Treatment of Bacterial Vaginosis (BV) With Tinidazole: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Bacterial Vaginosis (BV) With Tinidazole (NCT00334633), a randomized phase 4 study. The primary outcome is Cure of Bacterial Vaginosis.

2. Clinical Question

The registry describes a randomized, triple-masked, parallel-group phase 4 trial. The posted primary outcome counts are 75 participants in the metronidazole group, 73 in the tinidazole 500 mg group, and 77 in the tinidazole 1 gm group. These counts are considered alongside their reported group denominators and the estimated risk differences with confidence intervals.

The clinical question is comparative: how did the recorded cure outcome differ across the assigned regimens in this trial? The posted results do not by themselves establish that any regimen is generally preferable. They describe outcomes in the trial’s recorded population and timeframe, with uncertainty that matters when interpreting apparent differences.

3. Trial Design

The registry record identifies a randomized, triple-masked, parallel-group phase 4 trial sponsored by the University of Alabama at Birmingham. Its enrollment is recorded as 593, and its status is completed. The recorded start was 2004-11 and the primary completion was 2009-12. These dates describe the registry record; they do not supply details about how long individual participants were followed beyond the stated outcome timeframes.

The parallel design assigned participants to metronidazole, tinidazole 500 mg, or tinidazole 1 gm. The record lists metronidazole 500 twice daily for 7 days, tinidazole 500 mg twice daily for 7 days, and tinidazole 1 gm twice daily for 7 days. Randomization and masking are recorded, but the method used to generate the allocation sequence, the masking procedures, and which roles were masked are not reported in the registry record.

The primary outcome was cure of bacterial vaginosis, assessed at one month and defined as resolution of Amsel criteria. The registry labels its population ITT. The posted group counts are 75 of 117 for metronidazole, 73 of 118 for tinidazole 500 mg, and 77 of 114 for tinidazole 1 gm. The registry also lists recurrence of bacterial vaginosis from baseline to 4 weeks as a secondary outcome. Its recurrence counts are recorded with group denominators in the posted results.

The record lists two outcome measures and no analyses in its analysis count. It does not describe the original sample-size justification, the trial’s statistical analysis plan, interim analyses, or the handling of missing outcome data. These omissions limit how fully the posted aggregate results can be connected to the trial’s planned analysis.

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

Analysis population for the primary outcome, as defined in the registry: ITT

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 Cure of Bacterial Vaginosis, measured over one month.

The primary endpoint is cure of bacterial vaginosis at one month. The registry defines cure as resolution of Amsel criteria for bacterial vaginosis and labels the outcome population ITT. The measure is a count of participants meeting the endpoint within each group, rather than a continuous measurement. The registry does not provide further details about the criteria assessment procedure or the treatment of participants whose outcome status was unavailable.

A cure endpoint gives a clinically interpretable summary of whether the condition met the stated resolution criteria at the specified follow-up. Reporting the number meeting the endpoint alongside the group denominator allows the observed group experience to be described, while a comparative estimate such as a risk difference puts the between-group contrast on an absolute scale. The confidence interval around that contrast communicates how uncertain the estimate is.

The posted primary counts are 75 of 117 for metronidazole, 73 of 118 for tinidazole 500 mg, and 77 of 114 for tinidazole 1 gm. These are registry-recorded counts, not a full account of each participant’s clinical course. A single assessment at one month does not describe outcomes beyond that timeframe. The registry separately lists recurrence from baseline to 4 weeks, so cure and recurrence should be understood as distinct recorded outcomes rather than assumed to be interchangeable measures.

The endpoint is useful for framing the trial’s stated comparison, but the registry record does not report additional endpoint-validation details or a more complete assessment schedule. Interpretation should therefore remain tied to the definition, population label, and timeframe that are recorded.

7. Results Posted in the Registry

• Tinidazole 500 mg: 61.9% (73/118) versus 64.1% (75/117) on control; risk difference -2.2 percentage points (95% CI -14.6 to 10.1), risk ratio 0.97 (0.79–1.17); unadjusted two-proportion z-test p = 0.722.
• Tinidazole 1 gm: 67.5% (77/114) versus 64.1% (75/117) on control; risk difference 3.4 percentage points (95% CI -8.8 to 15.7), risk ratio 1.05 (0.87–1.27); unadjusted two-proportion z-test p = 0.581.

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.

Recurrence of BV

• 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:
  • Tinidazole 500: 39.5% (45/114) versus 35.9% (42/117) on control; risk difference 3.6 percentage points (95% CI -8.9 to 16.1), risk ratio 1.10 (0.79–1.53); unadjusted two-proportion z-test p = 0.575.
  • Tinidazole 1 gm: 31.4% (37/118) versus 35.9% (42/117) on control; risk difference -4.5 percentage points (95% CI -16.6 to 7.5), risk ratio 0.87 (0.61–1.25); unadjusted two-proportion z-test p = 0.461.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tinidazole 500 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tinidazole 1 gm and the control. The interval gives the range of effects that remain compatible with the data.

Recurrence of bacterial vaginosis is the listed secondary endpoint, measured from baseline to 4 weeks. Its group comparisons show point estimates in different directions for the two tinidazole regimens, while both confidence intervals include zero. In broad terms, the recurrence results do not supply a consistent, precise additional signal that resolves the uncertainty in the primary cure comparisons.

The secondary outcome is related to the primary question because both concern bacterial vaginosis during the recorded follow-up period, but it is not interchangeable with cure at one month. Each outcome has its own definition and observation timeframe. A recurrence count does not by itself confirm or negate the cure outcome, and the record does not provide an individual-level account linking participants’ cure and recurrence statuses.

Secondary endpoints generally carry less confirmatory weight when many outcomes or comparisons are examined without a stated multiplicity plan. Repeated testing can increase the chance that an apparently notable result arises by chance. The registry record lists the secondary endpoint but does not report whether the trial prespecified an adjustment for multiple comparisons, how secondary analyses were prioritized, or whether any were intended to be confirmatory.

For that reason, the secondary results are best treated as descriptive context. Their estimates and uncertainty can inform how the overall pattern is understood, but they should not be used to make a strong standalone claim or to override the primary endpoint. The absence of reported analyses in the registry record further limits assessment of how these results fit with any planned testing strategy.

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

• Recurrence of BV

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary: each participant is counted according to whether cure was recorded. For a binary endpoint, a group-level event count and denominator describe the observed event frequency. A risk difference compares those frequencies by subtracting the comparator frequency from the intervention frequency. Its zero value corresponds to no difference in the event frequencies on this scale. Positive and negative estimates indicate opposite directions of contrast according to the comparison’s ordering.

What does the risk difference express?

The reported risk differences are -0.022 for tinidazole 500 mg versus metronidazole and 0.034 for tinidazole 1 gm versus metronidazole. Each estimate is a point estimate: it gives one value for the contrast based on the posted group data. It should not be read as the exact underlying difference. The associated confidence interval describes uncertainty around the estimate and is more informative than the point estimate alone when judging the range of plausible contrasts.

The registry also gives relative measures, including risk ratios and odds ratios. These express comparisons on different scales from the risk difference. A risk ratio compares event frequencies as a ratio, while an odds ratio compares event odds. Different scales can be useful for different questions, but they do not change the underlying group observations. For this explanation, the absolute risk-difference scale is emphasized because it directly expresses the estimated difference between group event frequencies.

How should a confidence interval be understood?

A confidence interval is a statistical procedure for representing uncertainty in an estimate. In general, a wider interval indicates less precision, and an interval that includes the no-difference value means the data do not exclude that value at the corresponding confidence level. This does not mean that all values inside the interval are equally likely, nor that values outside it are impossible. It also does not establish equivalence. The interpretation depends on the design and calculation assumptions as well as the observed data.

For the primary comparisons, both reported risk-difference intervals include zero. The endpoints extend to values on either side of zero, so the posted estimates permit contrasts favoring either group. This is why the direction of a point estimate alone should not be treated as a conclusive finding. The unadjusted p-values of 0.722 and 0.581 are also consistent with the intervals not excluding zero; neither is a probability that a treatment effect is true or false.

What does unadjusted mean?

An unadjusted comparison uses the posted group summaries without accounting for other variables or for a family of multiple comparisons. It can be a transparent way to describe the observed contrast, but it may not match a trial’s prespecified primary analysis. The registry record does not report the trial’s complete statistical analysis plan or any reported analysis set, so the intended adjustment strategy is not reported in the registry record. The posted recalculations should be read as simple comparisons of the available summaries, not as evidence that no other analysis was performed.

Randomization is intended to support a fair comparison of assigned groups, but it does not guarantee that every measured or unmeasured characteristic is identical between groups. A complete interpretation would consider allocation procedures, adherence, follow-up, missing data, and the planned analysis. The record identifies randomization and an ITT label for the primary outcome, but details on those other matters are not reported in the registry record.

Why does over-dispersion matter?

Over-dispersion is a general concern when observed variability is greater than a statistical model assumes. If a model understates variability, its standard errors and confidence intervals can be too small, creating an impression of greater precision than the data warrant. The posted primary endpoint is a binary participant count, and the registry does not report a model-based over-dispersion assessment. This concept is therefore general context, not a claim that over-dispersion occurred in this trial.

The calculations associated with the posted comparisons use the group summary information and are described as unadjusted recalculations. The record reports no discrepancy for these recalculations. If a sponsor analysis were available, its own prespecified methods and conclusions would be important context; a detailed sponsor analysis is not reported in the registry record.

What can be concluded from the methods information?

The registry supports a description of the randomized parallel-group structure, masking label, outcome definition, group counts, and unadjusted comparisons. It does not report enough detail to reconstruct the full analysis process. In particular, the original sample-size assumptions, missing-data rules, analysis population details beyond the ITT label, multiplicity handling, and any interim-analysis plan are not reported in the registry record. Statistical interpretation should distinguish what the posted aggregate results show from what would require those additional methods details.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the comparison estimate. For cure, the tinidazole 500 mg risk difference is -0.022, and its confidence interval runs from -0.146 to 0.101. The tinidazole 1 gm risk difference is 0.034, with an interval from -0.088 to 0.157. Both intervals include zero, and each spans values on both sides of zero. Thus, neither point estimate is precise enough to establish the direction of the underlying difference from the posted comparison alone.

The intervals also show why the results should not be described as proof of no difference. Their ranges include zero but also include nonzero contrasts in either direction. The evidence is compatible with no difference as well as with differences that the trial’s posted estimates do not resolve precisely. Whether particular values would be considered important is not specified in the registry record; no clinical equivalence margin is reported.

The recurrence comparisons likewise have intervals that include zero: 0.036 with an interval from -0.089 to 0.161 for tinidazole 500, and -0.045 with an interval from -0.166 to 0.075 for tinidazole 1 gm. These ranges reinforce that the secondary comparisons are uncertain, rather than providing a more precise answer to the primary question.

Confidence intervals describe uncertainty under the calculation method; they do not account automatically for every limitation, such as missing outcome data, departures from the analysis plan, or multiple testing. The registry record does not report enough detail to assess all such sources. The intervals should therefore be read as an essential description of statistical precision, not as a complete summary of every uncertainty in the trial.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not a report of the trial’s original design target. They assume a two-sided significance level of 0.05, equal allocation between the two arms being compared, and a normal approximation. Each planning row 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.

For these binary outcomes, the planning figures are participants per arm, not total participants and not total events. The 80% power column indicates the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column gives the corresponding planning size for a higher chance of detecting that effect. These are design targets under assumptions, not guarantees about what a future study would find.

Rows that plan for 100%, 75%, or 50% of the observed effect represent different assumed effect sizes. A smaller effect is harder to distinguish from random variation, so the planning calculation requires more participants per arm. For example, the primary tinidazole 500 mg comparison lists 7,305 participants per arm for 80% power when planning for 100% of the observed effect, and 29,037 participants per arm when planning for 50% of that effect. These figures illustrate how sensitive the planning estimate is to the assumed effect size.

The sample-size curve should be read as a visual version of this relationship: as the effect to detect becomes smaller, the required planning sample grows. The figures are not observed power and do not measure the probability that the trial’s result is correct. They also do not establish that the original trial was underpowered, because its design assumptions are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.641; treatment proportion p₁ = 0.619; average p̄ = 0.630.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6829 = 1.3384.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6827 = 0.5745.
4. n = (1.3384 + 0.5745)² / (-0.0224)² = 7,304.8, rounded up to 7,305 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 <- 0.641025641025641                          # control proportion
p1 <- 0.61864406779661                          # 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(334633)
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 = 7,305 (80% power), 9,779 (90% power)
 75% of observed effect: n per arm = 12,947 (80% power), 17,331 (90% power)
 50% of observed effect: n per arm = 29,037 (80% power), 38,872 (90% power)
power.prop.test: 7304.8 
Simulated power at n = 7,305 per arm: 0.799 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, groups, timeframes, or statistical comparisons are examined. Each additional test creates another opportunity for a result to appear noteworthy by chance. A prespecified strategy can address this issue by identifying a primary endpoint and defining how secondary tests will be interpreted or adjusted. The registry record identifies cure as the primary outcome and recurrence as a secondary outcome, but a multiplicity procedure is not reported in the registry record.

The posted comparisons include two tinidazole regimens against the metronidazole group for the primary outcome, as well as comparisons for recurrence. The reported p-values are unadjusted. They should therefore be understood as comparisons without a reported correction for the family of tests. The record does not state whether the trial’s own analysis used a different procedure, whether secondary findings were intended to be confirmatory, or what decision rules were planned.

The registry labels the primary outcome population ITT, but does not report the operational definition used for that population or describe how participants with missing measurements were handled. The group denominators in the posted results may differ across outcomes and arms. The record does not explain those denominator differences, whether all randomized participants contributed to every analysis, or whether any imputation or sensitivity analysis was used. Missing-data assumptions can affect both estimates and precision, especially when outcome status is unavailable in ways related to participants’ outcomes.

The analysis count is recorded as zero, and the record contains no reported analyses. This should not be interpreted as proof that no analysis was conducted; it means the registry record does not provide a reported analysis set for assessment. The original analysis plan, covariate adjustments, interim analyses, and any stopping rules are not reported in the registry record. Those omissions prevent a full evaluation of whether the posted summaries match the prespecified analysis or how multiplicity and missing data were handled.

These limitations do not invalidate the posted counts or their descriptive comparisons. They do mean that inferential claims should remain modest: the unadjusted estimates and confidence intervals describe the available registry results, while unreported procedures cannot be assumed.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse events as zero in the metronidazole group among 197 participants at risk, zero in the tinidazole 500 mg group among 200 at risk, and zero in the tinidazole 1 gm group among 196 at risk. These are the serious adverse event figures recorded for the groups. No serious adverse event terms are listed.

Zero reported events means that no serious adverse events were entered in these registry group counts; it does not establish that the risk is absent or that the regimens have identical safety profiles. With no events recorded, a comparative effect estimate for serious adverse events is not presented in the posted results. The denominators also show the reported at-risk populations for this outcome, but the registry does not explain their relationship to the primary outcome populations.

Death counts are not reported in the registry record. The record lists other, non-serious adverse event counts separately, but those counts should not be conflated with serious adverse events. As with any registry safety summary, the figures describe what was recorded and do not provide details on event definitions, ascertainment, timing, or completeness beyond the posted fields.

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

The posted primary results show cure counts that are close in descriptive terms across the metronidazole and tinidazole groups, while the estimated risk differences remain uncertain. Both primary confidence intervals include zero and extend across contrasts in either direction. The registry comparisons therefore do not establish a clear difference in cure between metronidazole and either tinidazole regimen at the stated one-month assessment.

This does not mean the regimens have been shown to be equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty lies within that margin. No equivalence margin is reported in the registry record. Nor do the results prove that a difference is absent; the confidence intervals allow a range of possible contrasts.

The findings are specific to the registry-recorded trial, its participants, regimens, outcome definition, and follow-up. The primary endpoint is resolution of Amsel criteria at one month, and recurrence is separately recorded from baseline to 4 weeks. The outcomes do not describe longer-term status or all aspects of bacterial vaginosis. A single endpoint cannot capture every patient-relevant outcome, and the registry does not report additional efficacy measures beyond those listed.

The results also do not support conclusions about groups or circumstances not described in the record. Details about eligibility criteria, adherence, missing outcomes, and analysis procedures are limited or absent. The posted estimates are aggregate comparisons, not a complete account of individual responses or the reasons participants may have had different outcomes.

The serious adverse event summary records zero events in each group, but that finding is not evidence that no serious events could occur. Death counts are not reported in the registry record, and the safety summary does not by itself characterize every possible harm. Overall, the record supports a cautious statistical reading of the observed comparisons, not medical advice or a general claim about treatment choice.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares two tinidazole regimens with an active metronidazole comparator and reports an absolute measure of the primary contrast. The registry also identifies randomization, masking, the primary outcome definition, and the assessment timeframe. Those details make it possible to describe the question and examine the posted group counts rather than relying only on a broad statement that the treatments were compared.

The key statistical lesson is the difference between a point estimate and a precise conclusion. The primary estimates point in different directions across the tinidazole comparisons, but their confidence intervals include zero and allow contrasts on either side. A small or directionally suggestive point estimate cannot by itself settle the comparative question. The uncertainty interval is essential to judging what the results can support.

The trial also illustrates why a non-significant unadjusted result should not be translated into proof of equivalence. The posted results do not identify a clear difference, but the record does not provide an equivalence margin or a design intended to establish equivalence. Likewise, sample-size planning illustrations based on observed effects are not a substitute for the original design assumptions and are not observed power.

Finally, the record highlights the importance of transparency about methods. Information on missing-data handling, multiplicity, analysis populations beyond the ITT label, and the original sample-size justification is not reported in the registry record. Such details affect how confidently registry results can be connected to a planned analysis. The available data still permit a careful descriptive interpretation, provided that uncertainty and the record’s omissions remain explicit.

18. 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 limitations specific to this record constrain interpretation. The registry lists an enrollment of 593, while the outcome-specific group denominators shown for cure and recurrence do not form a single uniform set across all entries. The record does not explain the differences between these denominators, identify how many randomized participants lacked each outcome, or describe whether the analysis population varied by endpoint. The ITT label for the primary outcome is not accompanied by an operational definition.

The registry does not report the original sample-size justification or the assumptions used to plan the trial. The planning illustrations based on observed effects cannot fill that gap because they are retrospective calculations. The statistical analysis plan, covariate adjustment strategy, interim analyses, stopping rules, and multiplicity procedures are also not reported in the registry record. As a result, the relationship between the posted unadjusted comparisons and any prespecified trial analysis cannot be assessed in detail.

The primary endpoint is defined as resolution of Amsel criteria at one month, but the registry does not provide further information on assessment procedures, outcome adjudication, or missing measurements. The recurrence outcome is recorded from baseline to 4 weeks; the record does not explain its operational definition or how it relates at the participant level to the cure outcome.

The posted results are aggregate summaries. They do not show the distribution of participant characteristics, adherence, or individual outcome histories. The registry’s safety summary records serious event counts but does not report event terms, timing, or details of ascertainment; deaths are not reported in the registry record. These limitations call for restraint in interpreting both efficacy and safety beyond the stated outcomes and recorded timeframes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Treatment of Bacterial Vaginosis (BV) With Tinidazole — NCT00334633.
• Registry record last updated 2017-12-02; status last verified 2017-10.
• Results first posted 2011-06-23.
• 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.

22. Record Summary

The registry describes a completed, randomized, triple-masked, parallel-group phase 4 trial of tinidazole for bacterial vaginosis, sponsored by the University of Alabama at Birmingham. Recorded enrollment was 593. The primary outcome was cure at one month, defined as resolution of Amsel criteria, with the population labeled ITT.

The posted primary comparisons are unadjusted. The risk-difference estimates for tinidazole 500 mg and tinidazole 1 gm versus metronidazole have confidence intervals that include zero. Recurrence was listed as a secondary outcome, and serious adverse event counts were recorded as zero in each group. The registry record does not report the trial’s complete statistical plan, original sample-size assumptions, missing-data procedures, or multiplicity handling.