsules — NCT03340961.
• Registry record last updated 2021-03-01; status last verified 2021-02.
• Results first posted 2020-04-21.
• 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.

21. Record Summary

NCT03340961 is a completed phase 2, randomized, quadruple-masked, parallel-group study of DFD-29 Extended Release Capsules for rosacea. The registry lists enrollment of 205 and four once-daily treatment groups over 16 weeks: DFD-29 40 mg, DFD-29 20 mg, Oraycea® 40 mg and placebo.

The primary endpoint was Week 16 IGA treatment success, defined as Grade 0 or 1 with at least 2 grade reduction from Baseline. Posted efficacy counts were 35 of 53, 15 of 47, 16 of 48 and 6 of 52, respectively. Unadjusted active-versus-placebo risk differences and confidence intervals are reported for each comparison.

The record identifies the FAS but does not report the full statistical plan, missing-data approach or multiplicity strategy. Serious adverse event counts and deaths are reported by group, with no deaths recorded in any group.