Multi-Center Study of New Medications to Treat Vaginal Infections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Multi-Center Study of New Medications to Treat Vaginal Infections (NCT02308046), a randomized phase 3 study. The primary outcome is Clinical Cure as Assessed by the Investigator at the Test-of-cure Visit.

2. Clinical Question

The trial addresses a direct comparative question: whether investigator-assessed clinical cure differed between participants assigned terconazole vaginal gel and participants assigned gel vehicle. The primary outcome is binary at the participant level: each participant either met the stated cure definition or did not. The posted comparison describes the observed results within the mITT population, rather than establishing what would happen in every population or care setting.

The record describes a randomized, triple-masked, parallel-group phase 3 study. It reports enrollment of 212, while the primary endpoint results are presented for 73 participants in the terconazole arm and 67 in the gel vehicle arm. The record does not explain the relationship between the overall enrollment and the primary analysis counts. It also does not report the planned primary comparison's sample-size justification or the assumptions used in the original trial design.

3. Trial Design

The registry identifies this as a phase 3, randomized, triple-masked, parallel-group study. Participants were assigned to terconazole vaginal gel or gel vehicle. Both arm descriptions specify one applicator full at bedtime. The record names Curatek Pharmaceuticals, LLC as sponsor and gives the study status as completed.

The listed enrollment is 212. The registry gives 2015-06 as the study start and 2017-06 as the primary completion date. These dates describe the recorded study timeline; they do not by themselves establish when individual participants were enrolled or assessed.

The primary endpoint was clinical cure assessed by the investigator at the test-of-cure visit, 7-14 days after beginning treatment. The primary population is described as mITT, defined in the record as participants with a positive baseline yeast culture who used at least one dose of study medication. The endpoint counts are 47 among 73 participants in the terconazole arm and 25 among 67 in the gel vehicle arm.

Randomization supports a comparison between assigned groups, while masking is intended in general to limit influences on assessment and conduct. The record identifies the design as triple-masked but does not describe which roles were masked or how masking was maintained. The method of sequence generation, allocation concealment, or any stratification factors is not reported in the registry record. Nor is the original trial's sample-size calculation or statistical analysis plan reported in the registry record. Those absences limit what can be concluded about design details beyond the elements explicitly recorded.

The number enrolled and the number analyzed for the primary outcome are different registry entries. The record does not report a participant flow explanation that reconciles them, so no reason for the difference should be inferred from the posted counts.

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: mITT population (positive baseline yeast culture and used at least one dose of study medication)

5. Baseline Characteristics

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

Population: modified intent-to-treat (mITT) population includes all subjects randomized to treatment and administered at least one dose of study drug. In addition, subjects must have a positive baseline vaginal fungal culture for Candida species.

6. Primary Endpoint

The registry lists the primary outcome as Clinical Cure as Assessed by the Investigator at the Test-of-cure Visit, measured over 7-14 days after beginning treatment.

The primary endpoint is the number of participants assessed as having clinical cure at the test-of-cure visit. In the record's definition, cure means resolution of all signs and symptoms attributable to vulvovaginal candidiasis. Assessment occurred 7-14 days after beginning treatment. The registry labels the unit as participants and the measure as a count of participants.

This endpoint is used to translate a clinical assessment into a binary outcome for each participant: the stated cure criteria were either met or not met at the assessment. Comparing the proportion meeting the criteria across randomized arms gives an interpretable summary of how often the recorded outcome occurred in each group. It does not describe the degree of improvement among participants who did not meet the full cure definition, and it does not capture outcomes beyond the specified visit.

The registry reports 47 participants with clinical cure among 73 in the terconazole arm, compared with 25 among 67 in the gel vehicle arm. The posted comparison expresses the difference in the observed cure proportions as a risk difference, with a recalculated estimate of 0.271 and a 95% confidence interval from 0.111 to 0.430. The sponsor's reported analysis is a corrected chi-squared comparison, with p = 0.002.

In general, an endpoint's usefulness depends on how clearly it is defined, when it is measured, and how consistently it is assessed. The record provides a clinical definition and assessment window, but further details about assessment procedures and adjudication are not reported in the registry record.

7. Results Posted in the Registry

• Terconazole Vaginal Gel: 64.4% (47/73) versus 37.3% (25/67) on control; risk difference 27.1 percentage points (95% CI 11.1 to 43.0), risk ratio 1.73 (1.21–2.46); 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.

Number of Participants Reporting Complete Resolution of Symptoms by Test of Cure Visit

• 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:
  • Terconazole Vaginal Gel: 61.6% (45/73) versus 43.3% (29/67) on control; risk difference 18.4 percentage points (95% CI 2.1 to 34.6), risk ratio 1.42 (1.03–1.98); unadjusted two-proportion z-test p = 0.030.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Terconazole Vaginal Gel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover improvement or cure of individual and cumulative signs, symptoms, and infection criteria; mycologic cure; complete symptom resolution by the test-of-cure visit; and treatment-emergent adverse events. Four secondary outcomes are identified as posted. The available secondary result detailed in the registry concerns complete resolution of symptoms by the test-of-cure visit, 7-14 days after beginning treatment. Its counts and comparisons are reported separately from the primary clinical-cure outcome.

At a broad level, the posted complete-symptom-resolution result is directionally consistent with the primary comparison: the observed proportion is higher in the terconazole arm than in the gel vehicle arm. However, the sponsor's reported corrected chi-squared analysis for that secondary outcome gives p = 0.088, while the simple unadjusted re-calculation gives p = 0.03. This contrast illustrates why direction and statistical evidence should not be collapsed into a single judgment. The secondary result is less conclusive under the sponsor's reported test than the primary result.

Secondary endpoints provide context about other dimensions of the outcome, but they do not replace the primary endpoint. Clinical cure, complete symptom resolution, mycologic cure, and adverse events are distinct measures; a difference on one does not establish the same pattern for all others. The registry lists several secondary outcome categories, but detailed numerical results for every listed category are not included in the available record. Any broader claim about consistency across all secondary endpoints would therefore go beyond the posted details.

In general, testing multiple outcomes creates a multiplicity concern: the more comparisons made, the greater the chance that at least one appears statistically significant by chance if each is assessed without adjustment. The registry does not report a multiplicity correction or a hierarchy for interpreting secondary outcomes. Consequently, unadjusted secondary p-values carry less confirmatory weight than a clearly prespecified primary analysis. They are most appropriately treated as supportive or exploratory evidence, especially when the statistical plan and multiplicity handling are not reported.

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

• Improvement/Cure of Individual and Cumulative Signs, Symptoms and Criteria for the Infection
• Mycologic Cure
• Number of Participants Reporting Complete Resolution of Symptoms by Test of Cure Visit
• Number of Participants With Treatment Emergent Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant in the mITT population either satisfied the clinical-cure definition at the test-of-cure visit or did not. For binary outcomes, a direct way to compare randomized arms is to estimate the event proportion in each arm and express their contrast. Here, the posted re-calculation uses a risk difference. This is an absolute measure, defined generally as the event proportion in one group minus the event proportion in the comparison group. The reported estimate is 0.271, with arm proportions 0.644 and 0.373.

The risk difference is useful because it keeps the comparison on the same scale as the outcome proportions. A value of zero would mean equal observed proportions; values above or below zero indicate which group has the larger observed proportion according to the comparison's direction. The estimate is not a count of additional cures and should not be interpreted as a forecast for any particular participant. It is a summary of the difference between the observed arm proportions.

The 95% confidence interval for the recalculated risk difference runs from 0.111 to 0.430. In general, a confidence interval describes the range of values compatible with the data under the assumptions of the method. It expresses sampling uncertainty, not the probability that the true value lies in the particular interval after the data are observed. The interval's endpoints do not account automatically for limitations such as missing outcomes, outcome misclassification, or an analysis population that differs from the intended population.

The record also reports relative effect summaries: a risk ratio of 1.725 with an interval from 1.211 to 2.459, and an odds ratio of 3.037 with an interval from 1.525 to 6.048. In general, a risk ratio compares event proportions as a ratio, whereas an odds ratio compares odds. Both are relative measures, and an odds ratio is not the same as a risk ratio. When an outcome is not rare, the two measures can differ appreciably. For that reason, the absolute risk difference and the relative measures should be read as complementary descriptions, not as equivalent statements.

The sponsor's reported primary test is identified as corrected chi-squared, with a superiority analysis and p = 0.002. A chi-squared test is generally used to test whether categorical outcome distributions differ across groups. A correction modifies the test's calculation; the specific correction and any additional details are not reported in the registry record. A p-value describes, under the null hypothesis and test assumptions, how unusual data at least as incompatible with that hypothesis would be. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of the effect.

The posted unadjusted re-calculation gives p = 0.001. It is based on the summary counts and is not a substitute for the sponsor's reported analysis. The registry's discrepancy flag is false. The record does not report enough detail to reconstruct all choices underlying the corrected chi-squared analysis, so the sponsor's reported result remains the appropriate description of the trial's own analysis. The registry does not report whether there were additional covariate-adjusted or stratified analyses for this endpoint.

For binary outcomes, statistical precision is influenced by the amount of information in each arm and by how common the outcome is. In general, more observed participants can narrow an interval, but the amount of improvement depends on the event proportions and analysis method. Unequal numbers in the comparison arms are reflected in the precision of the estimate. It is not appropriate to infer a cause for the primary analysis counts from the overall enrollment alone.

General statistical context: the concept of over-dispersion applies chiefly to count or rate models in which variability exceeds what a chosen probability model expects. The primary measure is a binary participant outcome analyzed with a categorical comparison, and the registry does not report a dispersion estimate or a model requiring an over-dispersion adjustment. No such adjustment should be assumed.

The primary analysis population is explicitly described as mITT: participants with a positive baseline yeast culture and at least one dose of study medication. The record does not report how participants with missing endpoint assessments were handled, whether imputation was used, or whether sensitivity analyses assessed alternative assumptions. It also does not report a detailed statistical analysis plan, prespecified covariates, interim analyses, or multiplicity adjustments. These omissions matter because analysis choices can affect uncertainty and the interpretation of p-values, especially when more than one endpoint is assessed.

Overall, the methods information supports a basic reading of the event counts, the unadjusted effect estimates, and the sponsor's reported categorical test. It does not support a reconstruction of unreported design or analysis decisions. Any interpretation should therefore distinguish explicitly posted results from general statistical explanations and should avoid treating a recalculation as if it were the complete trial analysis.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.271, and its 95% confidence interval is 0.111 to 0.430. The interval describes uncertainty around the unadjusted estimate: values across that range are compatible with the observed data under the calculation's assumptions. Since the interval does not include zero, the re-calculated comparison is consistent with a positive difference in observed clinical cure proportions in the terconazole arm relative to gel vehicle.

The interval still spans a range of possible effect sizes. Its lower and upper bounds are not separate estimates of what happened; they mark the uncertainty around the single point estimate. The estimate is based on 73 participants in the terconazole arm and 67 in the gel vehicle arm, with clinical cure counts of 47 and 25, respectively. Precision is therefore tied to the analyzed counts and the binary outcome, rather than to the enrollment figure alone.

The relative measures have their own intervals: the risk ratio is 1.725, with an interval from 1.211 to 2.459, and the odds ratio is 3.037, with an interval from 1.525 to 6.048. These intervals also exclude their respective null values in the posted recalculation. The relative estimates are expressed on different scales, so their numerical widths cannot be compared directly with the risk-difference interval.

In general, a confidence interval addresses sampling variability under the method used; it does not include every source of uncertainty. The registry does not report enough detail to assess possible effects of missing data, deviations from assigned treatment, or endpoint assessment procedures. The sponsor's reported p-value comes from a corrected chi-squared analysis; confidence intervals for that analysis are not reported in the registry record. The recalculated interval should therefore be read as an unadjusted summary, not as the sponsor's complete inferential result.

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

For this binary participant outcome, the planning figures are participants per arm, not total events. The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the specified effect under the stated assumptions if that effect is the true one. The 90% power column gives the corresponding planning number for a 90% chance. These are design probabilities under assumptions, not guarantees that a study of that size will achieve statistical significance.

The rows use the full observed effect and smaller fractions of it. Planning for 75% of the observed effect requires more participants per arm than planning for the full observed effect; planning for 50% requires more again. This reflects a general feature of study design: smaller differences are harder to distinguish from random variation, so more information is generally needed to detect them at a chosen significance level and power.

For example, planning for 100% of the observed effect gives 53 participants per arm for 80% power and 70 participants per arm for 90% power. Planning for 75% gives 94 and 126 participants per arm, respectively. Planning for 50% gives 211 and 281 participants per arm. These figures are illustrative only and do not establish what assumptions the original investigators used. This is not observed power: it does not measure the probability that the completed trial detected its effect, and it should not be used to reinterpret the observed p-value.

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 = 0.373; treatment proportion p₁ = 0.644; average p̄ = 0.508.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3857.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6806 = 0.5728.
4. n = (1.3857 + 0.5728)² / (0.2707)² = 52.3, rounded up to 53 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 <- 0.373134328358209                          # control proportion
p1 <- 0.643835616438356                          # 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(2308046)
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 = 53 (80% power), 70 (90% power)
 75% of observed effect: n per arm = 94 (80% power), 126 (90% power)
 50% of observed effect: n per arm = 211 (80% power), 281 (90% power)
power.prop.test: 52.3 
Simulated power at n = 53 per arm: 0.786 (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 comparison as a corrected chi-squared test, with a superiority analysis and p = 0.002. This is the trial's own reported inferential result. The registry also displays a simple unadjusted re-calculation from the posted primary endpoint counts: a risk difference of 0.271, a 95% confidence interval from 0.111 to 0.430, and p = 0.001. The discrepancy flag is false.

The re-calculation and sponsor analysis are related but not identical presentations. The re-calculation expresses the arm contrast as an absolute risk difference and uses the posted summary statistics. The sponsor's reported method is a corrected chi-squared test, and the registry does not provide its full computational details or a confidence interval for that analysis. The two p-values should not be treated as exact duplicates or as a reason to replace one analysis with the other.

In general, recalculating from summary counts can be useful for understanding the size and precision of a group difference. It cannot reproduce unreported analysis choices. For the trial's primary inference, the sponsor's own analysis takes precedence when the record identifies a discrepancy; in this record the discrepancy flag is false, and the sponsor analysis remains the reported trial result. Both presentations indicate a difference in the primary outcome, but the risk difference and its interval communicate magnitude and uncertainty more directly than a p-value alone.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is reported as mITT, defined as participants with a positive baseline yeast culture who used at least one dose of study medication. The registry does not report an intention-to-treat analysis population, a per-protocol population, or how participants with missing test-of-cure assessments were handled. It also does not report imputation methods, sensitivity analyses for missing outcomes, or a participant flow account explaining the difference between total enrollment and the endpoint-specific arm counts. These details are important for understanding which participants contributed information and how incomplete observations may affect an estimate.

The registry identifies multiple secondary outcomes and reports primary and secondary comparisons. It does not report whether formal multiplicity control was used, whether endpoints were arranged in a testing hierarchy, or whether the secondary analyses were intended to be confirmatory. In general, assessing multiple hypotheses without adjustment can make nominal p-values less persuasive as evidence for individual secondary findings. This is why the primary endpoint and its prespecified analysis usually carry greater interpretive weight than a set of unadjusted secondary comparisons.

The original statistical analysis plan is not reported in the registry record. In particular, the record does not report covariate adjustment, stratification details, interim analyses, stopping rules, or the original sample-size justification. Absence of these details is not evidence that a procedure was or was not used; it means that the registry record does not establish it.

The study is described as randomized and triple-masked, but allocation sequence methods, concealment procedures, and which parties were masked are not reported. These are design details that can help assess the risk of bias, especially for an investigator-assessed endpoint. The record gives a clinical cure definition, but not the assessment manual, adjudication process, or reliability information. These gaps do not erase the posted counts, but they constrain assessment of how fully the analysis and outcome measurement can be evaluated.

16. 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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse event figures separately from the primary efficacy population. For terconazole vaginal gel, 102 participants were listed as at risk for serious adverse events and 0 as affected. For gel vehicle, 99 were listed as at risk and 0 as affected. The death counts are 0 in both arms. No serious adverse event terms are listed.

The record also reports other adverse events affecting 16 of 102 participants in the terconazole arm and 14 of 99 in the gel vehicle arm. These are reported under the registry's other-adverse-event category and should not be combined with the serious adverse event figures. The record does not provide event-level descriptions or severity details for these other events in the available safety summary.

In general, a zero count in a trial record means no events were recorded in the stated group and safety category; it does not establish that the risk is absent. Safety counts should be read in light of the population monitored, the duration of observation, and how events were collected. The registry does not report enough detail to characterize those aspects fully. These figures describe the posted safety record and should not be used as personalized medical guidance or as a complete account of all possible harms.

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

The primary result shows a higher observed clinical-cure proportion in the terconazole vaginal gel arm than in the gel vehicle arm within the reported mITT population. The investigator-assessed endpoint was defined as resolution of all signs and symptoms attributable to vulvovaginal candidiasis and measured at the test-of-cure visit, 7-14 days after beginning treatment. The recalculated risk difference is 0.271, with a 95% confidence interval from 0.111 to 0.430; the sponsor's corrected chi-squared analysis reports p = 0.002.

These statistics describe the outcome recorded in this trial. They do not mean that every participant in the terconazole arm was cured, that no participant in the vehicle arm was cured, or that the same result would necessarily occur in another population. The counts show outcomes varied within both arms. Nor does the result describe persistence or recurrence beyond the specified test-of-cure visit; later outcomes are not part of the stated primary endpoint.

A statistically significant group comparison does not by itself determine clinical importance. The registry does not state a threshold for a clinically important difference or provide a longer-term outcome that would establish the durability of the observed difference. A confidence interval helps describe uncertainty in the estimated contrast, but does not address every possible source of bias or uncertainty in measurement and analysis.

The record also does not report the original sample-size rationale, missing-data methods, a full statistical analysis plan, or multiplicity handling. These gaps limit independent evaluation of some design and analysis decisions. The reported primary outcome and test remain interpretable as recorded, but conclusions should stay within the outcome, population, and assessment period defined by the registry.

Finally, a trial comparison is not individualized medical advice. The registry statistics describe group-level results in a particular study design and should not be used alone to make decisions about care.

18. Why This Trial Matters Statistically

This trial is statistically informative because it reports a binary clinical outcome with a stated cure definition, a defined assessment window, and counts for both randomized arms. Those details allow the primary comparison to be read on an absolute scale as well as through the sponsor's categorical test. The reported risk difference and confidence interval make magnitude and uncertainty visible, rather than relying on a p-value alone.

The comparison also demonstrates why analysis methods should be kept distinct. The registry's own corrected chi-squared test reports p = 0.002, while the posted unadjusted re-calculation uses a risk difference and reports p = 0.001. The p-values are not the effect itself. The effect estimate indicates the direction and scale of the contrast, while the test addresses compatibility with a no-difference hypothesis under its assumptions. Reading both thoughtfully gives a fuller statistical account.

The secondary outcome results illustrate an additional issue: a directionally similar pattern does not necessarily have the same strength of statistical evidence under every analysis. When multiple outcomes are posted, multiplicity and prespecification affect how much weight to give nominal secondary p-values. The registry does not report those planning details, so restraint is warranted in treating secondary findings as confirmatory.

Finally, the record highlights the value of transparent reporting. It provides the primary population definition and several endpoint statistics, but does not report important information about missing data, analysis planning, allocation procedures, and assessment processes. Recognizing both the information available and the information absent is part of sound biostatistical interpretation.

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.

Several trial-specific limitations of interpretation follow from the registry record. The primary analysis uses the stated mITT population, defined by positive baseline yeast culture and use of at least one dose. The record does not explain how participants outside that analysis population were handled, how missing test-of-cure assessments were treated, or why the endpoint-specific counts differ from the overall enrollment entry. The effect estimate therefore describes the posted analysis group, and the registry does not support a fuller accounting of participant flow.

The primary endpoint is a short-term investigator assessment at 7-14 days after beginning treatment. Although the record defines clinical cure as resolution of all attributable signs and symptoms, assessment procedures, adjudication, and reliability are not described. The outcome does not address later recurrence or durability beyond that visit.

Important trial-design and analysis details are not reported in the registry record: the original sample-size assumptions, detailed statistical analysis plan, allocation sequence and concealment, masking roles, missing-data procedures, interim analyses, and multiplicity handling. Their absence limits independent review; it should not be interpreted as proof that particular procedures were absent from the conduct of the trial.

Safety reporting is also limited in the available summary. Serious adverse event counts and deaths are reported, along with counts in the other-adverse-event category, but detailed descriptions and observation procedures are not available. The posted counts alone cannot characterize the full range, timing, or severity of events.

Finally, the sponsor's test and the unadjusted recalculation are based on different stated presentations. The corrected chi-squared test is the reported trial analysis, while the recalculated risk difference is a simple summary-based comparison. They should be distinguished rather than treated as a reconstruction of the complete analysis plan.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Multi-Center Study of New Medications to Treat Vaginal Infections — NCT02308046.
• Registry record last updated 2020-07-27; status last verified 2020-07.
• Results first posted 2020-07-27.
• 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 record describes NCT02308046, a completed randomized, triple-masked, parallel-group phase 3 study sponsored by Curatek Pharmaceuticals, LLC. Listed enrollment is 212. The study start is 2015-06, and primary completion is 2017-06. Terconazole vaginal gel was compared with gel vehicle, with one applicator full at bedtime specified for each arm.

The primary outcome was investigator-assessed clinical cure at the test-of-cure visit, 7-14 days after beginning treatment, among the mITT population. Clinical cure was defined as resolution of all signs and symptoms attributable to vulvovaginal candidiasis. The reported counts were 47 of 73 in the terconazole arm and 25 of 67 in the gel vehicle arm. The sponsor's corrected chi-squared analysis reports p = 0.002; the unadjusted recalculated risk difference is 0.271, with a 95% confidence interval from 0.111 to 0.430.

Secondary outcomes include symptom resolution, mycologic cure, improvement or cure criteria, and treatment-emergent adverse events. Serious adverse events and deaths were reported as 0 in each arm in the safety summary. The registry does not report several design and analysis details, including missing-data handling, multiplicity procedures, and the original sample-size rationale.