Chlorhexidine-Alcohol Versus Povidone-Iodine for Cesarean Antisepsis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Chlorhexidine-Alcohol Versus Povidone-Iodine for Cesarean Antisepsis (NCT02202577), a randomized na study. The primary outcome is Number of Patients With Surgical Site Infection.

2. Clinical Question

This is a question about the comparative frequency of an infection outcome after two surgical skin preparations. It does not ask whether either preparation is better than no antiseptic preparation, nor does it establish effects for procedures or populations not described in the registry record. The primary outcome includes superficial, deep, and organ space surgical site infections as defined by CDC criteria. A secondary outcome concerns non-infectious surgical site complications during the same timeframe.

The trial is listed as randomized, with a parallel model and no masking. Its record identifies the primary hypothesis but does not report the protocol details needed to evaluate all aspects of how that hypothesis was planned to be tested. In particular, the original design assumptions and the registry's distinction between its posted analyses are not reported in the registry record.

3. Trial Design

NCT02202577, titled “Chlorhexidine-Alcohol Versus Povidone-Iodine for Cesarean Antisepsis,” is listed as a randomized, parallel-group trial with no masking. The registry lists Case Western Reserve University as the sponsor. The phase is recorded as not applicable. The trial status is completed, with enrollment of 932 participants; the registry gives a start date of 2014-03 and a primary completion date of 2016-07.

The two arms compared pre-operative skin preparation with chlorhexidine gluconate-isopropyl alcohol against povidone-iodine scrub and paint. For the primary outcome, 461 participants were listed in the chlorhexidine-isopropyl alcohol arm and 471 in the povidone-iodine arm. The primary endpoint was the number of participants with a surgical site infection within 4 weeks after cesarean delivery. A secondary outcome recorded non-infectious surgical site complications within the same timeframe.

Randomization means assignment to the study preparations was intended to be determined by chance, rather than chosen solely by the treating team or participant. The registry does not report the randomization sequence method, concealment procedures, or any stratification factors. No masking was used, according to the record; it does not describe whether endpoint assessors were masked separately.

The posted results include event counts by arm, two registry-reported Fisher Exact analyses for the primary outcome, and an unadjusted recalculation based on the posted summary statistics. The record does not explain why it lists two primary analyses or how their roles differ. Details of the original sample-size justification, planned analysis population, missing-data handling, and any interim analyses 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.

Overall Study

Reasons for not completing this period:

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 Patients With Surgical Site Infection, measured over 4 weeks after cesarean delivery.

The primary endpoint counts participants with a cesarean-related surgical site infection by CDC criteria. The definition covers superficial, deep, and organ space infections, and the specified assessment timeframe is 4 weeks after cesarean delivery. The registry reports the outcome as a participant count, not as a time-to-event measure or a measure of infection severity.

Counting participants who experience an event gives a direct way to compare the observed frequency of infection between the randomized preparations. The arm sizes matter when interpreting the counts: the same number of events can represent different observed proportions when the numbers of participants differ. The reported recalculation therefore expresses the arm comparison as a risk difference and also gives relative measures.

General statistical context: a binary endpoint reduces each participant's outcome to whether the defined event occurred during the specified assessment period. This makes the endpoint relatively straightforward to interpret, but the result depends on how consistently events are identified and recorded. The registry names CDC criteria but does not provide further information about endpoint adjudication, completeness of follow-up, or the handling of participants whose outcome status was unknown. Those details are not reported in the registry record.

The secondary endpoint is a distinct count of participants with non-infectious surgical site complications. It can add context about complications other than infection, but it does not replace or redefine the primary infection outcome.

7. Results Posted in the Registry

• Povidone-Iodine Scrub and Paint: 7.0% (33/471) versus 6.3% (29/461) on control; risk difference 0.7 percentage points (95% CI -2.5 to 3.9), risk ratio 1.11 (0.69–1.80); unadjusted two-proportion z-test p = 0.661.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Patients With Non-infections Surgical Site Complications

• 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:
  • Povidone-Iodine Scrub and Paint: 3.6% (17/471) versus 4.1% (19/461) on control; risk difference -0.5 percentage points (95% CI -3.0 to 2.0), risk ratio 0.88 (0.46–1.66); unadjusted two-proportion z-test p = 0.685.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Povidone-Iodine Scrub and Paint and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: participants with non-infectious surgical site complications within 4 weeks after cesarean delivery. Its unadjusted comparison is close to the null on the risk-difference scale, and its confidence interval includes zero. This broadly parallels the primary result in that neither posted unadjusted comparison gives a clear statistical separation between the preparations.

The secondary outcome concerns a different kind of complication from the primary infection endpoint. Considering it may provide context about complications beyond infection, but it does not confirm or overturn the primary result. The outcome's definition and assessment timeframe are those stated in the registry; additional detail about how events were classified is not reported in the registry record.

General statistical context: secondary outcomes are often useful for describing a broader range of trial results, but they typically carry less weight for confirmatory conclusions when the primary hypothesis is the main planned question. Testing multiple outcomes can increase the chance that at least one result appears noteworthy by chance. Whether and how the investigators controlled that risk is not reported in the registry record. The posted secondary comparison is unadjusted, and its result should not be treated as a separate confirmation of the primary finding.

The record reports no sponsor analysis for this secondary endpoint. The recalculated estimate should therefore be understood as a summary derived from the posted arm counts, not as a registry-reported inferential analysis. No combined assessment across the primary and secondary outcomes is reported, and the endpoints should not be pooled or treated as interchangeable.

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

• Number of Patients With Non-infections Surgical Site Complications

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical context: randomized comparisons aim to estimate how outcomes differ between assigned groups while reducing systematic differences in participant characteristics. Randomization does not guarantee that every feature is balanced, and the methods used to generate and conceal assignments can matter. The registry identifies the trial as randomized but does not report those operational details.

What does the risk difference describe?

The recalculated risk difference compares the observed event proportions in the two arms. In this comparison the direction is povidone-iodine relative to chlorhexidine-isopropyl alcohol: a positive estimate means the observed proportion is higher in the povidone-iodine arm, while a negative estimate means it is lower. The estimate is 0.007. Its 95% confidence interval, -0.025 to 0.039, includes zero, the value corresponding to no difference in observed risk under this measure. This is an unadjusted recalculation from the posted arm summaries, not a claim about an adjusted model.

What do relative measures add?

A risk ratio compares event risks as a ratio rather than a difference. An odds ratio compares event odds. These measures use different scales, so their numerical values are not directly interchangeable with the risk difference. The recalculation lists relative estimates and intervals for the primary outcome; the registry also reports risk-ratio analyses using Fisher Exact. Because the reported analyses and the recalculated quantities are not described as the same procedure, they should be kept distinct. The registry record does not explain the distinction between its two reported primary analyses.

What is a confidence interval?

General statistical context: a confidence interval conveys uncertainty about an estimated effect under the assumptions of the method used. A wider interval indicates less precision than a narrower interval. An interval that includes the null value does not establish that the true effect is exactly null; it indicates that the data and method are compatible with a range of values that includes no difference. The interval also indicates which effect directions remain plausible under that method. It is not a probability statement that the true value lies in the particular calculated interval.

What does a p-value convey?

General statistical context: a p-value is calculated under a null hypothesis and a test procedure. It describes how unusual data at least as discrepant as those observed would be under that model. It does not measure the size of an effect, the probability that the null hypothesis is true, or the probability that a result will replicate. A p-value should be read alongside the effect estimate, its uncertainty, study design, and endpoint definition. The registry lists p = 0.661 for the unadjusted recalculation and p-values of 0.38 and 0.26 for the two Fisher Exact analyses.

Why use Fisher Exact?

Fisher Exact is a method for testing association in a two-by-two table of counts. General statistical context: it calculates the probability of tables at least as extreme as the observed table under a specified null model, conditional on the margins. It is often used for binary outcomes, particularly when counts are limited, and does not rely on the same large-sample approximation as some alternative tests. The registry names Fisher Exact for its reported risk-ratio analyses. The registry does not describe all implementation details or the exact rationale for selecting that method.

What does “unadjusted” mean?

The recalculation uses the posted counts and arm sizes without adjustment for other variables. It therefore summarizes the crude contrast between the two groups. General statistical context: adjustment can account for specified covariates and may alter an estimate or its uncertainty, but the choice and interpretation depend on a prespecified model and the available participant-level data. No adjusted analysis details are reported in the registry record. The recalculated figures should not be represented as the trial's full statistical analysis plan.

The registry gives counts rather than continuous outcome measurements, and no dispersion measure is relevant to these binary counts. The result is appropriately discussed in terms of event frequency, effect estimates, uncertainty, and the stated assessment timeframe. The registry record does not report an analysis plan that would establish whether other endpoints, subgroups, or analysis populations were prespecified.

11. Confidence Intervals and Precision

The recalculated primary risk difference is 0.007, with a 95% confidence interval from -0.025 to 0.039. The interval spans zero and reaches in both directions, so the posted data are compatible with no difference as well as with differences favoring either preparation under this measure. Its breadth limits how precisely the comparison identifies the direction and magnitude of the effect.

General statistical context: precision concerns how narrowly an estimate is pinned down, not whether an estimate is important or whether a treatment works. Confidence intervals show uncertainty under a specified statistical method; they do not guarantee that all relevant values are covered, especially if the method's assumptions or data completeness are inadequate. Here, the interval is based on an unadjusted recalculation of posted summary statistics.

The registry's two Fisher Exact entries report risk-ratio estimates of 0.90 and 0.83, with 95% upper confidence limits of 1.35 and 1.25. Their lower confidence limits are not reported in the registry record. The corresponding p-values are 0.38 and 0.26. Since the record does not explain how the two entries differ, they cannot be used to infer a single, fully described sponsor analysis interval.

The secondary outcome also has an unadjusted risk-difference interval, from -0.030 to 0.020. As with the primary endpoint, it includes zero. Confidence intervals for these outcomes do not establish equivalence, and the record does not report a target margin for deciding what range would count as practically negligible.

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 the trial's original design calculation. For these binary outcomes, the listed figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The trial's own original design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for an analysis to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and those assumptions held. The 90% power column gives the corresponding illustration for a 90% chance. These are design-planning quantities, not statements about what the completed trial achieved.

Rows for planning at 100%, 75%, and 50% of the observed effect show how the illustration changes when the target effect is smaller than the observed estimate. The smaller the effect targeted for detection, the more participants are needed under the same assumptions. In this trial, the observed primary effect is small on the risk-difference scale, and the planning figures are correspondingly large; they are not evidence that the trial had a particular probability of finding a result.

This is not observed power. The figures describe hypothetical future planning scenarios based on the observed effect, rather than a retrospective measure of the probability that the completed trial detected an effect.

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 = 0.063; treatment proportion p₁ = 0.070; average p̄ = 0.066.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3523 = 0.6905.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3523 = 0.2965.
4. n = (0.6905 + 0.2965)² / (0.0072)² = 19,019.5, rounded up to 19,020 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 <- 0.0629067245119306                          # control proportion
p1 <- 0.0700636942675159                          # 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(2202577)
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 = 19,020 (80% power), 25,462 (90% power)
 75% of observed effect: n per arm = 33,391 (80% power), 44,700 (90% power)
 50% of observed effect: n per arm = 74,176 (80% power), 99,300 (90% power)
power.prop.test: 19019.5 
Simulated power at n = 19,020 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. Analyses Reported by the Sponsor

The registry lists two sponsor-reported Fisher Exact analyses for the primary endpoint. Both are presented as risk ratios: one estimate is 0.90 with a reported 95% upper confidence limit of 1.35 and p = 0.38; the other is 0.83 with a reported 95% upper confidence limit of 1.25 and p = 0.26. Lower confidence limits are not reported in the registry record.

The recalculated comparison uses the posted event counts and arm sizes to estimate an unadjusted risk difference of 0.007, with a 95% confidence interval from -0.025 to 0.039 and p = 0.661. It is a simple recalculation from summary statistics and should not be mistaken for the sponsor's analysis. A risk difference and a risk ratio use different scales, and the registry does not identify which of its two reported analyses corresponds to a particular analysis population or purpose.

The record does not explain why there are two reported analyses, how their estimates were calculated, or how they relate to the recalculation. The discrepancy flag is false, but that does not fill in the missing methodological explanation. The figures are best read as distinct reported results, with no unsupported attempt to reconcile them.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary infection outcome and one secondary outcome, as well as two analyses for the primary endpoint. The record does not describe a prespecified strategy for handling multiple analyses or multiple outcomes. It also does not explain the reason for listing two primary analyses. Without that information, the extent to which the reported p-values were planned as confirmatory tests, or whether any adjustment for multiplicity was intended, is not reported in the registry record.

General statistical context: when multiple hypotheses are tested, the chance of at least one apparently unusual result can increase. Procedures for controlling multiplicity may be used to preserve a chosen overall error rate, or results may be interpreted as exploratory. The appropriate interpretation depends on the protocol and statistical analysis plan. Neither is described in enough detail in the registry record to determine the intended approach.

The record does not report which participants were included in each analysis, whether the analyses followed an intention-to-treat principle, or how exclusions after randomization were handled. It does not provide missing-data counts, describe loss to follow-up, or state how unknown outcome status was treated. These details matter because the primary outcome depends on whether infection was ascertained within 4 weeks for participants in each arm.

There is also no reported description of interim analyses, stopping rules, subgroup analyses, or covariate adjustment. These are not assumed to have occurred; their details are simply not reported in the registry record. The randomized design is identified, but the available record does not establish every element needed to evaluate the prespecification, completeness, and analysis population underlying the posted results.

These omissions do not change the arithmetic of the posted counts or recalculated estimates. They do limit assessment of how completely those summaries represent the trial and how the reported analyses were selected. Accordingly, the posted results support a descriptive comparison, while stronger claims about confirmatory testing or robustness require information not reported in 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 0% reporting threshold.

The adverse-event record lists 0 serious adverse events and 0 other adverse events in the chlorhexidine-isopropyl alcohol arm, among 461 participants at risk. It likewise lists 0 serious adverse events and 0 other adverse events in the povidone-iodine arm, among 471 participants at risk. Deaths are recorded as 0 in each arm.

These entries describe what is recorded in the registry's adverse-event fields. They should not be read as proof that no adverse effects occurred or that the preparations have identical safety profiles. The record does not provide a list of serious adverse event terms, and it does not report further detail about ascertainment, duration of safety monitoring, or the completeness of event reporting.

General statistical context: observing zero events in a trial does not establish that an event is impossible or that the underlying risk is zero. The size of the study and the way events were collected affect how much can be inferred from a zero count. The posted safety figures are therefore limited to the adverse-event summary recorded for these trial arms.

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

The posted data describe a randomized comparison of two pre-operative skin preparations before cesarean delivery. The primary outcome was the number of participants with surgical site infection by CDC criteria within 4 weeks after delivery. The observed arm counts and the unadjusted recalculation do not provide a clear statistical distinction between the preparations, and the confidence interval permits effects in either direction.

That finding is not proof that the preparations are equivalent, nor does it show that any possible difference is too small to matter. Equivalence or non-inferiority requires a suitable design and a prespecified margin, neither of which is reported in the registry record. The registry's stated superiority hypothesis is not itself evidence that superiority was demonstrated.

The findings also do not establish what would happen for other surgical procedures, different populations, other skin-preparation protocols, or outcomes beyond the stated timeframe. The record reports a secondary complication outcome and adverse-event summaries, but these entries do not answer every question about efficacy or safety. Details of missing data and the analysis populations are not reported, which limits a full assessment of the results.

General statistical context: a nonsignificant test does not show that there is no effect. It means that the data did not provide strong evidence against the test's null model under the method used. Estimates and confidence intervals are more informative about the range and precision of plausible effects, but interpretation also depends on study design, measurement quality, and clinical context. That context cannot be posted by the registry results alone.

The defensible conclusion is descriptive: the trial recorded the stated infection counts in each arm, and the posted analyses do not show a clear between-arm difference. They do not settle whether a clinically important difference exists, establish identical outcomes, or support a general recommendation. Those conclusions would require evidence and contextual information beyond the statistics reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be interpreted through both its event counts and its uncertainty. A difference between observed counts does not by itself show a reliable difference in risk; arm sizes, the effect scale, and the interval around the estimate all matter. Here the recalculated risk difference is accompanied by an interval that includes zero and extends in both directions, underscoring that the direction and size of any underlying difference remain uncertain.

It also demonstrates why sponsor-reported analyses and transparent recalculations should be described separately. The registry lists two Fisher Exact risk-ratio results, while the simple recalculation reports a risk difference from the posted summary statistics. These are not the same measure or necessarily the same analysis. Since the record does not explain the two entries, careful reporting avoids treating them as a single result or inventing a reconciliation.

Planning illustrations based on an observed effect can also be useful for understanding how effect size relates to sample requirements, but they are not a substitute for the original design rationale. In this case the trial's own sample-size justification is not reported. The illustrations are hypothetical and do not indicate the trial's observed power.

Finally, the record highlights how interpretation depends on information beyond the point estimate: analysis populations, missing outcomes, endpoint assessment, and multiplicity plans all contribute to evaluating trial evidence. Their absence from the registry record should qualify the strength of conclusions drawn from the posted results.

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 registry record does not report the original sample-size justification or the assumptions used to design the trial. The sample-size illustrations are based on the observed effect and should not be mistaken for the trial's planned enrollment target or a retrospective assessment of power.

The record does not describe the randomization sequence, allocation concealment, or whether outcome assessors were masked. It identifies no masking, but does not clarify whether any specific assessments were conducted by masked personnel. Details of infection adjudication beyond the named CDC criteria are also not reported.

Missing outcome information and analysis populations are not described. Without those details, it is not possible to assess from the registry record whether all randomized participants were included in each outcome analysis, how unknown outcome status was handled, or whether follow-up was complete. The record also does not report protocol deviations or participant withdrawals.

The registry lists two Fisher Exact analyses for the primary outcome without explaining their distinction, and lower confidence limits are absent from both reported risk-ratio entries. No multiplicity strategy, interim-analysis plan, or adjusted analysis is described. These omissions constrain interpretation of the inferential results and their relationship to a prespecified analysis plan.

Finally, the primary endpoint has a stated 4-week timeframe, so it does not address later outcomes. The registry's posted safety summary records zero events in its adverse-event categories, but supplies no detailed event terms or further monitoring information. These are limits of what the registry record reports, not evidence that other events or analyses did or did not occur.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Chlorhexidine-Alcohol Versus Povidone-Iodine for Cesarean Antisepsis — NCT02202577.
• Registry record last updated 2022-07-21; status last verified 2022-07.
• Results first posted 2022-07-21.
• 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

NCT02202577 is a completed randomized, parallel-group trial comparing chlorhexidine-isopropyl alcohol with povidone-iodine scrub and paint for pre-operative skin preparation before cesarean delivery. The registry lists enrollment of 932 participants and no masking.

The primary endpoint was participants with CDC-defined surgical site infection within 4 weeks after delivery. The arm counts were 29 of 461 and 33 of 471. The unadjusted recalculated risk difference is 0.007, with a 95% confidence interval from -0.025 to 0.039 and p = 0.661. The registry also lists two Fisher Exact risk-ratio analyses, but does not explain their distinction.

The posted results do not show a clear statistical separation between the preparations. The record does not report the original design assumptions, analysis populations, missing-data methods, or multiplicity plan, limiting assessment beyond the posted summaries.