A Randomized Study Evaluating the Therapeutic Equivalence of Two Butoconazole Nitrate Vaginal Cream, 2% Formulations: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Randomized Study Evaluating the Therapeutic Equivalence of Two Butoconazole Nitrate Vaginal Cream, 2% Formulations (NCT01039584), a randomized na study. The primary outcome is The Test of Equivalence Between the Test and Reference Products Was Based on the Therapeutic Cure Rates at Visit 3/Test-of-Cure..

2. Clinical Question

The trial was randomized, double-masked, and parallel-group. Its stated focus was the efficacy and safety of the generic formulation compared with Gynazole 1, with vehicle control included. The key statistical distinction is between asking whether two products differ and asking whether their outcomes are close enough to meet a prespecified equivalence criterion. The registry record describes the latter question, but the margin and the full decision rules are not reported in the registry record.

3. Trial Design

This was a randomized, double-masked, parallel-group study of butoconazole nitrate vaginal cream, 2%, for vulvovaginal candidiasis. The registry record lists the study as completed, with Padagis LLC as sponsor. It lists phase as NA. Enrollment was 611. The study start is recorded as 2008-02 and primary completion as 2009-09.

There were three arms: Test Product, Reference Product, and Placebo. The test arm received butoconazole nitrate vaginal cream; the reference arm received Gynazole 1 vaginal cream; and the placebo arm received the vehicle of the test product. Each was applied intravaginally once within 48 hours of randomization. The registry record identifies the trial as randomized and double-masked, but details of the randomization procedure, allocation concealment, and who was masked are not reported in the registry record.

The primary outcome was assessed at Visit 3, Day 22-31. Its analysis population was per-protocol, rather than all enrolled participants. The posted primary outcome counts are 137 for the test product, 133 for the reference product, and 67 for placebo. The registry record does not provide a participant flow account explaining the relationship between total enrollment and these analysis counts.

Clinical Cure and Mycological Cure were also posted as secondary outcomes at the same visit. The record includes three reported analyses overall and reports safety figures separately by arm. The protocol, trial registration history, detailed analysis plan, and reasons for any exclusions from the per-protocol population are not reported in the registry record. The available description therefore supports a basic account of the groups, dosing, masking, and outcome timing, but not a reconstruction of all operational or analytic decisions.

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: per-protocol

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 The Test of Equivalence Between the Test and Reference Products Was Based on the Therapeutic Cure Rates at Visit 3/Test-of-Cure., measured over Visit 3: Day 22-31.

The primary endpoint was therapeutic cure at Visit 3, Day 22-31, assessed in the per-protocol population. A participant counted as cured only when both components were present: mycological cure, defined as mycologically proven eradication of infection caused by Candida species, and clinical cure, described as evidence of clinical success. The endpoint therefore combines a laboratory-based assessment with a clinical assessment rather than treating either component alone as sufficient.

A combined outcome can reflect whether both dimensions of cure were achieved at the assessment visit. It also means that failure to meet either component prevents classification as therapeutic cure. Clinical Cure and Mycological Cure were posted separately as secondary outcomes, allowing the components to be considered apart from the composite primary measure.

The study used this endpoint to compare therapeutic cure rates for the test and reference formulations. The primary objective was framed as equivalence, so the relevant question is not merely whether the observed rates are identical or whether a conventional test detects a difference. Equivalence requires judging whether the uncertainty around the comparison lies within a prespecified acceptable range. That margin is not reported in the registry record. The posted counts and recalculated confidence interval describe the observed comparison, but do not by themselves establish the complete equivalence decision rule.

7. Results Posted in the Registry

• Test Product: 53.3% (73/137) versus 54.9% (73/133) on control; risk difference -1.6 percentage points (95% CI -13.5 to 10.3), risk ratio 0.97 (0.78–1.21); unadjusted two-proportion z-test p = 0.792.
• Placebo: 23.9% (16/67) versus 54.9% (73/133) on control; risk difference -31.0 percentage points (95% CI -44.3 to -17.7), risk ratio 0.44 (0.28–0.69); 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.

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:
  • Test Product: 66.4% (91/137) versus 69.2% (92/133) on control; risk difference -2.7 percentage points (95% CI -13.9 to 8.4), risk ratio 0.96 (0.81–1.13); unadjusted two-proportion z-test p = 0.629.
  • Placebo: 47.8% (32/67) versus 69.2% (92/133) on control; risk difference -21.4 percentage points (95% CI -35.7 to -7.1), risk ratio 0.69 (0.52–0.91); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test Product 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 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mycological 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:
  • Test Product: 60.6% (83/137) versus 59.4% (79/133) on control; risk difference 1.2 percentage points (95% CI -10.5 to 12.9), risk ratio 1.02 (0.84–1.24); unadjusted two-proportion z-test p = 0.842.
  • Placebo: 26.9% (18/67) versus 59.4% (79/133) on control; risk difference -32.5 percentage points (95% CI -46.0 to -19.0), risk ratio 0.45 (0.30–0.69); 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 Product 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 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes examine clinical cure and mycological cure separately at Visit 3, Day 22-31. Across these components, the posted pattern is broadly consistent with the primary endpoint in showing similar observed results between the test and reference arms, while the vehicle-control comparisons show lower observed cure counts than the reference comparisons. Considering the two components can help describe whether the combined endpoint's pattern is reflected across its clinical and mycological elements.

These secondary outcomes do not replace the primary therapeutic-cure result. The primary endpoint required both clinical success and mycological eradication, whereas each secondary outcome considered one component. Differences in the separate measures may therefore occur without changing the definition or interpretation of the combined primary outcome. The secondary results add context, but the primary analysis remains the prespecified focus described in the registry record.

The posted secondary p values are unadjusted. When multiple outcomes and comparisons are examined, a result that appears statistically notable can arise by chance more often than when a single comparison is planned. Adjustment or a prespecified hierarchy can help control that concern, but a multiplicity procedure is not reported in the registry record. For that reason, the secondary results are best treated as supportive descriptive evidence rather than as independent confirmatory findings.

The registry record does not report a detailed analysis plan establishing how these outcomes were prioritized, whether any were intended to support a formal claim, or how missing measurements were handled. The consistent broad direction across outcome components can inform interpretation, but it does not resolve the missing multiplicity and analysis-plan details. Nor does it supply the equivalence margin needed to interpret the primary comparison formally.

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

• Clinical Cure
• Mycological Cure

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is counted as having achieved therapeutic cure or not. For a binary outcome, an arm's event count is interpreted alongside the number of participants in that arm. The posted primary results give counts for the per-protocol population. The recalculated risk difference compares the proportion with cure in the test arm with the corresponding proportion in the reference arm, with the direction defined as test minus reference. A negative estimate means the observed test-arm proportion was lower; a positive estimate means it was higher.

What does a risk difference express?

A risk difference is an absolute contrast between two event proportions. Unlike a relative measure, it expresses how far apart the proportions are on the probability scale. A value of zero corresponds to equal observed proportions. The recalculated estimate of -0.016 is the posted unadjusted contrast for the primary comparison. The confidence interval communicates the range of values reasonably compatible with the data under the calculation method. It is not a guarantee that the true difference lies in that particular interval, and it does not incorporate uncertainty about choices that were not included in the calculation.

The registry also displays risk ratios and odds ratios for the comparisons. These are relative measures: a risk ratio compares event proportions as a ratio, while an odds ratio compares the odds of an event. They answer different descriptive questions from the risk difference and can have different numerical behavior. For the primary clinical interpretation, the absolute risk difference is especially direct because it describes the gap in cure proportions. No single effect measure replaces the need to consider the endpoint definition, analysis population, and uncertainty.

How should a confidence interval be read?

A confidence interval describes statistical precision under the assumptions of its method. A narrower interval indicates greater precision for the contrast being estimated; a wider interval leaves more possible values compatible with the data. For the recalculated primary comparison, the interval crosses zero. This means the unadjusted data are compatible with a test rate somewhat lower than the reference rate, a rate somewhat higher, or no difference on the risk-difference scale. Whether the interval is sufficiently narrow for equivalence depends on the prespecified margin, which is not reported in the registry record.

The posted unadjusted p value for the primary recalculation is 0.792. A p value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the model 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. A large p value does not establish equivalence. Equivalence calls for a margin and an analysis designed to determine whether the uncertainty is contained within that margin.

What is different about equivalence analysis?

In an ordinary test for a difference, the null hypothesis commonly represents no difference. In an equivalence framework, the aim is to show that the difference is bounded within acceptable limits on both sides. The acceptable limits are set before examining outcomes. The confidence interval must be considered relative to those limits, not only relative to zero. Since the registry record does not report the equivalence margin or its detailed decision rule, the formal criterion cannot be checked from the posted estimates alone.

The registry's sponsor analysis is labeled as a legacy non-inferiority or equivalence analysis and identifies Wald's method with Yates continuity correction. A continuity correction adjusts a discrete-data approximation when relating counts to a continuous statistical distribution. The record reports a 90% interval for the primary comparison, while the recalculation gives a 95% interval for an unadjusted risk difference. Different confidence levels and methods can produce different intervals. The record does not provide enough detail to infer every element of the sponsor's calculation or its scale from the legacy entry.

Why does the analysis population matter?

The primary outcome is specified for the per-protocol population. This population includes participants meeting the protocol requirements for that analysis, but the registry record does not describe those requirements or the exclusions applied. A per-protocol analysis can differ from an analysis of everyone randomized because its membership depends on post-randomization adherence or evaluability rules. In equivalence studies, population choice can be particularly consequential: interpretation should consider how the prespecified analysis populations and missing outcomes were handled. The full plan is not reported in the registry record, so those checks cannot be reproduced.

The recalculated comparisons are simple unadjusted calculations from posted arm counts. They do not incorporate covariate adjustment or other modeling beyond the stated calculation, and they do not replace the sponsor's reported analysis. Since the discrepancy indicator is false, no disagreement is flagged between the posted sponsor result and recalculation. Even so, the estimates have different stated methods and confidence levels, and should be understood in their respective contexts rather than treated as interchangeable outputs.

What do the secondary comparisons add?

Clinical Cure and Mycological Cure are also binary outcomes. Their risk differences and intervals describe the separate components at the same visit, while therapeutic cure requires both. The individual component results can help describe the pattern underlying the combined endpoint, but they do not redefine the primary outcome. The posted secondary p values are unadjusted. When several outcomes or comparisons are considered, the chance of obtaining an apparently notable result by chance can increase. A multiplicity strategy can address that issue, but one is not reported in the registry record.

Statistical significance, interval precision, and equivalence are related but distinct ideas. A p value is tied to a specified null hypothesis; an interval gives a range of effect sizes compatible with the data under the method; and an equivalence decision depends on whether the interval meets prespecified bounds. Reading all three in the context of the endpoint, population, and analysis plan avoids treating any one statistic as a complete verdict.

11. Confidence Intervals and Precision

The recalculated 95% confidence interval for the primary test-reference risk difference extends from -0.135 to 0.103. Its inclusion of zero means the posted data are compatible with no difference, but also with a negative or positive difference of the sizes covered by the interval. The interval is the clearest concise description of the uncertainty around the unadjusted estimate; the point estimate alone would give an incomplete account.

Precision is limited by the amount of information in the analyzed population and by the frequency of the endpoint. The primary per-protocol counts are 137 in the test arm and 133 in the reference arm, with 73 cures recorded in each. The interval remains broad enough to include differences in both directions. This does not identify which possible value is correct; it describes the uncertainty that remains with these data and this calculation.

The confidence level and method matter. The recalculation reports a 95% interval, whereas the sponsor's legacy analysis reports a 90% interval using Wald's method with Yates continuity correction. Those intervals are not direct substitutes: they use different reported confidence levels and are presented through different analysis summaries. The registry record does not state an equivalence margin, so the interval cannot be judged against the boundary needed for a formal equivalence conclusion.

Confidence intervals quantify sampling uncertainty under their assumptions. They do not account automatically for missing outcomes, selection into the per-protocol population, multiplicity, or uncertainty about an unreported analysis plan. The record does not report enough detail to assess those sources fully. Thus the interval is useful for describing the precision of the posted recalculation, but it is not a complete measure of all uncertainty about the study's conclusions.

12. Planning a Similar Trial: Sample Size

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

The planning estimates describe participants per arm for comparisons between two arms. They are not total enrollment targets for all three arms. The curve and estimates are illustrations based on the observed effect, not the trial's own original design assumptions. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. For non-time-to-event outcomes such as these binary cure outcomes, the estimates count participants per arm; the event-count convention for time-to-event outcomes does not apply.

The 80% power column gives the illustrated participants per arm for a design with an 80% chance of detecting the stated effect under those assumptions, if that effect and assumptions were true. The 90% power column gives the corresponding planning figure for a 90% chance. These are design calculations, not probabilities that the observed result is correct and not measures of the trial's achieved power. This is not observed power.

Planning for 100% of the observed effect uses the full observed contrast as the target effect. Planning for 75% or 50% of the observed effect uses a smaller target contrast. Smaller effects are harder to distinguish from sampling variation, so they require more participants per arm under the same assumptions. The effect fractions are planning scenarios, not claims that those effects are established or expected.

The estimates are illustrative rather than a reconstruction of the original design. The registry record does not report the trial's original sample-size justification or assumptions. The planning figures should therefore be read as conditional estimates tied to the posted observed effects and specified calculation assumptions, not as evidence about the design decisions made for this trial.

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 = 0.549; treatment proportion p₁ = 0.533; average p̄ = 0.541.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7047 = 1.3813.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7047 = 0.5930.
4. n = (1.3813 + 0.5930)² / (-0.0160)² = 15,177.9, rounded up to 15,178 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 <- 0.548872180451128                          # control proportion
p1 <- 0.532846715328467                          # 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(1039584)
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 = 15,178 (80% power), 20,319 (90% power)
 75% of observed effect: n per arm = 26,966 (80% power), 36,099 (90% power)
 50% of observed effect: n per arm = 60,632 (80% power), 81,168 (90% power)
power.prop.test: 15177.9 
Simulated power at n = 15,178 per arm: 0.800 (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 a sponsor analysis for the primary test-reference comparison using Wald's method with Yates continuity correction. It is labeled as a legacy non-inferiority or equivalence analysis and reports a value of 1.5 with a 90% confidence interval from -9.1 to 12.3. No p value is recorded for this primary sponsor analysis. The registry entry does not state the equivalence margin or provide the surrounding protocol decision rule.

The recalculation is a simple unadjusted risk difference from the posted counts, with estimate -0.016, 95% confidence interval from -0.135 to 0.103, and p value 0.792. These results are not identical presentations of one analysis: the registry identifies a sponsor method and 90% interval, while the recalculation is an unadjusted risk-difference analysis with a 95% interval. The record does not make their scales and all calculation details fully comparable.

No discrepancy is flagged between the sponsor result and recalculation. The recalculation can help describe the posted arm counts using an absolute risk contrast, but it should not replace the sponsor's own reported analysis when interpreting the registered equivalence question. At the same time, the sponsor result cannot be fully evaluated against an equivalence criterion without the margin and decision details, which are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and two secondary outcomes, with comparisons involving the test, reference, and placebo arms. It does not report a multiplicity adjustment, testing hierarchy, or other strategy for accounting for the collection of outcomes and comparisons. The secondary p values are unadjusted, so they should not be read as if each had been evaluated in isolation under a fully specified confirmatory plan. No inference about whether an adjustment was used outside the registry record is warranted.

Missing-data handling is not reported in the registry record. The record does not state how missing Visit 3 assessments were treated, whether participants with incomplete components were counted as not cured, or whether any imputation method was used. The posted primary outcome is described as per-protocol, but the record does not give the inclusion rules or explain how participants entered or left that analysis population. These omissions limit assessment of how the reported counts relate to all randomized participants.

The registry reports total enrollment of 611 and separate outcome counts by arm. It does not provide a participant flow account, reasons for exclusions, or arm-specific numbers randomized. As a result, the relationship between enrollment, treatment assignment, safety populations, and the per-protocol efficacy populations cannot be reconstructed fully from the registry record.

The trial's statistical analysis plan, original sample-size justification, interim-analysis details, equivalence margin, and detailed decision criteria are not reported in the registry record. These are important for understanding whether the analysis followed prespecified rules and how equivalence was to be declared. Their absence does not mean that such procedures were not used; it means they cannot be confirmed from the registry record. Interpretation should remain tied to the outcomes and analyses that are actually posted.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry reports zero serious adverse events and zero other adverse events in each listed safety group: Test Product, Reference Product, and Placebo. The corresponding numbers at risk are 246, 243, and 122. These figures describe the posted safety record for those groups; they should not be confused with the per-protocol efficacy counts, which refer to a different outcome population.

The record does not list serious adverse event terms. Death counts are null rather than a reported numeric result, so deaths are not reported in the registry record. A zero recorded event count means no events of that category are posted for the listed group, but it does not by itself establish that the treatments have no risk. The number of participants exposed, the duration and completeness of safety follow-up, and the detailed event collection procedures are not described sufficiently in the registry record to support broader safety conclusions.

These figures are a concise account of what was posted, not a full assessment of comparative safety. The record does not provide event narratives, severity grading, causality assessments, or a detailed account of monitoring. The zero counts should therefore be interpreted narrowly as registry-reported counts rather than as proof that no adverse events could occur.

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

The primary results describe observed therapeutic-cure counts in the per-protocol population and an unadjusted estimate of the difference between test and reference products. The estimate is near zero, but its confidence interval includes values on either side of zero. This combination supports a cautious reading: the posted data do not show a clear difference under the unadjusted comparison, yet the interval does not establish that the products are identical.

The trial was framed as an equivalence study, and equivalence requires more than a nonsignificant difference test. A prespecified margin defines how much difference can still count as equivalent. That margin and the full decision rule are not reported in the registry record, so the formal equivalence conclusion cannot be verified from the available entry alone. The sponsor's legacy analysis is reported, but its result also needs the intended equivalence bounds for a complete interpretation.

The vehicle-control comparison and the secondary outcomes provide additional descriptions of observed outcomes, but they do not change the primary question. The secondary comparisons are unadjusted, and the registry does not report a multiplicity plan. They should not be treated as independent confirmation of the primary equivalence claim.

The results apply to the reported endpoint, visit, analysis population, and study groups. The registry record does not report enough about missing data, participant flow, or analysis-population rules to determine how those factors might affect the estimates. The posted safety counts are also limited to the recorded categories and groups; they do not establish the absence of risk.

Accordingly, the statistical findings can be described as estimates with uncertainty from a randomized, double-masked comparison. They do not by themselves provide a complete account of the protocol, the prespecified equivalence standard, or all aspects of efficacy and safety. No treatment recommendation follows from these registry statistics alone.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical question must match the study's stated objective. Equivalence is not established simply because a conventional test does not detect a difference. It depends on a prespecified margin and on uncertainty being sufficiently limited relative to that margin. Here, the registry identifies equivalence as the primary aim, but the margin is not reported in the registry record. That gap matters because the same estimate and interval can be interpreted differently depending on the acceptable bounds.

The trial also shows why effect estimates and confidence intervals should be read together. The risk difference provides an absolute summary of the primary comparison, while the interval describes the range of values compatible with the unadjusted data under its method. A point estimate close to zero does not remove uncertainty, and a p value does not quantify that uncertainty by itself.

Another statistical issue is the distinction between an analysis population and total enrollment. The primary outcome is per-protocol, while the record gives a larger overall enrollment figure and separate safety denominators. Without participant flow and population definitions, readers cannot fully trace how the analyzed groups were formed. That is particularly relevant when interpreting equivalence, where analysis choices can influence the conclusion.

Finally, secondary outcomes and multiple comparisons need context. Separate clinical and mycological measures provide useful descriptive information, but unadjusted results across several outcomes do not carry the same confirmatory weight as a prespecified primary analysis with a complete statistical plan. This example emphasizes the value of transparent reporting of margins, missing-data procedures, multiplicity decisions, and analysis populations alongside effect estimates.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the equivalence margin, so the formal criterion for deciding whether the test and reference products were sufficiently similar cannot be checked. The sponsor analysis is labeled as an equivalence or non-inferiority legacy analysis, but the record does not supply all details needed to reconstruct its decision rule. The unadjusted recalculation is informative about the posted counts, but it does not substitute for that missing criterion.

The primary outcome uses a per-protocol population. The registry does not describe the population's eligibility rules, the number excluded, reasons for exclusion, or how missing outcome assessments were handled. Total enrollment and outcome-analysis counts are recorded separately, but participant flow is not reported. This limits assessment of selection into the primary analysis and of how representative the analyzed group is of all randomized participants.

The registry reports secondary outcomes and multiple arm comparisons but does not report a multiplicity strategy or detailed outcome hierarchy. The secondary p values are unadjusted. The original sample-size justification, interim-analysis details, and full statistical analysis plan are also not reported in the registry record. Consequently, the planning illustrations based on observed effects should not be mistaken for the trial's original design rationale.

Safety reporting is limited to counts for serious and other adverse events, with no serious terms listed and deaths not reported in the registry record. The entry does not give detailed follow-up, event descriptions, or the methods used to assess attribution. These limitations are specific to the available registry information and do not establish that the omitted procedures or details were absent from the study itself.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Randomized Study Evaluating the Therapeutic Equivalence of Two Butoconazole Nitrate Vaginal Cream, 2% Formulations — NCT01039584.
• Registry record last updated 2023-07-12; status last verified 2023-07.
• Results first posted 2013-01-21.
• 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.

23. Record Summary

NCT01039584 is a completed randomized, double-masked, parallel-group study sponsored by Padagis LLC. It evaluated butoconazole nitrate vaginal cream, 2%, against Gynazole 1 vaginal cream, 2%, and vehicle control for vulvovaginal candidiasis. The registry lists enrollment of 611 and phase as NA.

The primary endpoint was therapeutic cure at Visit 3, Day 22-31, in the per-protocol population. Cure required both mycological eradication and clinical success. The posted recalculation gives a test-reference risk difference of -0.016, with a 95% confidence interval from -0.135 to 0.103 and an unadjusted p value of 0.792. The formal equivalence margin is not reported in the registry record.

Clinical Cure and Mycological Cure were posted as secondary outcomes. Safety records list zero serious and zero other adverse events in the three arms; deaths are not reported in the registry record. The available entry does not include the full analysis plan, missing-data procedures, participant flow, or multiplicity strategy.