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 (NCT02308007), a randomized phase 3 study. The primary outcome is Clinical Cure of Mixed Infection (BV and VVC) as Assessed by the Investigator at the Test-of-cure Visit.

2. Clinical Question

3. Trial Design

The registry describes a randomized, triple-masked, parallel phase 3 study of vaginal gels for vaginal infection. It is marked completed, lists enrollment of 475, and identifies Curatek Pharmaceuticals, LLC as sponsor. Its title describes a multi-center study, but the number and locations of centers are not reported in the registry record. The dates listed are 2015-06 for study start and 2018-06 for primary completion.

Three treatment groups are listed: terconazole vaginal gel, metronidazole vaginal gel, and terconazole/metronidazole vaginal gel. Each arm description specifies one applicator full at bedtime. The record does not report the treatment duration, whether additional treatment instructions differed by group, the allocation ratio, or details of random sequence generation and allocation concealment. Triple masking is recorded, but which roles were masked and how masking was maintained are not reported in the registry record.

The primary endpoint is investigator-assessed clinical cure of mixed BV and VVC at the test-of-cure visit, 7-14 days after beginning treatment. Its analysis population is defined as participants meeting the stated baseline BV and yeast-culture criteria who used at least one dose of study medication. The arm denominators for this endpoint are 83.0 for terconazole, 84.0 for metronidazole, and 82.0 for the combination. They are outcome-specific denominators and should not be substituted for the overall enrollment figure.

The registry lists secondary outcomes covering cure of the BV and VVC components, microbiologic and mycologic cure, symptom resolution, and treatment-emergent adverse events. Statistical details such as the planned primary analysis, multiplicity strategy, missing-data procedure, and original sample-size justification are not reported in the registry record. The term phase 3 describes the trial phase; it does not supply those missing design details.

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 (Baseline Nugent Gram stain score of 4 or more, and 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 Nugent score of 4 or more on Baseline visit Gram stain slide and a Baseline visit yeast culture positive for Candida species.

6. Primary Endpoint

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

The primary endpoint counts participants whom the investigator assessed as having clinical cure of both BV and VVC at the test-of-cure visit, scheduled 7-14 days after beginning treatment. The outcome is a joint clinical endpoint: a participant must satisfy the BV definition and also have resolution of all signs and symptoms attributable to VVC. For BV, the record specifies that discharge has returned to normal or physiologic, the whiff test is negative, and the saline wet mount has <20% clue cells. For VVC, the definition is resolution of all attributable signs and symptoms.

A joint endpoint is relevant to a mixed infection because it asks whether both components are clinically resolved at the same assessment, rather than whether only one component improves. That makes it directly aligned with the stated purpose of evaluating the combination treatment against the two single-entity treatments. It also means that the result cannot be interpreted as a general measure of cure for either infection considered alone; the component outcomes are reported separately as secondary outcomes.

The endpoint is assessed at a particular post-treatment time, not over long-term follow-up. It is a count of participants meeting the cure definition in each arm, with the comparison expressed in the recalculation as a risk difference. The registry record does not report how investigators adjudicated ambiguous findings, how missing test-of-cure assessments were handled, or whether the primary endpoint was assessed by any reviewer independent of the investigator.

7. Results Posted in the Registry

• Metronidazole Vaginal Gel: 34.5% (29/84) versus 37.3% (31/83) on control; risk difference -2.8 percentage points (95% CI -17.4 to 11.7), risk ratio 0.92 (0.62–1.39); unadjusted two-proportion z-test p = 0.704.
• Terconazole/Metronidazole Vaginal Gel: 52.4% (43/82) versus 37.3% (31/83) on control; risk difference 15.1 percentage points (95% CI 0.1 to 30.1), risk ratio 1.40 (0.99–1.99); unadjusted two-proportion z-test p = 0.051.

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.

Cure of the BV Component of Mixed Infection

• 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:
  • Metronidazole Vaginal Gel: 54.8% (46/84) versus 45.8% (38/83) on control; risk difference 9.0 percentage points (95% CI -6.1 to 24.1), risk ratio 1.20 (0.88–1.62); unadjusted two-proportion z-test p = 0.246.
  • Terconazole/Metronidazole Vaginal Gel: 65.9% (54/82) versus 45.8% (38/83) on control; risk difference 20.1 percentage points (95% CI 5.2 to 34.9), risk ratio 1.44 (1.09–1.91); unadjusted two-proportion z-test p = 0.009.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Metronidazole Vaginal Gel and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Terconazole/Metronidazole Vaginal Gel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Cure of the VVC Component of Mixed Infection

• 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:
  • Metronidazole Vaginal Gel: 44.0% (37/84) versus 62.7% (52/83) on control; risk difference -18.6 percentage points (95% CI -33.5 to -3.7), risk ratio 0.70 (0.52–0.94); unadjusted two-proportion z-test p = 0.016.
  • Terconazole/Metronidazole Vaginal Gel: 64.6% (53/82) versus 62.7% (52/83) on control; risk difference 2.0 percentage points (95% CI -12.7 to 16.7), risk ratio 1.03 (0.82–1.30); unadjusted two-proportion z-test p = 0.791.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Metronidazole Vaginal Gel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Terconazole/Metronidazole Vaginal Gel and the control. The interval gives the range of effects that remain compatible with the data.

Microbiologic and Mycologic Cure

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Metronidazole Vaginal Gel: 6.0% (5/84) versus 22.9% (19/83) on control; risk difference -16.9 percentage points (95% CI -27.3 to -6.6), risk ratio 0.26 (0.10–0.66); unadjusted two-proportion z-test p = 0.002.
  • Terconazole/Metronidazole Vaginal Gel: 29.3% (24/82) versus 22.9% (19/83) on control; risk difference 6.4 percentage points (95% CI -7.0 to 19.7), risk ratio 1.28 (0.76–2.15); unadjusted two-proportion z-test p = 0.351.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Metronidazole Vaginal Gel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Terconazole/Metronidazole Vaginal Gel and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide a broader view of the two infection components and of microbiologic or mycologic findings. Their overall pattern is not a single uniform confirmation of the primary joint clinical endpoint: component-specific outcomes address only part of the mixed-infection question, and the microbiologic and mycologic outcome uses a different type of assessment. These outcomes can help describe where observed differences arise, but they do not replace the primary endpoint’s requirement for clinical cure of both components.

The registry reports recalculated comparisons for cure of the BV component, cure of the VVC component, and microbiologic and mycologic cure. Sponsor-reported tests are available for the two component-cure outcomes, while no sponsor-reported test is listed for microbiologic and mycologic cure. The numerical results and their endpoint-specific uncertainty should be read in their respective outcome displays rather than treated as a common summary estimate. No result for complete symptom resolution or treatment-emergent adverse events is reported in the registry record as a secondary outcome result.

Secondary endpoints often have a supportive or exploratory role, especially when the record does not describe a prespecified testing hierarchy or multiplicity adjustment. Testing several endpoints and pairwise comparisons creates more opportunities for nominally small p-values by chance. The registry record does not report how that issue was addressed. Consequently, an isolated secondary p-value should carry less weight than a well-specified primary analysis with documented error control. The secondary findings can inform interpretation of the clinical pattern, but they do not independently settle the primary question.

There is also overlap among outcomes: clinical cure of the mixed infection depends on both components, while the component outcomes and laboratory-related outcome capture related but nonidentical features. Agreement across measures can be informative, but disagreement is not necessarily contradictory because the definitions and assessment types differ. The record does not provide enough methodological detail to assess whether all secondary outcomes were prespecified, how missing assessments were handled, or whether the reported secondary analyses were adjusted.

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

• Cure of the BV Component of Mixed Infection
• Cure of the VVC Component of Mixed Infection
• Microbiologic and 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

What is being compared?

The primary outcome is binary: each participant either meets the clinical-cure definition at the test-of-cure visit or does not. The posted counts are compared for the combination gel against terconazole gel and, separately, against metronidazole gel. The recalculated effect measure is a risk difference: the estimated event probability in the combination arm minus the estimated event probability in the comparator arm. Positive values indicate a higher observed cure proportion in the combination group, while negative values indicate a lower observed cure proportion. This is a general explanation of the measure; it does not make the comparison adjusted for any baseline factors.

The recalculation uses the arm-level event counts and denominators in the registry record. It is unadjusted, so it does not incorporate covariates, stratification, or any analysis features that may have been used by the sponsor. Its confidence intervals and p-values belong to that recalculation and must be kept separate from the sponsor-reported tests.

What do the reported tests describe?

The registry reports corrected chi-squared tests and Cochran-Mantel-Haenszel tests for the primary comparisons. A chi-squared test assesses whether the observed event distributions differ between the groups under the test’s assumptions. The label corrected indicates a correction within the chi-squared procedure; the record does not explain the exact implementation. The word corrected should not be taken as evidence that the sponsor adjusted for multiple comparisons.

A Cochran-Mantel-Haenszel test is generally used to compare groups while accounting for strata. In general, stratification can allow a comparison to account for grouping factors, rather than treating all observations as if they came from a single undivided set. The registry record does not identify the strata used, explain how they were selected, or provide estimates adjusted by that method. Consequently, the reported Cochran-Mantel-Haenszel p-values can be stated, but their precise adjustment cannot be reconstructed from this record.

For the combination-versus-metronidazole primary comparison, the registry reports p = 0.030 for the corrected chi-squared test and p = 0.020 for the Cochran-Mantel-Haenszel test. For combination versus terconazole, it reports p = 0.073 and p = 0.049, respectively. A p-value is a measure of how compatible the observed data are with a specified null model under the chosen analysis; it is not the probability that the null hypothesis is true, nor does it quantify the chance that the finding is due to bias. Different tests can give different p-values because they use different procedures or assumptions.

Why keep recalculations separate?

The risk differences, confidence intervals, and unadjusted p-values are recalculated from posted arm summaries. The registry also contains sponsor-reported analyses. When these differ, they should not be presented as if they were interchangeable estimates from one analysis. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence. The recalculation remains useful as a transparent, simple comparison of the posted counts, but it is not a substitute for the sponsor’s planned or adjusted analysis. The original statistical analysis plan is not reported in the registry record.

Confidence intervals describe a range of estimates compatible with the data and the method, subject to its assumptions. For a risk difference, an interval spanning zero is compatible with no difference as well as effects in either direction; an interval entirely on one side of zero is less compatible with a zero difference under that interval procedure. This is a general interpretation, not a statement that the interval captures every source of uncertainty. In particular, it does not incorporate unreported design choices, missing-data handling, or multiplicity adjustments.

What assumptions are not documented?

The registry identifies the mITT population and its baseline criteria, but does not report the complete analysis plan, the primary test chosen in advance, whether analyses were stratified in advance, or the rules for handling missing endpoint data. It also does not report whether the trial used interim analyses or a prespecified hierarchy for testing endpoints. These details matter because choices made after observing results can affect how nominal p-values should be interpreted. Their absence does not prove that no such procedures existed; it means they are not reported in the registry record.

Multiplicity is a particular concern when more than one comparison or endpoint is evaluated. If many hypotheses are tested without an adjustment or an ordered testing plan, the chance of at least one nominally small p-value can increase. This is a general statistical issue. The record does not provide enough information to determine whether the sponsor controlled that risk across the two primary comparisons and the secondary outcomes. Accordingly, individual p-values should be read as results of their named analyses, not as a complete account of confirmatory error control.

Finally, the primary endpoint joins clinical assessments for two different infection components and is evaluated at one test-of-cure visit. Its interpretation depends on the definitions in the registry and the integrity of outcome assessment. The record does not describe independent adjudication or missing-visit rules. The posted data therefore support an account of the specified endpoint and comparisons, but not claims about unreported procedures or outcomes beyond the defined assessment.

11. Confidence Intervals and Precision

The recalculated primary risk difference for combination treatment versus terconazole has a confidence interval from 0.001 to 0.301. Its lower bound is just above zero, so the unadjusted interval excludes zero only narrowly. The associated unadjusted p-value is 0.051. This combination of a near-zero lower bound and a p-value close to the conventional 0.05 reference indicates limited precision about the size of the difference, even though the estimated direction favors the combination group in this recalculation.

For combination treatment versus metronidazole, the recalculated risk-difference interval runs from -0.174 to 0.117 and includes zero. Its unadjusted p-value is 0.704. The interval allows for a difference in either direction, including no difference, so the posted summary data do not estimate this comparison precisely enough to rule out a range of possibilities under the unadjusted method.

In general, a confidence interval communicates uncertainty in an estimate, conditional on the statistical method and its assumptions. It is not a guarantee that the true effect lies within the interval, and it does not account automatically for bias, missing data, measurement error, or multiple testing. The intervals are from unadjusted recalculations, not the sponsor’s reported analyses. The sponsor’s reported p-values arise from different named methods and do not provide confidence intervals in the registry record.

The arm denominators and event counts are modest in relation to the wide range of effects encompassed by these intervals. That context argues against reading a single point estimate as a precise measure of effect. In addition, the near-threshold result for one recalculated comparison is sensitive to analysis method: the sponsor’s corrected chi-squared test and Cochran-Mantel-Haenszel test report different p-values. The record does not include sponsor confidence intervals that would allow the precision of those analyses to be described in the same terms.

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 display is a planning illustration based on the observed effect, not a report of the original trial’s design calculations. Each row represents planning for a stated fraction of the observed effect. Read the 80% power column as the number of participants per arm that the stated planning procedure estimates would be needed for an 80% chance of detecting that effect under its assumptions. The 90% power column uses the same interpretation but targets a higher chance of detection. These are planning scenarios, not observed power.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For these non-time-to-event outcomes, the figures are participants per arm, not total participants across arms. The record’s general note distinguishes time-to-event planning figures, which would be total events, but the outcomes are not time-to-event outcomes. The original trial sample-size justification and its original design assumptions are not reported in the registry record.

The scenarios show why assumed effect size matters: planning for 75% of the observed effect requires more participants per arm than planning for 100%, and planning for 50% requires more still. This is a general feature of power calculations: smaller effects are harder to distinguish from random variation, so more information is typically needed. The very large requirements in some rows also reflect that the observed difference used as a planning basis may be small. Such values are illustrative estimates conditional on the stated assumptions, not guarantees that a future trial would achieve its target.

The sample-size calculations are not evidence that the completed study was adequately or inadequately powered. They are not observed power, and they do not reveal what the sponsor originally expected, what effect was considered clinically meaningful, or whether the trial used a different analysis plan. They should be read as conditional planning examples tied to the recalculated observed effects.

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 = 0.345; average p̄ = 0.359.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6786 = 1.3300.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6783 = 0.5708.
4. n = (1.3300 + 0.5708)² / (-0.0283)² = 4,525.4, rounded up to 4,526 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 <- 0.373493975903614                          # control proportion
p1 <- 0.345238095238095                          # 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(2308007)
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 = 4,526 (80% power), 6,058 (90% power)
 75% of observed effect: n per arm = 8,081 (80% power), 10,817 (90% power)
 50% of observed effect: n per arm = 18,258 (80% power), 24,441 (90% power)
power.prop.test: 4525.4 
Simulated power at n = 4,526 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses using corrected chi-squared and Cochran-Mantel-Haenszel tests. For the primary comparison of combination gel with metronidazole gel, the reported p-values are 0.030 and 0.020, respectively. For combination gel with terconazole gel, they are 0.073 and 0.049. These are the sponsor-reported analyses and should be kept distinct from the simple unadjusted recalculations.

The recalculated primary risk differences use only the posted event counts and denominators. They yield p = 0.704 for combination versus metronidazole and p = 0.051 for combination versus terconazole, with their own unadjusted confidence intervals. The different results may reflect analysis procedures beyond the unadjusted comparison, but the registry record does not provide sufficient detail to identify the reason for each difference. The Cochran-Mantel-Haenszel method, for example, is reported by name, but its strata are not described.

Because the record flags a discrepancy, the sponsor’s own analysis takes precedence. This means the recalculation should be presented as a transparent secondary check on the posted summaries, not as a correction that replaces the sponsor’s result. The record does not report the full statistical analysis plan or sponsor confidence intervals for these comparisons, so those aspects cannot be independently reconciled from the posted information.

15. Multiplicity, Missing Data and Analysis Populations

There are two primary pairwise comparisons: combination gel against terconazole gel and combination gel against metronidazole gel. The registry also lists several secondary outcomes. This creates a multiplicity question: if each comparison is judged independently at a nominal threshold, the overall chance of at least one false-positive result can be higher than for a single test. In general, multiplicity can be addressed through procedures such as adjusted thresholds or an ordered testing strategy, but the registry record does not report whether either approach was used. The label corrected in the chi-squared method does not establish that multiplicity was corrected.

The posted primary population is mITT, defined by baseline Nugent Gram stain score of 4 or more, positive baseline yeast culture, and use of at least one dose of study medication. That definition identifies who is included in the reported primary analysis, but it does not describe how participants were handled if they lacked a test-of-cure result or had incomplete data. Missing-data rules, imputation, sensitivity analyses, and participant disposition by reason are not reported in the registry record. The posted arm denominators should therefore be interpreted as outcome-specific analysis denominators, not as a full account of enrollment and follow-up.

The registry names corrected chi-squared and Cochran-Mantel-Haenszel methods for primary comparisons, and corrected chi-squared tests for some secondary comparisons. It does not report the full statistical analysis plan, the exact correction used, the stratifying factors for the Cochran-Mantel-Haenszel tests, or whether these methods were specified before outcomes were examined. It also does not report interim analyses or stopping rules. These details cannot be inferred from the methods labels alone.

Masking is recorded as triple, but the roles masked and procedures for preserving masking are not described. The record also does not report how the investigator’s clinical assessments were standardized or whether outcomes were independently adjudicated. These are relevant to interpreting clinical endpoints, but the absence of documentation is not evidence that safeguards were absent. It means their operation cannot be evaluated from the registry record.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diabetes mellitus inadequate control (0.7%).

The serious adverse event figures are reported separately by treatment group. The registry lists 1 serious adverse event among 149 participants at risk in the terconazole group, 0 among 151 in the metronidazole group, and 0 among 154 in the combination group. The record lists zero deaths in each group. It identifies Diabetes mellitus inadequate control as a top serious event term, with 0.7% shown.

These figures describe the recorded serious-event counts and the corresponding at-risk denominators. They do not establish whether an event was caused by a study treatment, and the registry record does not provide event-level narratives, timing, duration, or a detailed assessment of relatedness. Zero recorded serious events in a group does not mean that all possible harms were excluded; it means no serious events were recorded for that group in this registry summary.

The broader registry summary also lists other adverse events, but those figures are not serious-event counts and should not be combined with the serious-event figures. The record’s secondary-outcome list includes treatment-emergent adverse events, while a result for that secondary outcome is not reported in the registry record. These summaries therefore provide limited safety information and do not support a complete comparison of harms.

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

The posted data describe a randomized comparison of three vaginal-gel treatment groups in a defined mITT population with baseline evidence of both BV and yeast infection. At the test-of-cure visit, the combination arm has the largest posted count of participants meeting the clinical-cure definition. The sponsor’s reported tests and the unadjusted recalculations do not give identical statistical results, particularly for the comparison with terconazole. The discrepancy flag means the sponsor’s analyses take precedence over the recalculation, while the recalculation remains useful for understanding the posted counts and its own uncertainty.

The result does not, by itself, establish that the combination treatment is superior in every clinically relevant sense. The registry reports p-values from named tests but does not report sponsor confidence intervals for the primary comparisons, a multiplicity plan, or the full analysis plan. The recalculated interval for combination versus terconazole is close to zero at its lower end, while the interval for combination versus metronidazole includes zero. These are method-specific summaries of uncertainty, not measures of clinical importance.

The endpoint concerns clinical cure of both infection components at a test-of-cure visit 7-14 days after beginning treatment. It does not establish longer-term outcomes, effects in people who do not meet the stated baseline criteria, or results for either component alone. Secondary outcomes offer related information but do not erase the distinctions among joint clinical cure, component cure, and microbiologic or mycologic assessment.

The registry’s safety summary records serious adverse events and deaths by group, but it does not provide enough detail to determine causality or fully characterize non-serious harms. The secondary treatment-emergent adverse-event result is not reported in the registry record. Taken together, these data support a careful description of the trial’s posted outcomes, with substantial limits on conclusions beyond the measured population, endpoints, follow-up time, and analyses.

18. Why This Trial Matters Statistically

This trial illustrates several statistical issues that arise in randomized studies with multiple treatment comparisons. The primary question is a joint clinical endpoint, while the treatment groups create two separate comparisons against single-agent therapies. Those comparisons may produce different estimates and p-values, and they should not be condensed into a claim that the combination is uniformly better or worse. The sponsor’s tests and unadjusted recalculations also demonstrate why the named analysis method matters.

The comparison against terconazole is particularly instructive about precision and threshold-based interpretation. The unadjusted interval barely excludes zero, and its p-value is close to the conventional reference value, while the sponsor’s reported tests differ from one another. This makes it important to consider the effect estimate, uncertainty, analysis method, and prespecified plan together, rather than treating a threshold as a definitive dividing line. For the metronidazole comparison, the recalculated interval spans zero, while sponsor-reported tests give different p-values from the recalculation.

The mixed-infection endpoint also shows why component outcomes are useful but not interchangeable with a composite clinical outcome. Separate component results may explain the pattern behind the joint endpoint, yet each answers a narrower question. Multiple secondary tests raise the additional issue of multiplicity, which cannot be resolved from the registry record because the testing strategy is not reported.

Finally, the planning illustrations show how future sample-size requirements depend on assumptions about the effect to detect. They are not evidence about observed power or the trial’s original design. Overall, the record offers a case study in distinguishing descriptive counts, unadjusted recalculations, sponsor analyses, endpoint definitions, and planning calculations.

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 primary analysis population is restricted to participants with specified baseline test findings who used at least one dose. Results may not apply to participants outside those criteria, and the record does not give a full account of screening, exclusions, or missing test-of-cure assessments. Although overall enrollment is listed, it does not substitute for outcome-specific denominators or describe how enrollment flowed into the mITT analysis.

The primary endpoint combines clinical definitions for BV and VVC and is assessed at one test-of-cure visit. The record does not report how ambiguous clinical assessments were handled, whether assessors were independently adjudicated, or whether the same assessment procedures were applied consistently across centers. It also does not provide outcomes beyond the specified visit, so durability cannot be assessed from these data.

There is a discrepancy between the simple unadjusted recalculations and sponsor-reported analyses. The sponsor methods are reported by name, but the underlying analysis plan, the Cochran-Mantel-Haenszel strata, and sponsor confidence intervals are not reported. The registry record also does not explain whether multiplicity was controlled across the primary comparisons and secondary outcomes. This limits reconstruction and comparison of the inferential results.

The record lists a triple-masked design but does not identify the masked roles or describe implementation. It also does not report treatment duration, allocation ratio, missing-data procedures, interim analyses, or the original sample-size rationale. Safety information is limited to summarized event counts and does not include detailed event narratives or a secondary treatment-emergent adverse-event result. These gaps constrain assessment of bias, precision, and the completeness of the safety comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Multi-Center Study of New Medications to Treat Vaginal Infections — NCT02308007.
• Registry record last updated 2020-08-04; status last verified 2020-07.
• Results first posted 2020-08-04.
• 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

NCT02308007 is a completed randomized, triple-masked, parallel phase 3 study sponsored by Curatek Pharmaceuticals, LLC. The registry lists enrollment of 475 and three vaginal-gel groups: terconazole, metronidazole, and their combination. The primary endpoint is investigator-assessed clinical cure of mixed BV and VVC at the test-of-cure visit, 7-14 days after beginning treatment, in the defined mITT population.

The combination arm has the largest posted primary cure count. Sponsor-reported tests and simple unadjusted recalculations differ; because the record flags a discrepancy, the sponsor’s own analysis takes precedence. Secondary outcomes address the infection components and related assessments, but multiplicity and missing-data procedures are not reported in the registry record. Serious adverse-event counts and deaths are listed by group, with limited event detail. Interpretation should remain tied to the posted population, endpoints, follow-up time, and analyses.