Safety and Equivalence of a Terconazole Vaginal Suppository (Test Product) Compared to the Reference Terconazole Vaginal Suppository in the Treatment of Vulvovaginal Candidiasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Equivalence of a Terconazole Vaginal Suppository (Test Product) Compared to the Reference Terconazole Vaginal Suppository in the Treatment of Vulvovaginal Candidiasis (NCT00803738), a randomized na study. The primary outcome is Proportion of Subjects in Each Treatment Group With Therapeutic Cure.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group study listed as completed. The registry describes the study as investigator-blinded and records single masking. The study compared terconazole vaginal suppositories, 80 mg, as a test product with Terazol terconazole vaginal suppositories, 80 mg, as the reference product. The registry lists the phase as NA.

The recorded enrollment was 572. The study began in 2002-12, and primary completion was recorded as 2003-12. The condition was vulvovaginal candidiasis. The study objective was to compare safety and efficacy in participants with vulvovaginal candidiasis in order to establish bioequivalence. The official title specifies Candida species as the cause of the condition.

The primary efficacy analysis is identified as using the Per Protocol population. The primary outcome counts are reported for 153 participants receiving the test product and 147 receiving the reference product. The registry does not describe why these outcome groups are smaller than the overall enrollment, or how participants were assigned to the Per Protocol population. The original sample-size justification, detailed allocation procedure, and any interim-analysis plan are not reported in the registry record.

The primary outcome was assessed at Visit 3, Day 22-31. Two secondary outcomes were also posted for that visit: mycological cure and clinical cure. The record lists three outcome measures and three analyses, including the primary outcome and these two secondary outcomes. The registry does not specify the analysis population for the secondary outcomes.

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 (PP) population

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 Proportion of Subjects in Each Treatment Group With Therapeutic Cure, measured over Visit 3: Day 22-31.

The primary endpoint is the proportion of participants in each treatment group with therapeutic cure at Visit 3, Day 22-31. The registry defines a therapeutic cure as the combination of clinical cure and mycological cure: a participant had to meet both components. In the posted outcome counts, 105 of 153 participants in the test-product group and 93 of 147 in the reference-product group had therapeutic cure.

This combined endpoint captures two distinct aspects of the study’s stated efficacy question. Clinical cure concerns the clinical component, while mycological cure concerns the mycological component. Requiring both means that a participant who met only one component would not be counted as a therapeutic cure under the registry definition. The secondary outcomes report the two components individually, which can help readers distinguish the combined outcome from either component alone.

Using a proportion makes the outcome directly interpretable as the share of the analyzed group meeting the endpoint. The comparison is expressed as a risk difference, with the reference-product group contrasted against the test-product group. The registry identifies the primary population as Per Protocol. It does not give additional operational criteria for how clinical cure or mycological cure was determined, or explain how missing outcome measurements were handled.

7. Results Posted in the Registry

• Terazol 3 - Terconazole Vaginal Suppositories 80 mg: 63.3% (93/147) versus 68.6% (105/153) on control; risk difference -5.4 percentage points (95% CI -16.1 to 5.4), risk ratio 0.92 (0.78–1.09); unadjusted two-proportion z-test p = 0.327.

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.

Proportion of Subjects With 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:
  • Terazol 3 - Terconazole Vaginal Suppositories 80 mg: 79.6% (117/147) versus 83.0% (127/153) on control; risk difference -3.4 percentage points (95% CI -12.2 to 5.4), risk ratio 0.96 (0.86–1.07); unadjusted two-proportion z-test p = 0.448.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Terazol 3 - Terconazole Vaginal Suppositories 80 mg and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Subjects With 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:
  • Terazol 3 - Terconazole Vaginal Suppositories 80 mg: 68.7% (101/147) versus 76.5% (117/153) on control; risk difference -7.8 percentage points (95% CI -17.8 to 2.3), risk ratio 0.90 (0.78–1.03); unadjusted two-proportion z-test p = 0.131.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Terazol 3 - Terconazole Vaginal Suppositories 80 mg and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary outcomes separate the components that together define therapeutic cure: mycological cure and clinical cure. Across these outcomes, the estimated differences follow the same general direction as the primary comparison, with lower observed proportions in the reference-product group under the comparison’s coding. Their intervals span zero, so they do not resolve the uncertainty about the direction of the group differences.

These secondary results provide context for the combined primary endpoint. A combined outcome can conceal whether one component or both components contribute to the overall pattern; the separately posted outcomes offer a way to see those components. However, they should be interpreted alongside, not in place of, the primary endpoint, which the registry identifies as the primary efficacy measure in the Per Protocol population.

The secondary comparisons are unadjusted. In general, examining several outcomes increases the chance that at least one comparison will appear notable by chance alone. A prespecified hierarchy or multiplicity adjustment can help control that risk. Neither a hierarchy nor an adjustment is described in the registry record. The secondary p-values should therefore carry less confirmatory weight than a result from a clearly prespecified primary analysis with an appropriate decision framework.

The record does not state the analysis population for these secondary outcomes, how missing measurements were handled, or whether the secondary analyses were prespecified in a detailed statistical plan. These omissions limit how much can be inferred from their relationship to the primary result. Taken together, the secondary outcomes are broadly consistent with the primary comparison’s uncertainty, but they do not independently establish equivalence or settle the treatment-group contrast.

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

• Proportion of Subjects With Mycological Cure
• Proportion of Subjects With Clinical Cure

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison is a binary-outcome comparison: each participant either met the registry’s definition of therapeutic cure or did not. The outcome counts are 105 of 153 in the test-product group and 93 of 147 in the reference-product group. The accompanying risk difference compares the reference-product proportion with the test-product proportion. A negative estimate therefore points toward a lower proportion in the reference-product group in this coding, while a positive estimate points toward a higher proportion. The recalculated estimate is -0.054.

What does a risk difference express?

In general, a risk difference is the difference between two event proportions. It keeps the comparison on the same scale as the outcome: a difference of zero corresponds to equal proportions, and values farther from zero indicate a larger absolute separation. Here the posted interval for the primary comparison runs from -0.161 to 0.053. Because it crosses zero, it includes both directions of difference as well as equality. This does not prove that the groups are identical; it reflects uncertainty around the estimate.

How should the p-value be read?

The unadjusted p-value for the primary recalculated comparison is 0.327. In general, a p-value describes how compatible the observed data are with a specified statistical model, assuming that model and its assumptions. It is not the probability that the null hypothesis is true, nor the probability that the products are equivalent. It also does not indicate the clinical importance of a difference. The p-value should be read alongside the effect estimate and its interval, rather than as a stand-alone decision.

The word unadjusted matters because the value is not described as accounting for the other posted outcome comparisons. The registry reports a primary endpoint and two secondary endpoints. When multiple outcomes are tested, the chance of seeing at least one apparently notable result can increase. An adjustment or a prespecified hierarchy can address that issue, but a multiplicity procedure is not reported in the registry record. The posted unadjusted p-values therefore do not, by themselves, constitute a multiplicity-controlled set of confirmatory tests.

What is an interval estimate?

In general, a confidence interval expresses statistical uncertainty around an estimate using a method with a stated coverage level. Its endpoints show a range of values compatible with the data and method; they do not guarantee that the true value lies within that particular interval. For the recalculated primary result, the record does not identify the confidence level attached to the interval. The sponsor analysis separately reports a 90% interval, so that level should not be transferred to the recalculated interval.

The sponsor analysis is described as Wald's method with Yates' continuity. This is the method named in the legacy registry entry. The record gives an analysis value of .05 and a 90% interval from -4.30 to 15.02, but does not describe the value’s role or provide a plain-language conclusion. The reported interval uses a different presentation from the recalculated risk-difference interval. Without further detail about its scale and decision rule, readers should not assume the two intervals are interchangeable.

Why distinguish the sponsor analysis from a recalculation?

The recalculated comparison uses posted summary counts to present a simple, unadjusted risk difference. It is not a reconstruction of every feature of the trial’s original analysis. A sponsor’s prespecified method may incorporate a particular scale, continuity correction, analysis population, or equivalence framework. The registry does not provide enough detail to reproduce that complete framework. Accordingly, the sponsor’s own analysis takes precedence when describing the formal trial analysis, while the recalculation offers a separate view based on the posted counts. The registry does not flag a discrepancy between these results.

For equivalence questions, a failure to find a statistically notable difference is not the same as demonstrating equivalence. In general, equivalence is assessed by comparing an interval against a prespecified margin that defines how large a difference can be while still meeting the equivalence criterion. The registry lists .05 in the sponsor analysis, but its role and interpretation are not explained. The record also does not give the original sample-size justification or fuller statistical plan. Thus, the sponsor’s reported interval and the recalculated difference should be described as posted, without inferring an equivalence conclusion that the registry does not state.

Finally, the primary population is identified as Per Protocol. In general, this population includes participants meeting protocol-defined conditions, but the precise membership rules are specific to the study. Those rules, the handling of missing measurements, and the methods for dealing with protocol deviations are not reported in the registry record. These omissions limit independent assessment of how the analysis population was formed and how robust the result is to alternative analysis choices.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.054, with a posted recalculated interval from -0.161 to 0.053. The interval crosses zero, so the data are compatible with differences favoring either group as well as no difference. Its width signals that the estimate is not highly precise: the possible values span a meaningful range in both directions. The unadjusted p-value of 0.327 is consistent with the uncertainty represented by that interval, but it does not quantify the probability that the products are the same.

The interval for the primary recalculation is not assigned a confidence level in the registry record. It should not be described as a 90% or 95% interval on the basis of the sponsor’s separate reported analysis, which is explicitly given as a 90% interval from -4.30 to 15.02. These are distinct reported analyses, and the record does not explain the scale of the sponsor interval in enough detail to equate it directly with the recalculated risk difference.

For context, the recalculated risk ratio is 0.922, with an interval from 0.783 to 1.085; the odds ratio is 0.787, with an interval from 0.488 to 1.271. In general, ratio measures use a different scale from risk differences, and a value of one corresponds to no relative difference. Both posted intervals include one. No one measure removes the uncertainty visible in the others.

The size of the overall enrollment does not, by itself, describe the precision of this particular estimate. The primary outcome is reported for the Per Protocol population, with the posted group counts of 153 and 147. The record does not explain the difference between these analysis counts and total enrollment or report how missing outcomes were handled. Those details matter when judging the reach and robustness of the estimate.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these binary outcomes, the figures are participants per arm, not total events. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row applies a stated fraction of the observed effect as the effect to detect. The trial’s own sample-size justification is not reported in the registry record.

The 80% power column gives the planned participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect, if that effect and the model assumptions are correct. The 90% power column gives the corresponding number for a design with a 90% chance under the same assumptions. These are planning concepts, not statements about the probability that the trial’s observed result is true. The displayed figures are not observed power.

The rows consider planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so it generally requires more participants. For the primary outcome, planning for 100% of the observed effect gives 1,225 participants per arm for 80% power and 1,640 participants per arm for 90% power. Planning for 75% gives 2,158 and 2,888 participants per arm, respectively; planning for 50% gives 4,806 and 6,434 participants per arm. These are illustrative estimates under the stated assumptions, not a reconstruction of the original trial’s design.

The curve should be read as a visual expression of the same planning relationship between effect size and required sample size, not as an additional analysis of observed outcomes. It depends on the chosen assumptions and does not account for any design features that are 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 = 0.686; treatment proportion p₁ = 0.633; average p̄ = 0.659.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6702 = 1.3135.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6691 = 0.5631.
4. n = (1.3135 + 0.5631)² / (-0.0536)² = 1,224.9, rounded up to 1,225 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 <- 0.686274509803922                          # control proportion
p1 <- 0.63265306122449                          # 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(803738)
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 = 1,225 (80% power), 1,640 (90% power)
 75% of observed effect: n per arm = 2,158 (80% power), 2,888 (90% power)
 50% of observed effect: n per arm = 4,806 (80% power), 6,434 (90% power)
power.prop.test: 1224.9 
Simulated power at n = 1,225 per arm: 0.798 (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 the sponsor’s primary analysis as Wald's method with Yates' continuity. That entry lists an analysis value of .05 and a 90% interval from -4.30 to 15.02. It does not include a p-value or a plain-language statement of the sponsor’s conclusion. The role of the listed value and the precise interpretation of the reported scale are not explained in the registry record.

The recalculated comparison is a simple, unadjusted risk difference from the posted primary counts. It is -0.054, with an interval from -0.161 to 0.053 and an unadjusted p-value of 0.327. These figures offer a direct comparison based on the posted group counts, but they are not a substitute for the sponsor’s stated method or its original analysis framework. The registry record does not flag a discrepancy between the sponsor result and the recalculation.

When characterizing the trial’s formal analysis, the sponsor’s own analysis takes precedence. The recalculation can help readers understand the event proportions and the direction and uncertainty of a straightforward contrast. It cannot establish that the sponsor’s equivalence criteria were met. The record does not clarify the meaning of .05, identify an explicit equivalence margin in explanatory terms, or state whether the sponsor concluded equivalence.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary efficacy outcome and two secondary efficacy outcomes. It reports unadjusted recalculated comparisons for these binary outcomes. No multiplicity adjustment, testing hierarchy, or other approach to controlling the family of outcome tests is reported in the registry record. In general, when several outcomes are assessed, interpreting each unadjusted result as if it were the only test can overstate the strength of evidence. This is one reason the secondary results should be read as supportive context rather than as separate confirmatory findings.

The primary efficacy population is identified as Per Protocol. The criteria defining that population, the number of participants excluded from it, and the reasons for exclusion are not reported in the registry record. The primary outcome group counts are 153 and 147, while overall enrollment is recorded as 572; the record does not explain the difference. The analysis populations for the two secondary outcomes are also not specified.

How missing outcome data were handled is not reported in the registry record. The record does not describe imputation, assumptions about participants without an assessment, or sensitivity analyses for missingness. It also does not report how protocol deviations were handled or whether additional analysis populations were used. These are important details because choices about analysis populations and incomplete outcome data can affect both the estimated proportions and the uncertainty around their comparison.

The registry entry does identify a sponsor analysis method for the primary result and the two secondary results, but a complete statistical analysis plan is not reported. The original sample-size justification, interim analyses, and prespecified decision rules are not reported in the registry record. The listed .05 in the sponsor analysis is not explained, so its role in any multiplicity or equivalence framework cannot be established from the registry entry.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: appendicitis (0.4%).

The registry reports serious adverse events for 0 of 282 participants at risk in the test-product group and 1 of 275 participants at risk in the reference-product group. Appendicitis is listed among the top serious terms at 0.4%. The record does not give additional detail connecting that term to a specific participant or provide a broader narrative assessment of the serious event.

Other adverse events are reported for 48 of 282 participants at risk in the test-product group and 54 of 275 participants at risk in the reference-product group. These are counts of participants affected, as listed in the registry; they should not be confused with the serious-event counts. The record does not provide event-level detail in this summary sufficient to compare the type, timing, or clinical context of all other adverse events.

Deaths are not reported in the registry record. These safety figures describe the posted counts and their listed at-risk groups. They do not establish whether an event was caused by a study product, and they do not by themselves provide a complete assessment of comparative safety.

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

The posted results describe therapeutic cure at Visit 3, Day 22-31 in the Per Protocol population. They show the event counts in each group and an estimated risk difference with an interval that crosses zero. The result is therefore uncertain about the direction and size of the difference. The data do not provide a narrow estimate that would rule out a range of differences in either direction.

Equivalence is a distinct statistical claim from finding no statistically notable difference. In general, equivalence requires a prespecified margin and an analysis showing that the relevant interval lies within that margin. The registry describes the study objective as clinical equivalence and reports a sponsor analysis with a listed value of .05 and a 90% interval, but it does not explain the value’s role or state a plain-language conclusion. The posted summary therefore does not support an independent conclusion about whether the formal equivalence criterion was met.

The results also do not establish that the products are identical. A trial comparison estimates differences with uncertainty; a result that does not clearly separate the groups can reflect limited precision as well as a small underlying difference. The planning illustrations show that, under their assumptions, detecting smaller effects requires more participants, but they are not evidence about the original design or the likelihood that the observed result is correct.

The safety listing reports one serious adverse event in the reference-product group and none in the test-product group, alongside other adverse-event counts. Those figures are descriptive and do not establish causation or a complete comparative safety profile. Missing-data procedures, analysis-population details beyond the primary Per Protocol label, and full statistical decision rules are not reported in the registry record.

Overall, the registry presents a randomized comparison and outcome counts that can be described statistically, but the available record leaves important uncertainty about the equivalence framework and analysis details. The findings should be understood as the posted estimates and their precision, not as medical advice or a treatment recommendation.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical-equivalence question cannot be answered merely by asking whether a conventional difference test produces a small p-value. The primary recalculated p-value is 0.327, but that value does not establish equivalence. Equivalence depends on a prespecified margin and the position of an appropriate interval relative to that margin. Although the registry describes the study as designed to evaluate clinical equivalence, it does not explain the sponsor analysis value of .05 or state the sponsor’s conclusion in plain language.

The study also shows the value of separating an outcome’s point estimate from its precision. The primary estimate is a risk difference, and its interval spans zero and values on either side. Reporting the estimate together with the interval conveys more than a binary declaration of statistical significance: it shows the direction of the point estimate and the range of uncertainty. The separate mycological and clinical outcomes add context to a primary endpoint that requires both components.

Another statistical issue is the distinction between an original trial plan and a retrospective planning illustration. The displayed sample-size calculations use the observed effect and stated assumptions. They help explain how required sample size changes when the target effect changes, but they do not explain how the trial’s enrollment target was chosen. The original sample-size justification is not reported in the registry record.

Finally, interpretation depends on transparency about populations, missing data, and multiple outcomes. The primary population is identified as Per Protocol, but its detailed criteria and missing-data handling are not reported. The two secondary outcomes are unadjusted, with no multiplicity procedure described. These limitations matter because statistical conclusions rely not only on the arithmetic of an effect estimate, but also on the design and analysis choices that define what the estimate represents.

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 leaves several trial-specific details unclear. Overall enrollment is 572, whereas the posted primary outcome counts are 153 in the test-product group and 147 in the reference-product group. The primary analysis is identified as Per Protocol, but the record does not explain why the outcome counts are smaller than enrollment, how participants entered that analysis population, or why participants were not represented in the posted outcome counts.

The registry does not report the operational definitions or assessment procedures for clinical cure and mycological cure beyond stating that both were required for therapeutic cure. It also does not describe how missing outcome measurements were handled, the criteria for protocol deviations, or the analysis populations for the secondary outcomes. These omissions limit independent evaluation of the endpoint and the robustness of the reported comparisons.

The sponsor’s analysis is named as Wald's method with Yates' continuity, and a 90% interval is reported. However, the role of the listed value .05 and the scale of the reported interval are not explained in plain language. The record does not provide the complete statistical plan, a clearly explained equivalence margin, or a sponsor conclusion about whether equivalence was established. The original sample-size justification and any interim analyses are not reported in the registry record.

Two secondary efficacy outcomes are posted, but the record does not report a multiplicity adjustment or testing hierarchy. Their unadjusted comparisons should therefore be interpreted cautiously. Safety information is also presented as counts, with limited event-level detail; deaths are not reported in the registry record. These limitations do not invalidate the posted results, but they constrain how far the available summary can support conclusions about efficacy, equivalence, and comparative safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Equivalence of a Terconazole Vaginal Suppository (Test Product) Compared to the Reference Terconazole Vaginal Suppository in the Treatment of Vulvovaginal Candidiasis — NCT00803738.
• Registry record last updated 2021-10-13; status last verified 2021-10.
• Results first posted 2013-02-20.
• 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

The registry describes a completed randomized, parallel-group, investigator-blinded study comparing terconazole vaginal suppositories, 80 mg, as a test product with Terazol 3 terconazole vaginal suppositories, 80 mg, as the reference product. Enrollment was 572. The primary outcome was therapeutic cure at Visit 3, Day 22-31, defined as both clinical and mycological cure, and the primary analysis population was Per Protocol.

The posted primary counts were 105 of 153 in the test-product group and 93 of 147 in the reference-product group. The recalculated risk difference was -0.054, with an interval from -0.161 to 0.053 and an unadjusted p-value of 0.327. The registry also reports two secondary outcomes and descriptive adverse-event counts. The sponsor’s primary analysis is reported as Wald's method with Yates' continuity, with a 90% interval from -4.30 to 15.02 and a listed value of .05; the record does not explain that value or state a plain-language equivalence conclusion.