Vaginal Preparation Prior to Hysterectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Vaginal Preparation Prior to Hysterectomy (NCT03412734), a randomized phase 4 study. The primary outcome is Number of Participants With Contamination.

2. Clinical Question

3. Trial Design

The registry describes NCT03412734, titled Vaginal Preparation Prior to Hysterectomy, as a randomized controlled trial. Its official title frames the comparison as chlorhexidine vaginal preparation versus iodine in reducing bacterial count. The trial has a parallel-group model and no masking. It is listed as Phase 4 and its status is terminated. The sponsor is TriHealth Inc.

The record lists an enrollment of 94. The start date is 2018-05-18, and the primary completion date is 2019-08-26. The registry does not report why the trial was terminated or provide further information about the conduct of the termination. It also does not provide a narrative of recruitment or follow-up.

The two groups are Chlorhexidine and Iodine. For the primary outcome, the posted group counts are based on participants with cultures at 90 minutes: 42.0 in the Chlorhexidine Group and 41.0 in the Iodine Group. The endpoint count with contamination is 20.0 and 35.0, respectively. The record lists the condition as hysterectomy but does not include detailed participant eligibility criteria or a fuller description of either group’s preparation procedures.

Random allocation is intended to support a balanced comparison of groups, while a parallel design assigns participants to one group rather than having each participant receive both preparations. Those are general design concepts; the registry record does not report the sequence-generation method, allocation concealment, or further implementation details. Because masking is listed as none, the record indicates an open-label design. It does not describe whether outcome assessment or laboratory procedures were masked. The sponsor’s original sample-size assumptions and other design details are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 6 patients were excluded (3 - not randomized at the day of surgery; 3 - missing study consent).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Use participants with cultures at 90 minutes

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 Number of Participants With Contamination, measured over 90 minutes from initial preparation.

The primary endpoint is the number of participants with contamination, expressed as a count of participants. Contamination is defined in the record as having >5000 bacteria within a culture. The stated timeframe is 90 minutes from initial preparation, and the specified endpoint population is participants with cultures at 90 minutes.

This is a binary participant-level outcome: each participant is classified according to whether the culture meets the stated contamination definition. In general, a binary endpoint can make a microbiological threshold easier to compare between groups than a collection of individual bacterial measurements. The threshold turns a culture result into an event count, but it also means the endpoint does not describe how far above or below the threshold a culture lies. The registry does not provide the underlying bacterial counts, culture methods, or further details about the threshold’s selection.

The posted endpoint counts are 20.0 participants with contamination among the Chlorhexidine Group and 35.0 among the Iodine Group. The endpoint is relevant to the trial’s stated comparison of vaginal preparation methods and the bacterial environment during hysterectomy. It is a measured microbiological outcome at a specified time, not a direct report of postoperative infection or another patient-centered clinical outcome. No secondary outcome measures are posted in the registry record.

7. Results Posted in the Registry

• Iodine Group: 85.4% (35/41) versus 47.6% (20/42) on control; risk difference 37.7 percentage points (95% CI 19.2 to 56.3), risk ratio 1.79 (1.27–2.52); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: a culture either meets the stated definition of contamination or it does not. For this kind of endpoint, the basic data are the number of participants with the event and the number of participants assessed in each group. The registry reports 20.0 events among 42.0 participants in the Chlorhexidine Group and 35.0 among 41.0 in the Iodine Group. The comparison record presents unadjusted measures calculated from these posted summaries. The registry also reports a separate logistic-regression analysis.

What does a risk difference describe?

A risk difference is the difference between the two groups’ event proportions. Its sign depends on the order in which groups are contrasted. In the registry comparison, the contrast is iodine relative to chlorhexidine, and the reported estimate is 0.378, with a confidence interval from 0.192 to 0.563. This measure is expressed on the probability scale, so it describes an absolute contrast rather than a relative one. The estimate is an unadjusted recalculation from the posted summary statistics; it is not the sponsor’s logistic-regression estimate.

How do risk ratios and odds ratios differ?

A risk ratio compares the probability of the event in one group with the probability in the other. The unadjusted recalculation is 1.793, with a confidence interval from 1.274 to 2.523. An odds ratio compares event odds rather than event probabilities; its unadjusted recalculation is 6.417, with a confidence interval from 2.23 to 18.46. Since odds and probabilities are different quantities, an odds ratio should not be interpreted as if it were a risk ratio. In general, when an event is common, the odds ratio can be farther from the null value than the risk ratio. This is a general statistical point, not a separate trial result.

What does logistic regression do?

Logistic regression is a method commonly used for binary outcomes. It models the log odds of an event and can estimate an odds ratio for a group contrast. The registry reports a logistic-regression odds ratio of 10.6, a 95% confidence interval from 3.02 to 37.34, and p < 0.001. Although regression can include other variables, the registry does not report the model specification or covariates, so the reported result cannot be described as adjusted for any particular factor. The record also does not specify the contrast coding direction. These omissions limit detailed reconstruction of the model.

What does a confidence interval communicate?

A confidence interval gives a range of estimates compatible with the data and the method used, subject to the method’s assumptions. In repeated use of a specified procedure, confidence intervals are designed to cover the underlying parameter at their stated confidence level at the corresponding frequency. A particular interval is not a probability statement about the parameter, and it is not a range containing most individual outcomes. The width reflects statistical precision: wider intervals indicate greater uncertainty about the estimate than narrower intervals, when comparing the same type of estimate and method.

What does the p-value contribute?

A p-value evaluates how unusual data at least as inconsistent with a null hypothesis would be if that null hypothesis and the statistical model were correct. The unadjusted comparison reports p < 0.001, and the logistic-regression result also reports p < 0.001. A small p-value is not the probability that the null hypothesis is true, and it does not measure effect size, clinical importance, or the chance that the result will replicate. Interpretation should consider the estimated contrast, its confidence interval, the endpoint definition, and the design as well as the p-value.

Why distinguish recalculation from the reported analysis?

The unadjusted measures are recalculations from the posted counts and group denominators. They provide a transparent summary based on the available group-level statistics, but they do not reproduce an unspecified regression model. The registry’s logistic regression is the reported sponsor analysis. The record gives no covariate list or other modeling details with which to assess why its odds ratio differs from the unadjusted odds ratio. The registry record does not mark a discrepancy between the reported and recalculated results.

Randomization is a design feature intended to reduce systematic differences between groups, but it does not guarantee that every characteristic is balanced, particularly in a finite trial. No baseline characteristics or adjustment plan are included in the information available in the registry record. Likewise, the record does not report the statistical plan, any interim analyses, or procedures for handling missing endpoint data. Those elements should not be inferred from the methods that are listed.

10. Confidence Intervals and Precision

The risk-difference recalculation is 0.378, with a confidence interval from 0.192 to 0.563. The risk-ratio recalculation is 1.793, with a confidence interval from 1.274 to 2.523. The unadjusted odds-ratio recalculation is 6.417, with a confidence interval from 2.23 to 18.46. These intervals describe uncertainty around different measures of the group contrast, so their widths and limits should be interpreted on their own scales.

The sponsor’s reported logistic-regression odds ratio is 10.6, with a 95% confidence interval from 3.02 to 37.34. This interval is broad on the odds-ratio scale, indicating that the reported estimate is not highly precise. The registry does not state the regression specification, so the precise basis of this interval cannot be independently reconstructed from the posted information. The unadjusted odds-ratio interval is also broad; the two estimates arise from different analyses and should not be treated as identical quantities.

In general, confidence intervals help readers assess the range of effect sizes reasonably compatible with the analysis. They capture sampling uncertainty under the statistical method, but not all possible sources of uncertainty, such as limitations in measurement, incomplete reporting, or differences between the trial population and other settings. A confidence interval does not guarantee that the true effect lies within its limits, nor does it determine clinical importance.

The endpoints of the reported intervals are on the same side of the no-difference value for each measure: zero for a risk difference and one for a ratio measure. This describes the numerical intervals, not a conclusion about clinical consequences. The registry also reports p < 0.001 for both the unadjusted comparison and its logistic-regression analysis. Statistical evidence against a null contrast does not remove the uncertainty represented by the intervals.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The registry’s planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is specified as a fraction of the observed effect: 100%, 75%, or 50% of the observed effect.

For each assumed effect size, the 80% power column gives the planned number of participants per arm for a design with an 80% chance of detecting an effect of that size under the stated assumptions, if the assumptions and statistical model apply. The 90% power column gives the corresponding per-arm planning number for a 90% chance. These are design calculations, not observations from the trial. The illustration lists 24 and 31 participants per arm for 100% of the observed effect; 46 and 60 for 75% of the observed effect; and 107 and 143 for 50% of the observed effect, for the 80% and 90% power targets respectively.

Smaller effects generally require more participants to detect with the same power and significance level, which is reflected in the increasing planning values as the assumed effect fraction decreases. The registry’s original design assumptions, including whether these assumptions were used when planning the trial, are not reported in the registry record. These figures are planning illustrations based on the observed effect, not observed power.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.476; treatment proportion p₁ = 0.854; average p̄ = 0.665.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6675 = 1.3083.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6118 = 0.5149.
4. n = (1.3083 + 0.5149)² / (0.3775)² = 23.3, rounded up to 24 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 <- 0.476190476190476                          # control proportion
p1 <- 0.853658536585366                          # 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(3412734)
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 = 24 (80% power), 31 (90% power)
 75% of observed effect: n per arm = 46 (80% power), 60 (90% power)
 50% of observed effect: n per arm = 107 (80% power), 143 (90% power)
power.prop.test: 23.3 
Simulated power at n = 24 per arm: 0.827 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s analysis as logistic regression, with an odds ratio of 10.6, a 95% confidence interval from 3.02 to 37.34, and p < 0.001. This is the analysis reported in the registry. The record does not state the covariates, model specification, or contrast coding, so the estimate cannot be fully reconstructed from the entry.

The recalculated unadjusted odds ratio from the posted group summaries is 6.417, with a confidence interval from 2.23 to 18.46. This calculation uses the reported event counts and endpoint denominators and is not a replacement for the sponsor’s regression. The risk difference and risk ratio are also unadjusted recalculations, each expressing the group contrast on a different scale.

The numerical difference between the reported regression odds ratio and the recalculated unadjusted odds ratio should be read as a difference between the sponsor’s reported model result and a summary-statistic calculation. The registry does not provide enough methodological detail to identify why the estimates differ, and it does not mark a discrepancy. The sponsor’s analysis should be understood as the reported analysis; the recalculation is a supplementary, unadjusted reading of the posted summaries.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one outcome measure and one reported analysis. No secondary outcome measures are posted. The primary endpoint is the number of participants with contamination, based on cultures at 90 minutes. The record does not provide a full statistical analysis plan or state whether any additional analyses were conducted but not entered in the registry.

Multiplicity arises when a study tests multiple outcomes, time points, subgroups, or models, because repeated testing can increase the chance of at least one apparently notable result under a null hypothesis. That is a general statistical concern. The available record does not describe a multiplicity adjustment or a strategy for controlling multiple comparisons. With only one posted outcome measure and one reported analysis, the extent of any multiplicity beyond those entries cannot be assessed from the registry record.

The endpoint population is described as participants with cultures at 90 minutes. The registry provides group denominators for that endpoint, but it does not explain how participants without an available culture were handled, whether any cultures were unevaluable, or why endpoint denominators differ from the enrollment figure. The missing-data method is not reported in the registry record. The record does not state whether the analysis followed an intention-to-treat, per-protocol, or another analysis-population definition.

These gaps matter because the interpretation of a binary outcome can depend on who was included and how unavailable measurements were treated. This is a general methodological point; no particular missing-data problem can be inferred from the record. The registry also does not report interim analyses, stopping rules, or the trial’s statistical plan. Since the study status is terminated, the reason for termination and its relationship, if any, to the analysis or data collection are not reported in the registry record.

15. 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 0% reporting threshold.

The serious adverse event figures list zero serious adverse events in the Chlorhexidine Group and zero in the Iodine Group. The corresponding serious-event at-risk counts are 44 and 41. The other adverse event figures also list zero events in each group, with at-risk counts of 44 and 41, respectively. Deaths are listed as zero in both groups.

These figures describe what is recorded in the adverse-event fields; they do not establish that no adverse effects occurred. The record does not provide event descriptions for non-serious adverse events, and the serious-event terms list is empty. The adverse-event at-risk counts are not the same as the endpoint denominators, and the registry does not explain that difference.

In general, a zero recorded count means no event was entered in that category for the stated at-risk group. It does not show that the risk is exactly zero, especially when the amount of safety information is limited. The registry does not provide additional detail about adverse-event collection, observation duration, or how events were classified. These safety entries should therefore be read as the recorded counts, not as a comprehensive assessment of safety.

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

The registry’s primary endpoint data show fewer participants meeting the culture-based contamination definition in the Chlorhexidine Group than in the Iodine Group at 90 minutes from initial preparation. The posted counts are 20.0 and 35.0, respectively. The unadjusted risk-difference estimate is 0.378, with a confidence interval from 0.192 to 0.563. The registry’s logistic-regression analysis reports an odds ratio of 10.6, with a 95% confidence interval from 3.02 to 37.34 and p < 0.001.

These results describe a difference in the recorded bacterial-threshold endpoint in this randomized trial. They do not show whether the observed difference changes postoperative infection risk, other health outcomes, or the course of care. No such secondary outcomes are posted. The bacterial threshold is a surrogate-type microbiological measurement in the context of the trial’s stated question; the registry does not establish how it relates to later clinical outcomes.

Statistical evidence for a group contrast is not the same as evidence of clinical importance. A small p-value does not establish that the result is consequential to patients, and the confidence intervals do not address all sources of uncertainty. The lack of masking and the absence of detailed procedural, model, and missing-data information also limit how fully the comparison can be evaluated from the registry record.

The study’s randomized, parallel-group design is relevant to interpreting the comparison, but randomization alone does not settle questions about implementation, measurement, or applicability. The record is limited to the stated population, preparation comparison, and endpoint. It does not justify extrapolating the result to other settings, procedures, outcomes, or groups not described in the registry. No treatment recommendation follows from these registry statistics.

17. Why This Trial Matters Statistically

This trial illustrates how the choice of statistical scale affects the description of a binary outcome. A risk difference gives an absolute contrast in event proportions, while risk ratios and odds ratios give relative contrasts. The posted recalculations include all three, allowing readers to see that they address the same group comparison using different measures. They should not be substituted for one another or interpreted as though their numerical values had the same meaning.

The record also makes clear why the sponsor’s model result should be separated from a simple summary-statistic recalculation. Logistic regression is the reported analysis, while the recalculated risk difference, risk ratio, and odds ratio are unadjusted. Without details of the regression specification, covariates, or contrast coding, the model estimate cannot be fully audited from the registry entry. Transparent reporting of these elements helps readers understand what a model estimates and how it relates to the observed group summaries.

Precision is another central issue. The reported confidence intervals provide information beyond the point estimates, showing uncertainty around both the unadjusted contrasts and the logistic-regression result. Planning illustrations further show, in general, how a smaller effect assumption requires more participants per arm for a given power target. Those illustrations are not the trial’s original design record and are not observed power.

Finally, the endpoint is a defined bacterial threshold measured at a particular time. This is a useful statistical case for distinguishing a microbiological outcome from a clinical outcome and for recognizing the limits of what a registry result can establish. The trial’s status, endpoint denominators, and missing analysis details are part of that interpretation, not reasons to infer unreported procedures or outcomes.

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 trial-specific details that would help assess the result are not reported in the registry record. Although the trial is described as randomized and parallel, the record does not give details of sequence generation, allocation concealment, or implementation. Masking is listed as none, and the record does not state whether culture assessment or laboratory procedures were masked. The arm descriptions are blank, so procedural differences beyond the intervention names cannot be evaluated.

The registry lists an enrollment of 94, while the endpoint denominators are 42.0 for the Chlorhexidine Group and 41.0 for the Iodine Group. The record does not reconcile these figures or describe any participants without endpoint cultures. It does not report the missing-data approach, the analysis population definition, or reasons for unavailable cultures, if any. These omissions limit assessment of whether the endpoint comparison represents all enrolled participants.

The trial status is terminated, but the reason for termination is not reported in the registry record. The record does not say whether termination affected recruitment, data collection, or analysis, so no such explanation should be assumed. The original sample-size justification and statistical plan are also not reported. Planning figures based on the observed effect cannot substitute for that information.

Further limitations of interpretation follow from the endpoint itself: contamination is defined by a culture threshold at 90 minutes, and the registry does not provide the underlying bacterial counts, detailed culture procedures, or posted secondary clinical outcomes. Consequently, the record cannot establish the relationship between this measurement and later clinical outcomes. The logistic-regression model details are also absent, preventing a fuller assessment of the reported odds ratio.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Vaginal Preparation Prior to Hysterectomy — NCT03412734.
• Registry record last updated 2021-01-11; status last verified 2021-01.
• Results first posted 2020-11-18.
• 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

NCT03412734 is a Phase 4 randomized, open-label, parallel-group trial sponsored by TriHealth Inc. It compares chlorhexidine and iodine vaginal preparation before hysterectomy. The registry lists enrollment of 94, a start date of 2018-05-18, a primary completion date of 2019-08-26, and a terminated status.

The primary outcome is the number of participants with contamination, defined as having >5000 bacteria within a culture, assessed 90 minutes from initial preparation. The posted counts are 20.0 of 42.0 in the Chlorhexidine Group and 35.0 of 41.0 in the Iodine Group. The reported logistic-regression odds ratio is 10.6, with a 95% confidence interval from 3.02 to 37.34 and p < 0.001. The registry lists one outcome measure and no posted secondary outcomes.

The record does not report the reason for termination, the original sample-size rationale, detailed regression specifications, or missing-data methods. The endpoint is a culture-defined measurement; the registry does not report later clinical outcomes.