A Study of Oral Oteseconazole for the Treatment of Patients With Recurrent Vaginal Candidiasis (Yeast Infection): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Oral Oteseconazole for the Treatment of Patients With Recurrent Vaginal Candidiasis (Yeast Infection) (NCT03562156), a randomized phase 3 study. The primary outcome is Percentage of Subjects With 1 or More Culture-Verified Acute VVC Episodes During the Maintenance Phase of the Study in the Intent-to-Treat Population.

2. Clinical Question

The study addressed recurrence after an initial treatment period. The registry describes a 2-week period treating the current VVC episode with 3 150mg doses of fluconazole, followed by a 12-week period when participants were randomly assigned to oteseconazole or placebo. A 36-week follow-up period followed. The primary outcome therefore concerns recurrent episodes during maintenance, rather than the initial episode treated before the randomized maintenance regimen.

The record also describes an amendment allowing eligible US participants at participating sites to continue in a 48-week observational extension if they completed the initial 48 weeks without a confirmed RVVC episode. That extension was intended to evaluate continued effectiveness; it is not the timeframe specified for the primary outcome. The registry identifies the study as identical to VMT-VT-1161-CL-012 (NCT03561701). No further detail about how the extension was analyzed is reported in the registry record.

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled study with a parallel-group design and triple masking, as recorded in the registry. The sponsor was Mycovia Pharmaceuticals Inc. The study is marked completed. Enrollment was 438. The registry records a start date of 2018-08-16 and a primary completion date of 2020-10-19.

The study evaluated oral oteseconazole (VT-1161) against placebo in participants with recurrent vulvovaginal candidiasis. Both arms are listed with the same dosing schedule: once daily for 7 days starting at Day 1, followed by once weekly for 11 weeks. Before that assigned regimen, the brief summary describes a 2-week treatment period for the current VVC episode with 3 150mg doses of fluconazole. The primary outcome timeframe is maintenance, post-randomization through Week 48, and includes culture-verified acute episodes.

The record describes an optional observational extension for certain US participants at participating sites. Eligibility was described as completing the initial 48 weeks without a confirmed RVVC episode. The extension period lasted 48 weeks and was designed to evaluate continued effectiveness. Its observational status distinguishes it from the randomized placebo-controlled comparison.

The posted primary outcome results list 217 participants for oteseconazole and 109 for placebo. The registry’s enrollment figure is 438, and the primary outcome description says the intent-to-treat population included all randomized subjects. The record does not explain the relationship between enrollment and the arm counts attached to the reported outcome. Details such as the randomization sequence, allocation concealment, site-level procedures, and the original sample-size justification are not reported in the registry record. The record also does not describe any interim analyses or stopping rules.

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.

Before assignment: A total of 438 subjects were enrolled in a 2-week Induction Phase after providing consent. During the Induction Phase, subjects received 3 sequential 150mg of fluconazole administered 72 hours apart. Subjects whose presenting acute VVC (vulvovaginal candidiasis) episode resolved during the Induction Phase (a total of 326) entered a 48-week Maintenance Phase comprised of a 12-week treatment period and a 36-week follow-up period.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on the ITT population which included all randomized subjects. Missing values were imputed with multiple imputation using the following auxiliary information: region, treatment, baseline body mass index, baseline age, ethnicity, and 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 Percentage of Subjects With 1 or More Culture-Verified Acute VVC Episodes During the Maintenance Phase of the Study in the Intent-to-Treat Population, measured over Maintenance phase (post-randomization through Week 48).

The primary endpoint is the percentage of participants with at least 1 culture-verified acute VVC episode during the maintenance phase, defined as post-randomization through Week 48. An episode required a positive fungal culture for Candida species together with a clinical signs and symptoms score of at least 3. The score combined vulvovaginal signs—erythema, edema, and excoriation—and symptoms—itching, burning, and irritation. Each was scored from 0, meaning none, through 3, meaning severe; higher scores indicate worse symptoms or signs.

This endpoint requires both microbiological evidence and a specified level of clinical signs and symptoms. That definition is intended to distinguish a recurrent episode from a symptom report alone or a positive culture alone. The percentage expresses how many participants in each analysis group met the episode definition during the specified period; it does not describe the number of episodes each participant experienced beyond whether at least 1 occurred.

The registry reports values of 6.7% for oteseconazole and 42.8% for placebo. It describes the analysis population as intent-to-treat, including all randomized subjects, and says missing values were imputed using multiple imputation with region, treatment, baseline body mass index, baseline age, ethnicity, and visit as auxiliary information. The registry record does not provide further detail on the endpoint’s handling of repeated episodes or the timing of individual events.

7. Results Posted in the Registry

• Oteseconazole (VT-1161): 6.9% (15/217) versus 43.1% (47/109) on control; risk difference -36.2 percentage points (95% CI -46.1 to -26.3), risk ratio 0.16 (0.09–0.27); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant either had at least 1 qualifying acute VVC episode during maintenance or did not. The registry reports the result as a percentage of participants. For a binary endpoint, a group percentage describes the frequency of participants meeting the event definition; it does not measure event severity or the total number of recurrent episodes.

What does the risk difference describe?

A risk difference is the event proportion in one group minus the event proportion in the comparison group. The posted unadjusted recalculation is -0.362 for oteseconazole relative to placebo. A negative value means the observed event proportion was lower in the oteseconazole group in that calculation. The confidence interval runs from -0.461 to -0.263. Because this interval remains below zero, the range of values compatible with the calculation does not include a zero risk difference. The unadjusted p-value is <0.001.

The values underlying that recalculation are 15 events among 217 participants for oteseconazole and 47 among 109 for placebo. The registry’s displayed outcome percentages are 6.7% and 42.8%, respectively. The record describes multiple imputation for missing values, while the recalculation uses the posted event counts and denominators. These are distinct statistical presentations. The registry does not specify in detail how its displayed percentages were derived, so no more specific reconciliation is possible from the record.

Why can missing-data handling matter?

When an outcome is missing for some participants, the observed records alone may not represent the full analysis population. Multiple imputation is a method that uses observed information to estimate plausible values for missing outcomes across multiple completed datasets, then combines results to reflect imputation uncertainty. This is a general description of the method. The registry says the analysis used multiple imputation and lists region, treatment, baseline body mass index, baseline age, ethnicity, and visit as auxiliary information. It does not report the number or pattern of missing outcomes, the imputation model details, or sensitivity analyses. Those details matter when judging how strongly results depend on assumptions about missingness.

What does the intent-to-treat description mean?

The registry defines the intent-to-treat population as all randomized subjects. In general, intent-to-treat analysis aims to retain participants in their randomized groups, preserving the comparison created by random assignment. The posted arm denominators for the primary outcome are 217 and 109, while enrollment is 438. The registry does not explain the relationship between these figures. It is therefore not possible to infer from the record why the displayed outcome denominators differ from enrollment or how all randomized participants contributed to the posted percentages.

The trial is described as randomized, double-blind, placebo-controlled, parallel-group, and triple-masked. Random allocation is generally intended to make groups comparable at the start of a trial, while masking can reduce the influence of treatment knowledge on care, reporting, and assessment. The registry does not provide procedural detail about how allocation or masking was implemented, so their specific safeguards cannot be evaluated from this record.

What can the p-value and confidence interval tell us?

In general, a p-value evaluates how compatible observed data are with a specified statistical hypothesis, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not indicate the probability that the result arose by chance in an everyday sense. The reported p-value belongs to the unadjusted recalculation. The registry does not report an analysis record specifying a separate model-based test.

A confidence interval gives a range of estimates compatible with the data and calculation method, with its stated confidence level understood through repeated use of that method. It communicates both direction and precision, but is not a guarantee that the true effect lies within a particular observed interval. The interval reflects the unadjusted risk-difference calculation; it does not automatically account for other uncertainties or possible departures from assumptions.

Over-dispersion is a general concern when observed variability exceeds what a statistical model assumes. It is especially relevant to count outcomes or clustered data, where events may be more variable than a simple model allows. The primary endpoint is a participant-level binary outcome, and the registry does not report a model that raises an over-dispersion issue. A specific over-dispersion adjustment is not reported in the registry record.

Overall, the calculations support a descriptive comparison of the recorded event proportions. The registry record contains no posted analysis records and does not report the full prespecified statistical analysis plan, adjustment methods, multiplicity approach, or sensitivity analyses. The unadjusted recalculation should therefore be read as a statistical summary of the posted counts, not as a substitute for an unavailable sponsor analysis plan.

10. Confidence Intervals and Precision

The confidence interval for the unadjusted risk difference is -0.461 to -0.263, with a point estimate of -0.362. This interval quantifies uncertainty in the estimated difference using the unadjusted calculation based on the posted event counts and denominators. Its endpoints are both below zero, indicating that the interval’s values represent a lower event proportion in the oteseconazole group relative to placebo under this calculation.

The interval is useful because it conveys more than the p-value alone: it gives a range of estimated differences compatible with the calculation and makes the direction and scale of uncertainty visible. It does not mean that every value in the interval is equally plausible, nor does it incorporate every source of uncertainty about study conduct, missing outcomes, endpoint classification, or generalizability. The registry’s multiple-imputation description and posted group percentages are additional context, but details needed to assess the influence of missing data are not reported in the registry record.

The point estimate is based on the posted event counts of 15 among 217 participants and 47 among 109 participants. The outcome percentages posted by the registry are 6.7% and 42.8%. The unadjusted recalculation and the registry’s percentages are different statistical displays; the record does not fully explain their relationship. Precision should therefore be interpreted in relation to the unadjusted recalculation rather than assumed to describe any unreported adjusted estimate.

Confidence intervals are not statements about certainty for an individual participant, and they do not establish clinical importance. They describe statistical precision for a group-level estimate under the method used. The registry record does not provide confidence intervals for the displayed arm percentages or a separately reported adjusted estimate.

11. Planning a Similar Trial: Sample Size

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

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

The 80% power column gives the number of participants per arm required under those assumptions for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding number per arm for a 90% chance. These are planning concepts: power describes a design’s ability to detect a specified effect under stated assumptions, not the probability that a particular result is true.

The scenarios include planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The listed figures are 22 and 28 participants per arm for the first scenario, 44 and 58 for the second, and 107 and 142 for the third, in the 80% and 90% power columns respectively. Smaller effects need more participants to detect under otherwise unchanged assumptions, which is why the planning counts rise as the assumed effect becomes smaller.

The estimates are illustrations rather than reconstructions of the trial’s actual enrollment plan. They use the observed effect from this comparison, so they should not be interpreted as observed power or as evidence that the trial was designed with these assumptions.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.431; treatment proportion p₁ = 0.069; average p̄ = 0.250.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6125 = 1.2005.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5564 = 0.4683.
4. n = (1.2005 + 0.4683)² / (-0.3621)² = 21.2, rounded up to 22 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 <- 0.431192660550459                          # control proportion
p1 <- 0.0691244239631336                          # 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(3562156)
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 = 22 (80% power), 28 (90% power)
 75% of observed effect: n per arm = 44 (80% power), 58 (90% power)
 50% of observed effect: n per arm = 107 (80% power), 142 (90% power)
power.prop.test: 21.2 
Simulated power at n = 22 per arm: 0.842 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is identified in the registry, and the outcome description states that missing values were imputed using multiple imputation. The listed auxiliary information was region, treatment, baseline body mass index, baseline age, ethnicity, and visit. The record does not report how many outcome values were missing, the reasons for missingness, the imputation model specification, or sensitivity analyses assessing alternative missing-data assumptions.

The record reports 0 posted secondary outcomes and 0 analysis records. It therefore does not present a set of secondary results from which to assess how many statistical comparisons were tested or whether the primary result was adjusted for multiple testing. A multiplicity plan, including any hierarchy among outcomes or adjustment procedure, is not reported in the registry record. The absence of posted details does not establish that no such planning occurred; it means the record does not document it.

The primary outcome population is described as intent-to-treat and includes all randomized subjects. In general, this approach seeks to preserve randomized assignment for analysis. However, the outcome arms list 217 participants for oteseconazole and 109 for placebo, while enrollment is 438. The registry does not explain why these numbers differ or how missing outcomes and denominators relate to the posted group percentages. The count-based recalculation uses the posted arm denominators; it cannot resolve those documentation gaps.

The registry does not report the original statistical analysis plan, whether the primary endpoint analysis was adjusted for covariates, or whether interim analyses were conducted. The multiple-imputation auxiliary variables are specified, but the detailed analysis model and inferential procedures are not. These omissions limit the ability to reproduce the sponsor’s full analysis or assess all prespecified decisions. The unadjusted recalculation is consequently a separate descriptive statistical summary of posted counts rather than a substitute for the unreported analysis plan.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: appendicitis (0.9%), bronchitis (0.9%), pneumonia (0.9%), vaginal haemmorrhage (0.9%), acute respiratory failure (0.9%).

The registry lists serious adverse events affecting 3 participants in the oteseconazole group, with 217 participants at risk, and 3 participants in the placebo group, with 109 at risk. It lists 129 participants with other adverse events among 217 at risk in the oteseconazole group and 63 among 109 at risk in the placebo group. Deaths are listed as 0 in each group.

These are counts of participants and the corresponding at-risk group sizes as recorded in the adverse-event results. They are not, by themselves, a comparison adjusted for follow-up time, baseline risk, or other factors. The record does not specify in this summary whether events were considered related to treatment, how severity was classified, or the observation period for these adverse-event counts. The serious adverse-event terms listed include Appendicitis, Bronchitis, Pneumonia, Vaginal haemmorrhage, Acute respiratory failure, and Asthma, each reported as 0.9%. The record does not assign these listed terms to particular groups in the summary.

Adverse-event counts should be read as descriptive trial results, not as a complete assessment of comparative safety or an explanation of causation.

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

The posted primary outcome results describe the proportion of participants with at least 1 culture-verified acute VVC episode during maintenance through Week 48. The registry reports 6.7% for oteseconazole and 42.8% for placebo. A separate unadjusted recalculation from the posted event counts estimates a risk difference of -0.362, with a 95% confidence interval from -0.461 to -0.263 and p < 0.001. Together, these values describe a lower observed event proportion in the oteseconazole group in this trial comparison.

The result applies to the defined endpoint and the studied period. A qualifying episode required both a positive Candida culture and a signs and symptoms score of at least 3. The outcome does not summarize every symptom, every culture result, or the total number of episodes per participant. Nor does it describe outcomes beyond the specified maintenance timeframe or the observational extension.

Statistical evidence against a no-difference hypothesis is not the same as proof of a particular mechanism, a guarantee of an individual outcome, or a complete account of clinical importance. The confidence interval describes precision for the unadjusted calculation; it does not remove uncertainty related to missing outcomes, reporting, endpoint assessment, or differences between the registry’s percentage display and the count-based recalculation.

The registry describes randomization and masking, but does not report full implementation details, the original sample-size justification, an interim-analysis plan, multiplicity handling, or a complete statistical analysis plan. It also does not explain the relationship between overall enrollment and the denominators in the primary outcome results. These limits affect how comprehensively the posted results can be evaluated.

The adverse-event figures are descriptive counts and do not establish whether an event was caused by treatment. The available data support a bounded interpretation of the recorded primary endpoint and adverse-event counts in this trial; broader conclusions are not established by these results alone.

16. Why This Trial Matters Statistically

This trial illustrates why a clinical endpoint needs a precise operational definition. A recurrent episode was not defined by symptoms alone: the registry required a positive fungal culture for Candida species and a signs and symptoms score of at least 3. That combined definition makes clear what the primary percentage counts and helps distinguish it from outcomes based only on symptoms or laboratory findings.

The endpoint is binary at the participant level: whether at least 1 qualifying episode occurred during maintenance through Week 48. This makes group proportions and a risk difference natural summaries. The unadjusted recalculation gives an estimate on an interpretable absolute scale, while its confidence interval communicates uncertainty around that estimate. Reading the p-value together with the effect estimate and interval avoids reducing the result to a significance label alone.

The record also demonstrates why analysis details matter. It describes multiple imputation and names auxiliary variables, yet does not give the missingness pattern, imputation model, sensitivity analyses, or full analysis plan. The posted arm percentages differ from the simple proportions represented by the event counts and denominators. Identifying these as different displays, rather than treating them as interchangeable, is important for transparent interpretation.

Finally, planning calculations based on an observed effect are not a substitute for an original design justification. The registry does not report the trial’s original sample-size assumptions, while the planning illustrations explicitly use the observed effect and stated hypothetical assumptions. Keeping those roles distinct helps prevent retrospective planning numbers from being mistaken for evidence about the trial’s design or observed power.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific reporting limitations constrain interpretation. The registry lists enrollment of 438, while the primary outcome results list 217 participants in the oteseconazole group and 109 in the placebo group. Although the outcome description says the intent-to-treat population included all randomized subjects, the record does not explain the relationship between enrollment and the outcome denominators. No explanation should be inferred from the counts alone.

The registry reports primary outcome percentages of 6.7% and 42.8%, and separately posted event counts and denominators that support an unadjusted recalculation. The record does not explain the precise relationship between the reported percentages and that recalculation. It does state that missing values were handled with multiple imputation, but does not report missingness counts, the imputation model, or sensitivity analyses. These gaps prevent a full assessment of how missing-data assumptions affected the reported results.

The registry does not report the original sample-size justification, the full statistical analysis plan, multiplicity procedures, interim analyses, or adjustment methods. It reports no analysis records and no secondary outcome results. Allocation and masking are described, but implementation details are not reported in the registry record.

The primary outcome is restricted to at least 1 qualifying episode during the maintenance phase through Week 48. It does not describe episode counts beyond that threshold or establish outcomes during the separate observational extension. Adverse-event summaries are limited to the posted counts; the registry summary does not specify treatment relatedness or provide sufficient detail to assess event timing. These limitations leave important questions unanswered without negating the descriptive results that are posted.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Study of Oral Oteseconazole for the Treatment of Patients With Recurrent Vaginal Candidiasis (Yeast Infection) — NCT03562156.
• Registry record last updated 2026-02-17; status last verified 2026-01.
• Results first posted 2022-01-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT03562156 is a completed Phase 3 randomized, double-blind, placebo-controlled parallel-group study of oral oteseconazole for recurrent vulvovaginal candidiasis. Enrollment was 438. The primary outcome was the percentage of participants with at least 1 culture-verified acute VVC episode during maintenance through Week 48.

The registry reports primary outcome percentages of 6.7% for oteseconazole and 42.8% for placebo. An unadjusted recalculation from the posted counts gives a risk difference of -0.362 (95% confidence interval -0.461 to -0.263; p < 0.001). Missing values were described as handled by multiple imputation, but further model and sensitivity details are not reported in the registry record.

The registry lists 3 participants with serious adverse events in each group and 0 deaths in each group. Its summary does not provide the full statistical analysis plan, original sample-size justification, or explanation of the difference between enrollment and the primary outcome denominators.