Clinical Equivalence of Two Butenafine Hydrochloride 1% Creams in Patients With Interdigital Tinea Pedis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Equivalence of Two Butenafine Hydrochloride 1% Creams in Patients With Interdigital Tinea Pedis (NCT00835510), a randomized phase 1 study. The primary outcome is Therapeutic Cure - Superiority Analysis.

2. Clinical Question

Therapeutic cure required both clinical cure and mycological cure. Clinical cure was judged using recorded signs and symptoms; mycological cure required negative potassium hydroxide testing and a negative fungal culture. This composite outcome therefore combines a clinical assessment with test results, rather than representing either component alone.

The central statistical distinction is between the study’s stated broader aim and the specific primary analysis posted in the registry. The primary result addresses superiority over vehicle. It does not, by itself, establish clinical equivalence between the active creams. The registry record does not report an equivalence margin or a separate equivalence analysis.

3. Trial Design

The registry describes NCT00835510 as a randomized, quadruple-masked, parallel-design study conducted at multiple sites. Its official title identifies it as placebo controlled. The record lists Phase 1 and an enrollment of 548. The trial status is completed. The two active groups received butenafine creams, while the comparator group received vehicle; all three regimens are described as applied for 7 days.

The primary outcome was therapeutic cure at 42 days, analyzed as the number of participants meeting the cure definition. The efficacy population excluded participants with negative baseline cultures and required a positive baseline culture, at least one dose, a follow-up visit, and day 42 data. Thus, the primary efficacy counts do not describe every enrolled participant. The registry record does not report the number randomized to each group in the primary analysis population before these eligibility and follow-up requirements were applied.

Although the study summary describes assessing comparable safety and efficacy between the two active products and superiority of active treatments over vehicle, the posted primary outcome is explicitly labeled a superiority analysis. The reported primary analyses compare Taro butenafine with vehicle and Lotrimin Ultra with vehicle. A direct active-versus-active result is not reported in the primary analyses presented in the registry record.

The record lists therapeutic cure, mycologic cure, clinical cure, and safety and adverse-event profile among secondary outcomes. It does not report the protocol’s original sample-size justification, the planned allocation ratio, details of sequence generation, or the full statistical analysis plan. Masking is recorded as quadruple, but the registry record does not specify which roles were masked. These omissions limit assessment of design details beyond the randomized, masked, parallel-group description.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Patients with negative cultures at baseline are excluded. Efficacy ITT analysis includes all patients with positive baseline cultures, who received at least one dose of medication, had a follow-up visit and had data for the day 42 visit.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Therapeutic Cure - Superiority Analysis, measured over 42 days.

The primary endpoint was therapeutic cure at 42 days, recorded as a participant count. A participant qualified only if both clinical cure and mycological cure were achieved. Mycological cure required both a negative potassium hydroxide test and a negative fungal culture.

Clinical cure was determined from fissuring, erythema, maceration, vesiculation, scaling, exudation, pruritus, and burning. Each was rated on a scale from 0 to 3, from none through severe. The definition required an erythema score of at most 2 and a total score for the other seven signs and symptoms of less than 2. This rule combines several clinical features rather than relying on a single symptom.

A composite endpoint can address more than one dimension of an outcome: in this case, clinical signs and symptoms alongside mycological findings. That makes the cure definition more specific than either a symptom assessment or a laboratory result alone. It also means that the overall endpoint depends on meeting both components; a participant who met one component but not the other would not meet the posted therapeutic-cure definition.

The endpoint is suited to the registry’s stated comparison of cure counts between treatment groups. However, the registry record does not report a separate threshold for equivalence between the active creams. The primary outcome’s stated analysis is superiority versus vehicle, so the endpoint and reported analysis should be interpreted in that context.

7. Results Posted in the Registry

• Butenafine Cream 1% (Taro): 53.1% (76/143) versus 34.3% (24/70) on control; risk difference 18.9 percentage points (95% CI 5.1 to 32.7), risk ratio 1.55 (1.08–2.22); unadjusted two-proportion z-test p = 0.010.
• Lotrimin Ultra (Butenafine) 1%: 71.1% (108/152) versus 34.3% (24/70) on control; risk difference 36.8 percentage points (95% CI 23.5 to 50.0), risk ratio 2.07 (1.48–2.91); 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.

Therapeutic Cure

• 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:
  • Butenafine Cream 1% (Taro): 20.1% (30/149) versus 15.5% (11/71) on control; risk difference 4.6 percentage points (95% CI -6.0 to 15.2), risk ratio 1.30 (0.69–2.44); unadjusted two-proportion z-test p = 0.409.
  • Lotrimin Ultra (Butenafine) 1%: 24.8% (38/153) versus 15.5% (11/71) on control; risk difference 9.3 percentage points (95% CI -1.5 to 20.2), risk ratio 1.60 (0.87–2.95); unadjusted two-proportion z-test p = 0.115.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Butenafine Cream 1% (Taro) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lotrimin Ultra (Butenafine) 1% and the control. The interval gives the range of effects that remain compatible with the data.

Mycologic Cure

• 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:
  • Butenafine Cream 1% (Taro): 71.6% (101/141) versus 47.1% (33/70) on control; risk difference 24.5 percentage points (95% CI 10.6 to 38.3), risk ratio 1.52 (1.16–1.99); unadjusted two-proportion z-test p = <0.001.
  • Lotrimin Ultra (Butenafine) 1%: 84.2% (128/152) versus 47.1% (33/70) on control; risk difference 37.1 percentage points (95% CI 24.0 to 50.1), risk ratio 1.79 (1.38–2.31); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Butenafine Cream 1% (Taro) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Lotrimin Ultra (Butenafine) 1% than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Clinical Cure

• 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:
  • Butenafine Cream 1% (Taro): 58.5% (83/142) versus 38.6% (27/70) on control; risk difference 19.9 percentage points (95% CI 5.9 to 33.9), risk ratio 1.52 (1.09–2.10); unadjusted two-proportion z-test p = 0.006.
  • Lotrimin Ultra (Butenafine) 1%: 73.0% (111/152) versus 38.6% (27/70) on control; risk difference 34.5 percentage points (95% CI 21.0 to 47.9), risk ratio 1.89 (1.39–2.58); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Butenafine Cream 1% (Taro) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Lotrimin Ultra (Butenafine) 1% than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover therapeutic cure at 7 days, mycologic cure at 42 days, clinical cure at 42 days, and safety and adverse-event profile. Across the three efficacy outcomes with posted group counts, the active groups generally have more recorded cures than vehicle at the corresponding assessment time. The pattern is not uniform in statistical precision: the 7-day therapeutic-cure recalculations have confidence intervals that include no difference for both active-versus-vehicle comparisons, while the 42-day mycologic-cure and clinical-cure intervals exclude no difference for both comparisons.

This broad pattern is consistent with the primary result in the limited sense that more cure events are recorded in the active groups than in vehicle in the posted efficacy comparisons. The secondary outcomes also separate the components of the primary composite: clinical cure reflects signs and symptoms, while mycologic cure reflects test results. Their pattern may help describe which aspects of the composite outcome are represented in the posted findings, but it does not replace the primary endpoint or establish an active-versus-active comparison.

These secondary comparisons carry less inferential weight than a prespecified primary analysis. The registry record does not report a multiplicity adjustment strategy for the many outcomes and comparisons. When several outcomes or contrasts are examined, the chance of finding apparently notable results can increase unless the analysis plan accounts for that testing. The registry does not report whether these secondary analyses were confirmatory or exploratory, or how their interpretation was intended to relate to the primary endpoint.

Accordingly, secondary results are best read as supporting descriptive context rather than as independent confirmation of the primary conclusion. The record’s secondary findings do not establish equivalence between the two active creams, and their interpretation is further limited by missing information about the analysis plan and handling of incomplete follow-up.

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

• Therapeutic Cure
• Mycologic Cure
• Clinical Cure
• Safety and Adverse Event Profile

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either met the therapeutic-cure definition or did not. The posted arm values are counts of participants meeting that definition, alongside the number included in each group. For a binary endpoint, a comparison can be expressed as a difference in the proportions with the event. Here, the recalculated risk difference subtracts the vehicle event proportion from the active-treatment event proportion. A positive risk difference indicates a higher observed event proportion in the active group.

What the reported test asks

The registry reports Fisher exact tests for the two primary active-versus-vehicle comparisons. Fisher’s exact test evaluates whether the observed allocation of event and non-event counts across two groups is compatible with no association, using the group totals and event counts. It is a method for categorical data. The registry gives p = 0.013 for Taro butenafine versus vehicle and p < 0.001 for Lotrimin Ultra versus vehicle.

A p-value describes how unusual data at least as incompatible with the null hypothesis as the observed data would be under that null model. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of a difference. The primary interpretation should therefore consider the observed counts and an effect estimate with its uncertainty, rather than relying on a p-value alone.

What the recalculation adds

The recalculated risk differences give an absolute comparison on the event-proportion scale. For Taro butenafine versus vehicle, the estimate is 0.189 and its 95% confidence interval is 0.051 to 0.327. For Lotrimin Ultra versus vehicle, the estimate is 0.368 and its 95% confidence interval is 0.235 to 0.500. The associated recalculated unadjusted p-values are 0.01 and less than 0.001, respectively. These are simple unadjusted calculations from the posted summary statistics. The registry-reported Fisher exact tests remain the sponsor’s own analyses and are reported separately.

Risk ratios and odds ratios are alternative ways to express associations for binary outcomes. They compare relative rather than absolute event frequency, and their numerical interpretation differs from that of a risk difference. The registry record includes recalculated relative measures, but the main interpretation can remain on the absolute risk-difference scale because it directly describes the difference in event proportions. No adjustment for covariates is represented by these unadjusted recalculations.

Why uncertainty matters

A confidence interval describes a range of effect estimates compatible with the observed data under the statistical method and its assumptions. A narrow interval indicates greater precision than a wide interval, while an interval spanning no difference leaves a wider range of plausible effects that includes no difference. The intervals for both primary recalculated comparisons exclude no difference, but their widths still matter: they convey uncertainty about the size of the effect, not just its direction.

General statistical explanation: a confidence interval does not guarantee that the true effect lies inside its endpoints, and it does not account automatically for every design or measurement limitation. Interpretation depends on the analysis population, outcome definition, assumptions, and handling of missing data. Those details are not all reported in the registry record.

Why the analysis population matters

The registry defines the primary efficacy population using baseline culture status, receipt of at least one dose, attendance at a follow-up visit, and availability of day 42 data. This population differs conceptually from an analysis that includes every randomized participant regardless of treatment received or follow-up completion. The record does not report a complete participant flow or the method used for missing day 42 outcomes. The reported estimates therefore describe the defined efficacy population, while the extent to which exclusions or missingness could affect the estimates cannot be assessed from the registry record.

The study’s stated aim includes comparing the active products for equivalence, but a superiority comparison of each product against vehicle does not answer that question. General statistical explanation: an equivalence analysis ordinarily needs an advance definition of the largest difference that would still count as equivalent, and the uncertainty interval is assessed against that boundary. The equivalence boundary and an equivalence analysis are not reported in the registry record. The vehicle comparisons can support interpretation of active-versus-vehicle differences, but should not be substituted for an active-versus-active equivalence test.

11. Confidence Intervals and Precision

The recalculated 95% confidence interval for Taro butenafine versus vehicle runs from 0.051 to 0.327 on the risk-difference scale. For Lotrimin Ultra versus vehicle, it runs from 0.235 to 0.500. Both intervals are entirely above no difference, consistent with higher observed therapeutic-cure proportions in the active groups in these comparisons.

The intervals also show that the exact size of each difference is uncertain. The Taro comparison spans a range from a smaller positive difference to a larger one; the Lotrimin Ultra comparison likewise allows a range of positive differences. A point estimate is a single summary of the data, whereas the interval communicates the range of estimates compatible with the data and method. It should not be treated as a guarantee about the true effect or as a measure of clinical importance.

The reported primary analysis uses Fisher exact tests, while the intervals above accompany unadjusted risk-difference recalculations. These are different statistical summaries, so they should be read as complementary descriptions rather than assumed to be outputs of one identical procedure. The recalculations use the posted group counts and do not incorporate covariate adjustment.

Precision is also affected by the analysis population and the number of observed outcomes. The primary efficacy counts were 143 participants in the Taro group, 152 in the Lotrimin Ultra group, and 70 in the vehicle group. The registry record does not report the original sample-size justification or the planned precision target. It also does not report enough information to assess the effects of missing day 42 data. Thus, the intervals quantify sampling uncertainty under the recalculation method, but do not resolve uncertainty arising from unreported analysis decisions or limitations in follow-up.

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 for these binary outcomes are expressed as participants per arm, not total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column indicates the planned participants per arm under those assumptions for a design intended to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning count for a design intended to have a 90% chance under the same assumptions. These are design illustrations, not descriptions of the trial’s actual randomized group sizes.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. That follows from the general statistical principle that smaller effects are harder to distinguish from random variation at a given significance level and power target. The observed effect is only a starting point for these illustrations; it may not be a reliable estimate of the effect expected in a future study.

These planning calculations are not observed power. They do not describe the probability that the completed trial’s results are correct, and they do not change the uncertainty shown by the observed estimates and confidence intervals. They also should not be taken as evidence that the trial was originally designed around these assumptions, because its own planning rationale is not reported in the registry record.

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 = 0.343; treatment proportion p₁ = 0.531; average p̄ = 0.437.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7015 = 1.3749.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6887 = 0.5796.
4. n = (1.3749 + 0.5796)² / (0.1886)² = 107.4, rounded up to 108 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 <- 0.342857142857143                          # control proportion
p1 <- 0.531468531468531                          # 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(835510)
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 = 108 (80% power), 144 (90% power)
 75% of observed effect: n per arm = 190 (80% power), 253 (90% power)
 50% of observed effect: n per arm = 419 (80% power), 561 (90% power)
power.prop.test: 107.4 
Simulated power at n = 108 per arm: 0.795 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses of the primary therapeutic-cure outcome using Fisher exact tests. The comparison of Taro butenafine with vehicle has p = 0.013, and the comparison of Lotrimin Ultra with vehicle has p < 0.001. These are the trial’s reported inferential results for the primary comparisons.

The recalculations express each comparison as an unadjusted risk difference with a 95% confidence interval and an unadjusted p-value. They use the posted event counts and group sizes, giving p = 0.01 for Taro butenafine versus vehicle and p < 0.001 for Lotrimin Ultra versus vehicle. Their purpose is to provide an absolute effect estimate and a transparent summary of uncertainty alongside the sponsor’s test results.

The registry record marks no discrepancy between the reported analysis and the recalculations. The direction of the results is consistent: both analyses indicate higher observed therapeutic-cure frequency in each active group than in vehicle. The sponsor’s reported analysis remains the trial’s own analysis; the recalculated risk differences are complementary, simple unadjusted estimates and are not a substitute for it.

Neither the reported sponsor comparisons nor these recalculations test equivalence between the two active products. The primary comparisons are each against vehicle, and an equivalence margin and direct active-versus-active equivalence analysis are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is therapeutic cure at 42 days, with two reported comparisons against vehicle. The registry also lists multiple secondary outcomes and reports additional efficacy measurements. This creates a multiplicity question: when several outcomes and comparisons are examined, the interpretation of individual p-values depends partly on whether the analysis plan controlled the overall false-positive risk or designated some analyses as exploratory.

A multiplicity adjustment or testing hierarchy is not reported in the registry record. It is therefore not possible to determine whether the reported p-values were adjusted, whether the two primary comparisons had a prespecified order, or how secondary tests were intended to affect the overall conclusions. The Fisher exact p-values should be understood as the reported results for their individual comparisons, not as evidence that a family-wide error rate was controlled.

The primary efficacy population is defined as participants with positive baseline cultures who received at least one dose, attended a follow-up visit, and had day 42 data. Participants with negative baseline cultures were excluded. This definition is not the same as including every randomized participant in the primary analysis. The registry record does not report a complete flow of randomized participants into the analysis groups, the number missing day 42 data, or the reasons for missingness.

The method for handling missing outcomes is also not reported. It is not possible to tell whether missing values were excluded, imputed, or addressed through sensitivity analyses. The registry record does not report sensitivity analyses assessing how alternative assumptions about missing outcomes might affect the result. These omissions matter because the primary analysis requires observed day 42 data, and the influence of missingness depends on why data are absent and how those participants compare with those assessed.

The record lists 548 enrolled participants, while the primary efficacy outcome uses smaller group-specific analysis counts. Without a reported flow diagram or fuller accounting, the reasons for that difference cannot be fully assessed. These limitations do not negate the posted comparisons, but they constrain conclusions about analysis populations, robustness, and the implications of testing multiple outcomes.

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

The posted primary results show that more participants met the therapeutic-cure definition in each active group than in the vehicle group at 42 days. The registry’s Fisher exact tests report p = 0.013 for Taro butenafine versus vehicle and p < 0.001 for Lotrimin Ultra versus vehicle. The unadjusted recalculations also estimate positive risk differences, and their 95% confidence intervals exclude no difference.

These results describe differences in the observed outcome frequencies for the defined efficacy population. They do not establish that the active creams are equivalent to each other. The primary analyses compare each active treatment with vehicle, and the registry record does not report an equivalence margin or a direct equivalence analysis. A finding that both active groups differ from vehicle is not, by itself, evidence that the active groups have equivalent outcomes.

The results also do not establish that every enrolled or randomized participant had the same outcome pattern. The efficacy analysis requires baseline culture positivity and day 42 data, among other conditions. The record does not report how missing day 42 outcomes were handled or provide a complete participant flow. The posted counts therefore apply to the analysis population described in the registry, and their generalization to participants outside that population is uncertain.

Statistical significance and effect size answer different questions. A p-value reflects compatibility with a null model under a particular test, while the risk difference and its confidence interval describe the estimated absolute contrast and its precision. Neither alone determines clinical importance. The registry record does not define a threshold for a clinically important difference.

Finally, these registry results do not constitute medical advice. They are a statistical account of the posted design and outcome findings. Decisions about treatment, individual circumstances, and evidence beyond this trial are outside what these results establish.

17. Why This Trial Matters Statistically

This trial illustrates why the question attached to an analysis matters as much as the treatment groups. The study summary describes both comparability between active products and superiority over vehicle, but the posted primary outcome is a superiority analysis with each active group compared against vehicle. Keeping those questions distinct prevents a positive vehicle comparison from being mistaken for evidence of equivalence between active treatments.

It also shows the value of reporting absolute effect estimates alongside hypothesis tests. The sponsor’s Fisher exact tests summarize evidence against a no-association model for each comparison. The recalculated risk differences give an absolute scale for the observed contrasts, while the confidence intervals communicate uncertainty around those estimates. Reading the test, estimate, and interval together gives a fuller account than relying on a p-value alone.

The primary endpoint also illustrates how composite definitions shape interpretation. Therapeutic cure required both clinical and mycological criteria, so the result combines distinct kinds of assessment. The separately posted clinical and mycologic outcomes provide context about those components, while their multiplicity and secondary status call for more cautious interpretation.

Finally, analysis-population definitions and missing-data information are essential to judging how broadly results apply. Here, the primary efficacy population required positive baseline cultures and day 42 data, while details about missing outcomes and the original statistical plan are not reported. These features do not erase the observed comparisons; they define the limits of what can be inferred from the registry record.

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 design-specific limitation is the difference between the study summary’s stated interest in active-product comparability and the posted primary analysis, which compares each active group with vehicle. The registry does not report an equivalence margin or a direct active-versus-active equivalence analysis. The primary results therefore cannot resolve the study’s equivalence question as stated in the summary.

The primary efficacy analysis is restricted to participants with positive baseline cultures who received at least one dose, had a follow-up visit, and had day 42 data. The record does not report a full flow from enrollment through randomization and analysis, or explain the reasons participants may not appear in the primary analysis counts. The handling and extent of missing day 42 outcomes are not reported.

Information needed to assess the original statistical plan is limited. The registry record does not report the original sample-size justification, planned allocation details, multiplicity strategy, or whether secondary analyses were confirmatory. The planning illustrations based on observed effects should not be confused with the trial’s own design rationale.

Safety information is also incomplete for interpretation. The registry lists affected-participant counts for serious and other adverse events, but does not give the numbers at risk for these summaries. Death counts are not reported in the registry record. Cellulitis at 0.9% and tachycardia at 0.5% are listed among serious-event terms, without enough detail in the posted information to attribute those percentages to a particular study group. Without denominators and fuller event context, comparative safety rates cannot be assessed from these figures alone.

These limitations are specific to the information recorded for this trial. They qualify interpretation of the efficacy population, the active-versus-active question, and safety comparisons, without changing the direction of the posted active-versus-vehicle outcome counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Equivalence of Two Butenafine Hydrochloride 1% Creams in Patients With Interdigital Tinea Pedis — NCT00835510.
• Registry record last updated 2014-02-04; status last verified 2014-01.
• Results first posted 2009-10-06.
• 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

NCT00835510 is a completed randomized, quadruple-masked, parallel-group, multiple-site study listed as Phase 1, with enrollment of 548. It compared Taro butenafine cream 1%, Lotrimin Ultra (butenafine) 1%, and vehicle; each was applied for 7 days.

The primary outcome was therapeutic cure at 42 days, requiring both clinical and mycological cure. The registry reports Fisher exact tests comparing each active treatment with vehicle. Both comparisons have higher observed cure counts in the active groups, and unadjusted risk-difference recalculations have 95% confidence intervals above no difference.

The primary efficacy population excluded baseline culture-negative participants and required treatment exposure, follow-up, and day 42 data. The registry record does not report the original sample-size justification, multiplicity strategy, or handling of missing day 42 outcomes. It also does not report an equivalence margin or a direct active-versus-active equivalence analysis.