Clinical Study to Evaluate the Therapeutic Equivalence of Ketoconazole Cream 2% in the Treatment of Tinea Pedis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Study to Evaluate the Therapeutic Equivalence of Ketoconazole Cream 2% in the Treatment of Tinea Pedis (NCT03824912), a randomized phase 3 study. The primary outcome is Primary Efficacy Endpoint: The Number of Patients in Each Treatment Group With a Therapeutic Cure of Tinea Pedis (Equivalence: Per-Protocol Population).

2. Clinical Question

The trial’s primary question concerns a comparison between two formulations of the same named cream, not a comparison of either formulation with placebo. The registry describes the study as randomized, double-blind, vehicle-controlled, parallel-design, and multiple-site. Its primary endpoint is a count of participants meeting a defined cure criterion, rather than a continuous measurement such as symptom score.

The reported primary results include 89 participants with therapeutic cure among 184 in the test group and 90 among 191 in the reference group. A recalculated unadjusted risk difference is 0.013, with a confidence interval from -0.089 to 0.114. These estimates describe the posted counts and the uncertainty around their unadjusted comparison. They do not, by themselves, establish whether a prespecified equivalence criterion was met. The registry’s equivalence margin and sponsor analysis are not reported in the registry record.

3. Trial Design

This was a phase 3 randomized, quadruple-masked, parallel-design study of treatments for tinea pedis. The official title describes it as a multiple-site clinical study and identifies the comparison as therapeutic equivalence between Ketoconazole Cream 2% from Encube Ethicals Pvt Ltd and Ketoconazole Cream 2% from G&W Laboratories Inc. A placebo cream, described as the test vehicle, was also included as a treatment group.

The registry records enrollment of 831 participants, a start date of 2018-08-23, primary completion on 2019-01-24, and completed status. These are whole-trial details; they are not the analysis sizes for every endpoint. For the primary therapeutic-cure result, the per-protocol groups contained 184 participants in the test arm and 191 in the reference arm. That primary analysis excluded the placebo group according to the endpoint description.

The primary outcome was assessed two weeks after the end of treatment, at Day 56 ± 4. The registry also lists four secondary efficacy outcomes: clinical cure and mycological cure, each evaluated for equivalence in the per-protocol population and for superiority in the modified intent-to-treat population. The modified intent-to-treat clinical-cure results include the placebo group; the posted per-protocol secondary comparisons use the test and reference groups.

The registry record does not report the trial’s original sample-size justification, the equivalence margin, or a detailed statistical analysis plan. It also does not describe which groups of people were masked despite recording quadruple masking. No sponsor-reported analyses are listed for the outcomes. Consequently, the numerical comparisons described in this analysis should be read as unadjusted recalculations from the posted summary counts, not as a replacement for a prespecified sponsor analysis.

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 Per-Protocol population was used for this analysis to determine equivalence between the Test and Reference groups only. To determine equivalence, only the test and reference treatment arms are analyzed.

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 Safety population was used for the baseline analysis population. The Safety population included all randomized patients who used at least one dose of product.

6. Primary Endpoint

The registry lists the primary outcome as Primary Efficacy Endpoint: The Number of Patients in Each Treatment Group With a Therapeutic Cure of Tinea Pedis (Equivalence: Per-Protocol Population), measured over Two weeks after the end of treatment (Day 56 ± 4) (Equivalence).

The primary endpoint counts participants in each treatment group who achieved therapeutic cure of tinea pedis in the per-protocol population. Assessment was scheduled two weeks after the end of treatment, at Day 56 ± 4. The registry defines therapeutic cure as meeting both the clinical-cure and mycological-cure criteria. Thus, a participant had to satisfy both parts of the endpoint definition to count as a therapeutic cure.

The endpoint description also defines therapeutic failure. A participant was considered a failure if they had clinical or mycological failure, were considered to have an insufficient therapeutic response, or used topical drug therapy for irritation or pruritus on the feet after the treatment phase. These rules make the outcome a combined clinical and mycological measure, rather than either component alone.

For an equivalence question, a combined cure endpoint can summarize whether participants met the stated response criteria in each treatment group. The primary analysis is restricted to the per-protocol population and compares only the test and reference treatments. The registry labels this an equivalence analysis, but the margin used to define acceptable similarity is not reported in the registry record. Without that margin and the sponsor’s analysis, the posted counts and recalculated confidence interval describe the observed comparison but do not establish the trial’s formal equivalence conclusion.

7. Results Posted in the Registry

• Test: Ketoconazole Cream 2%: 48.4% (89/184) versus 47.1% (90/191) on control; risk difference 1.2 percentage points (95% CI -8.9 to 11.4), risk ratio 1.03 (0.83–1.27); unadjusted two-proportion z-test p = 0.809.

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.

Secondary Efficacy Endpoint: The Number of Patients in Each Treatment Group With a Clinical Cure of Tinea Pedis (Equivalence: Per-Protocol Population)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Test: Ketoconazole Cream 2%: 52.7% (97/184) versus 57.6% (110/191) on control; risk difference -4.9 percentage points (95% CI -14.9 to 5.2), risk ratio 0.92 (0.76–1.10); unadjusted two-proportion z-test p = 0.343.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test: Ketoconazole Cream 2% and the control. The interval gives the range of effects that remain compatible with the data.

Secondary Efficacy Endpoint:The Number of Patients in Each Treatment Group With a Mycological Cure of Tinea Pedis (Equivalence: Per-Protocol Population)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Test: Ketoconazole Cream 2%: 69.0% (127/184) versus 62.1% (118/190) on control; risk difference 6.9 percentage points (95% CI -2.7 to 16.5), risk ratio 1.11 (0.96–1.29); unadjusted two-proportion z-test p = 0.159.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test: Ketoconazole Cream 2% and the control. The interval gives the range of effects that remain compatible with the data.

Secondary Efficacy Endpoint: The Number of Patients in Each Treatment Group With a Clinical Cure of Tinea Pedis (Superiority: Modified Intent-to-Treat Population)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Test: Ketoconazole Cream 2%: 51.3% (100/195) versus 58.3% (116/199) on control; risk difference -7.0 percentage points (95% CI -16.8 to 2.8), risk ratio 0.88 (0.73–1.05); unadjusted two-proportion z-test p = 0.162.
  • Placebo: Cream (Test Vehicle): 36.1% (35/97) versus 58.3% (116/199) on control; risk difference -22.2 percentage points (95% CI -34.0 to -10.5), risk ratio 0.62 (0.46–0.83); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test: Ketoconazole Cream 2% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo: Cream (Test Vehicle) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the picture by separating clinical cure from mycological cure and by reporting results in both per-protocol and modified intent-to-treat populations. The primary outcome combines clinical and mycological cure into therapeutic cure, so neither secondary component alone is identical to the primary endpoint. The population used also changes the meaning of a comparison: a per-protocol result and a modified intent-to-treat result answer related but distinct questions.

The per-protocol secondary outcomes are labeled as equivalence comparisons between the test and reference groups. The modified intent-to-treat outcomes are labeled as superiority comparisons, and the posted clinical-cure results include the placebo group. This difference in stated objective matters when interpreting estimates and p-values. Evidence relevant to superiority against placebo does not by itself establish equivalence between two active formulations, and a component outcome does not replace the combined primary endpoint.

The secondary results should be viewed as supportive or exploratory in relation to the primary question, rather than as independent confirmation of it. The registry lists no sponsor-reported analyses for these outcomes. The posted comparisons are unadjusted recalculations, and the record does not describe any multiplicity procedure or testing hierarchy. When several outcomes and comparisons are examined, the chance of at least one apparently notable result can increase; this is a general reason that unadjusted secondary findings carry less inferential weight.

The overall pattern is therefore best understood across endpoint definition, population, and comparison type, not by treating every result as a direct repeat of the primary analysis. The registry does not provide enough detail to establish how the investigators intended the secondary outcomes to support the primary objective. Their estimates add context, but they do not resolve the unreported equivalence margin or replace the missing formal analysis.

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

• Secondary Efficacy Endpoint: The Number of Patients in Each Treatment Group With a Clinical Cure of Tinea Pedis (Equivalence: Per-Protocol Population)
• Secondary Efficacy Endpoint:The Number of Patients in Each Treatment Group With a Mycological Cure of Tinea Pedis (Equivalence: Per-Protocol Population)
• Secondary Efficacy Endpoint: The Number of Patients in Each Treatment Group With a Clinical Cure of Tinea Pedis (Superiority: Modified Intent-to-Treat Population)
• Secondary Efficacy Endpoint:The Number of Patients in Each Treatment Group With a Mycological Cure of Tinea Pedis (Superiority: Modified Intent-to-Treat Population)

9. Statistical Interpretation

10. Statistical Methods Explained

All efficacy outcomes discussed are binary: each participant either meets the outcome definition or does not. The registry reports the number meeting the endpoint and the group size used in that analysis. The accompanying risk estimates express the group comparison on a proportion scale, while the risk difference expresses the test-group proportion minus the reference-group proportion. A risk difference of zero corresponds to equal observed proportions; a positive estimate indicates a higher observed proportion in the test group, and a negative estimate indicates a lower one. These are general descriptions of the measures.

The primary comparison’s recalculated risk difference is 0.013. Its confidence interval extends from -0.089 to 0.114. Because the interval includes zero, these unadjusted results do not rule out no difference on the risk-difference scale. They also allow differences in either direction. The interval is not an equivalence margin. For a formal equivalence analysis, the confidence interval would need to be compared with a prespecified range of differences considered acceptably small. That range is not reported in the registry record.

The registry labels the primary endpoint as therapeutic cure for equivalence in the per-protocol population. The endpoint definition requires both clinical and mycological cure, and it includes specified circumstances that count as therapeutic failure. The primary analysis population is not the full enrollment: it contains the participants included in the per-protocol comparison of the test and reference arms. A per-protocol analysis can focus on participants meeting the protocol’s analysis criteria, but the detailed criteria for inclusion and exclusion are not reported in the registry record. The record also does not report a primary sponsor analysis or a detailed analysis plan.

The secondary outcomes use different endpoint definitions and analysis populations. Clinical cure and mycological cure are each reported for a per-protocol equivalence question. Clinical cure and mycological cure are also listed for a modified intent-to-treat superiority question. The posted modified intent-to-treat clinical-cure comparison includes test, reference, and placebo groups. These distinctions matter: a comparison of clinical cure alone does not answer the combined therapeutic-cure question, and a superiority comparison is not the same inferential question as an equivalence comparison.

For the binary comparisons, the recalculated estimates are unadjusted. An unadjusted p-value evaluates the observed data under a null comparison for that particular calculation, but it does not account for testing several outcomes or treatment comparisons. A p-value is not the probability that the null hypothesis is true, and a larger p-value does not establish equivalence. In general, multiplicity adjustment or a prespecified hierarchy can help control the interpretation of repeated tests; whether and how the trial planned such procedures is not reported in the registry record.

Confidence intervals convey a range of effect values compatible with the data under the calculation’s assumptions and method. They are useful for assessing both direction and precision, not just whether a threshold is crossed. In general, an interval that spans zero indicates that the data do not clearly distinguish a positive from a negative risk difference at the corresponding confidence level. The interval does not include every possible source of uncertainty, such as uncertainty from missing outcomes or deviations from the analysis plan.

Over-dispersion is a concern for some count or rate outcomes when variability exceeds what a simple model assumes. It is not the main issue for the posted efficacy outcomes, which are participant counts with binary status and are compared using unadjusted risk estimates. More generally, selecting a method that reflects the outcome type and its variability matters; the registry does not report a sponsor model for these outcomes. The outcome summaries do not provide enough detail to assess model-based adjustments or covariate handling.

In a superiority question, a null result is commonly framed as no difference, while an equivalence question asks whether the treatment difference is confined to a prespecified acceptable range. These are different claims and require different inferential criteria. The primary outcome is explicitly identified as an equivalence endpoint, but its margin and the sponsor’s formal method are not reported in the registry record. The recalculated p-value of 0.809 is not itself an equivalence test.

The posted estimates are recalculated from summary statistics and are described as simple unadjusted comparisons. They should be distinguished from the analysis originally planned by the investigators. The registry lists zero reported analyses for the outcomes at issue. It does not report whether there were interim analyses, how missing outcome data were handled, or how the analysis populations were defined in detail. These features can affect interpretation and cannot be reconstructed from group counts alone.

Planning illustrations based on the observed effects are a separate calculation from the trial’s outcome analysis. They use a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. These figures illustrate sample sizes under those assumptions, not the actual design justification. They are not observed power. Their interpretation depends on the chosen effect size and assumptions, and they do not establish whether the trial had adequate power for its intended equivalence question.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.013, with a 95% confidence interval from -0.089 to 0.114. The interval includes zero and extends to both positive and negative values. This indicates that the unadjusted data are compatible with a range of directions and magnitudes of difference under the calculation’s assumptions. The interval gives more context than the point estimate alone, which is close to zero.

A confidence interval describes uncertainty around an estimate; it is not a guarantee that the true value lies inside the particular interval. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. Precision depends partly on the amount of information in the analysis, and is affected by factors such as the group sizes and the frequency of the outcome. The primary comparison used 184 participants in the test group and 191 in the reference group.

The interval should not be confused with the boundary required for equivalence. Equivalence is assessed against a prespecified acceptable range, not simply by observing that a difference test is nonsignificant or that an estimate is close to zero. The equivalence margin is not reported in the registry record, so the interval cannot be judged against the trial’s formal equivalence criterion. The registry also does not report a sponsor analysis whose interval or decision rule could be compared with this recalculation.

These confidence limits describe sampling uncertainty for the unadjusted risk difference. They do not resolve uncertainty arising from missing data, analysis-population definitions, or multiplicity. The record does not report enough detail to assess those issues fully. Accordingly, the interval is useful for describing the precision of the posted primary comparison, but it does not independently establish a clinical or formal statistical conclusion.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants and not total events. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. These are planning illustrations based on the observed comparison, rather than the trial’s original design assumptions; the original sample-size justification is not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under which the calculation would have an 80% chance of detecting the chosen effect if the assumptions and effect were correct. The 90% power column gives the corresponding illustrative number for a 90% chance. These are planning concepts, not guarantees about a future study’s results. The sample sizes depend on the assumed effect, outcome frequency, and calculation assumptions.

Rows using 100%, 75%, or 50% of the observed effect represent progressively smaller effects to detect. Smaller effects generally require more participants to distinguish them from random variation at the same target power and significance level. The displayed planning values vary by endpoint and comparison because the underlying observed effects differ.

These values are not observed power. They do not show the probability that the completed trial detected an effect, and they do not establish that the trial was adequately designed for its stated equivalence objective. In particular, an equivalence design depends on the prespecified equivalence margin, which is not reported in the registry record. The planning figures are illustrations under stated assumptions, not a substitute for the original protocol’s sample-size justification.

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 = 0.471; treatment proportion p₁ = 0.484; average p̄ = 0.477.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7064 = 1.3845.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7063 = 0.5945.
4. n = (1.3845 + 0.5945)² / (0.0125)² = 25,098.4, rounded up to 25,099 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 <- 0.471204188481675                          # control proportion
p1 <- 0.483695652173913                          # 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(3824912)
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 = 25,099 (80% power), 33,600 (90% power)
 75% of observed effect: n per arm = 44,608 (80% power), 59,717 (90% power)
 50% of observed effect: n per arm = 100,337 (80% power), 134,322 (90% power)
power.prop.test: 25098.4 
Simulated power at n = 25,099 per arm: 0.801 (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 lists several efficacy outcomes, including the primary therapeutic-cure endpoint and secondary clinical-cure and mycological-cure endpoints. The secondary endpoints include both equivalence questions in the per-protocol population and superiority questions in the modified intent-to-treat population. The registry record does not report a multiplicity adjustment, a prespecified testing hierarchy, or another procedure for interpreting repeated comparisons.

Multiplicity is a general statistical concern when several hypotheses are tested. If each is considered separately without adjustment or a planned ordering, the overall chance of a false-positive finding can be greater than for a single test. This does not mean that any particular posted result is false; it means that unadjusted secondary p-values should be interpreted cautiously and in the context of a prespecified plan. The registry’s reported analyses list is empty for the outcomes discussed, so the intended handling of multiple tests is not available.

Missing-data handling is also not reported in the registry record. The posted endpoint summaries give analysis group sizes, but do not describe how participants without an evaluable endpoint were treated, whether missingness was imputed, or what assumptions were made. The details of the per-protocol and modified intent-to-treat population definitions are not reported beyond their names and endpoint descriptions.

The record does not report interim analyses, the original sample-size justification, or the equivalence margin. These omissions limit assessment of whether the posted calculations match the planned inferential approach. The recalculated estimates remain descriptive comparisons based on the available summary statistics; they cannot recover absent decisions about analysis populations, missing observations, or multiplicity.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The safety counts are reported for three groups: test, reference, and placebo vehicle. Serious adverse events affected 0 of 314 participants at risk in the test group, 0 of 319 in the reference group, and 0 of 156 in the placebo group. Deaths were 0 in each group. The registry lists no serious adverse event terms.

These counts mean that no serious adverse events or deaths were recorded in the posted safety summaries for these groups. They do not show that the risk of a rare event is zero, nor do they establish that the groups have identical safety profiles. General interpretation of zero observed events depends on how many participants were monitored, the duration and completeness of follow-up, and how events were defined and collected. The registry record does not provide further detail about these aspects.

Other adverse events affected 12 participants in the test group, 15 in the reference group, and 6 in the placebo group. Those are separate from the serious-event counts. Counts alone do not describe event type, severity, timing, or causal attribution. The registry does not list the most frequent serious-event terms because none are posted.

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

The posted primary results describe therapeutic-cure counts in the per-protocol test and reference groups at Day 56 ± 4. The recalculated risk difference is 0.013, and its confidence interval ranges from -0.089 to 0.114. These values indicate that the observed difference is estimated with uncertainty that includes zero and values on either side. They are a statistical description of the posted summary counts.

They do not, on their own, establish that the formulations are equivalent. A formal equivalence conclusion requires a prespecified margin defining how much difference is acceptable and an analysis designed to assess whether the uncertainty lies within that margin. The equivalence margin and sponsor’s analysis are not reported in the registry record. Likewise, an unadjusted p-value of 0.809 is not evidence of equivalence simply because it is not small.

The findings also do not establish that either treatment works or does not work. A cure count in one group cannot establish a causal effect by itself, and the primary comparison is between two active formulations rather than against no treatment. The trial included a placebo vehicle arm, and a secondary modified intent-to-treat clinical-cure comparison is posted for that arm, but it is a different endpoint and population from the primary therapeutic-cure analysis.

More broadly, the registry’s posted counts and recalculations should be interpreted alongside the absence of a reported analysis plan, equivalence margin, missing-data methods, and multiplicity approach. Those details affect how a formal conclusion should be made. The available results can describe the observed outcomes and their statistical precision, but the registry record does not contain enough information to reconstruct all protocol-based decisions.

17. Why This Trial Matters Statistically

This trial is statistically notable because its primary objective is described as therapeutic equivalence, while the posted primary result is a count of participants meeting a combined cure definition. Equivalence is not established by a small observed difference or by a conventional test that fails to detect a difference. It depends on an acceptable margin chosen in advance and a suitable analysis. Since the margin and sponsor analysis are not reported in the registry record, readers must distinguish the observed comparison from the formal equivalence claim.

The endpoint structure also illustrates why outcome definitions matter. Therapeutic cure requires both clinical and mycological cure, whereas the secondary outcomes consider those components separately. A study can produce different estimates for a combined endpoint and its components because the criteria are not the same. Likewise, analysis populations matter: per-protocol and modified intent-to-treat results can address different estimands and should not be treated as interchangeable.

The registry includes a placebo vehicle group and reports safety counts across all three groups, but the primary equivalence analysis compares only the two active formulations. This highlights the importance of identifying which comparison answers which question. The unadjusted secondary findings also need cautious interpretation because multiple endpoints and comparisons are listed, while the planned multiplicity strategy is not reported.

Finally, planning illustrations based on observed effects can help readers understand how assumed effect size relates to sample size, but they cannot reveal the trial’s original design rationale. The original sample-size justification is not reported. Together, these features make clear why registry counts, uncertainty intervals, and formal protocol analyses should be read as distinct kinds of evidence.

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 main limitation for interpreting the primary result is that the registry labels it an equivalence endpoint but does not report the equivalence margin or sponsor analysis. Without those, the recalculated risk difference and interval cannot establish whether the prespecified equivalence criterion was met. The posted comparison is unadjusted and should be understood as a recalculation from summary counts.

The analysis population is per-protocol, but detailed criteria for inclusion in that population are not reported in the registry record. The record does not describe missing outcome data, the handling of participants without evaluable results, or sensitivity analyses. These details matter because exclusions and missingness can affect a per-protocol estimate.

Several secondary efficacy outcomes and comparison types are listed, but the record does not report a multiplicity procedure or testing hierarchy. It also lists no sponsor-reported analyses. Therefore, the secondary estimates and p-values cannot be evaluated against a complete prespecified analysis plan. The registry does not report interim analyses or the original sample-size justification; the observed-effect planning illustrations do not fill that gap.

Safety summaries report event counts, but do not provide detailed event descriptions, timing, duration, or causal assessments in the information considered. Zero serious events in the posted groups does not rule out uncommon risks. Finally, group counts and summary estimates do not provide participant-level information, limiting assessment of baseline balance, adherence, or other factors that might inform interpretation. These limitations concern what can be concluded from the registry record, not necessarily what was available to the trial investigators.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Study to Evaluate the Therapeutic Equivalence of Ketoconazole Cream 2% in the Treatment of Tinea Pedis — NCT03824912.
• Registry record last updated 2019-06-27; status last verified 2019-06.
• Results first posted 2019-06-13.
• 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, quadruple-masked, parallel-design, multiple-site study of Ketoconazole Cream 2% for tinea pedis. Enrollment was 831. The study compared the Encube test formulation with a G&W reference formulation and included a placebo vehicle arm.

The primary efficacy endpoint was therapeutic cure in the per-protocol population, assessed two weeks after treatment at Day 56 ± 4. Therapeutic cure required both clinical and mycological cure. The posted primary comparison included 184 participants in the test group and 191 in the reference group.

The recalculated unadjusted primary risk difference was 0.013, with a confidence interval from -0.089 to 0.114. The registry does not report the equivalence margin or sponsor analysis, and no sponsor-reported analyses are listed for the outcomes discussed. Safety summaries report zero serious adverse events and zero deaths in each of the three groups. The registry also lists secondary cure outcomes in per-protocol and modified intent-to-treat populations.