Cystoinflation to Prevent Bladder Injury in Obstetrics and Gynaecology Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cystoinflation to Prevent Bladder Injury in Obstetrics and Gynaecology Surgery (NCT04302545), a randomized na study. The primary outcome is Bladder Injury Rate.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-masked, parallel-group study, with an overall enrollment of 564 and a completed status. The record lists the study start as 2017-08-01 and primary completion as 2021-04-30. It identifies three parts: cystoinflation in repeat cesarean section, abdominal hysterectomy, and placenta accreta spectrum management. The brief summary says summaries for Parts 2 and 3 would be provided after publication; the posted results are for the repeat cesarean section comparison.

The intervention was a procedure rather than a drug. In the cystoinflation group, the bladder was retro-filled with 300cc saline during adhesiolysis; in the control group, adhesiolysis was performed without retrofill. The primary outcome was bladder injury, detected by direct visualization during the operation. The posted primary outcome groups each include 107.0 participants. The record does not explain how this outcome subset relates to the overall enrollment, nor does it report the sequence-generation method, allocation concealment, or how masking was maintained for participants and surgical staff.

Although the registry labels the study double-masked, the practical details of masking are not reported in the registry record. The registry also does not report the original sample-size justification or the protocol’s planned statistical analysis in enough detail to assess whether the posted analyses follow that plan. Those omissions matter when judging the design and analysis, but they do not change the basic randomized comparison described in the 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: Subjects admitted with full term pregnancy and previous 2 C-sections n=734 The study subjects were selected in two step assessment(a)preoperative (during operation). preoperatively Excluded n=346 due to medical disorders, placenta previa, bladder injury before group assignment, micturition problems before operation Declined to participate=5 During operation Excluded=174 as criteria of dense adhesions of bladder was not met with.

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.

Population: This study included Pakistani women eighteen years and above, coming to Lady Willingdon hospital for elective caesarean section due to the previous two or more C-sections, with no major medical disorder and found to have dense bladder adhesions on opening the abdomen; recognition of bladder was difficult due to overlying adhesions

6. Primary Endpoint

The registry lists the primary outcome as Bladder Injury Rate, measured over From the confirmation of adhesions to adhesiolysis and separation of bladder flap from uterus, before delivery of the baby during cesarean section.This time frame can range between 10-20 minutes..

The primary endpoint is the count of participants with bladder injury during adhesiolysis and separation of the bladder flap from the uterus, before delivery of the baby during cesarean section. The registry describes detection by direct visualization. The assessment window begins when adhesions are confirmed and ends after adhesiolysis and bladder-flap separation; the record says this period can range between 10-20 minutes.

This endpoint addresses the immediate surgical complication that the procedure is intended to help identify and avoid during dissection. Recording the number of participants with injury gives a binary outcome at the participant level: each participant either had a recorded bladder injury or did not. The posted results give the number with injury in each group and a comparison of the groups’ risks.

The endpoint is specific to the operative period and does not by itself summarize all potential benefits or harms of the procedure. Other outcomes listed in the record include blood loss, operating time, urinary tract infection, micturition problems, and fistula formation, as well as further postoperative measures. A primary endpoint provides a defined main comparison, but interpretation still depends on the quality and completeness of outcome ascertainment and the analysis plan. Details of adjudication, assessor masking, and missing primary-outcome data are not reported in the registry record.

7. Results Posted in the Registry

• Cystoinflation Group: 2.8% (3/107) versus 20.6% (22/107) on control; risk difference -17.8 percentage points (95% CI -26.0 to -9.5), risk ratio 0.14 (0.04–0.44); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

White Blood Cells Count Per High Power Feild

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Cystinflation Group: mean 6.26 versus 7.36 on control; difference -1.10 (95% CI -1.71 to -0.49), standardized effect d = -0.48; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Cystinflation Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Urine Culture Report for Micro-organisms

• 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:
  • Cystoinflation Group: 1.9% (2/107) versus 16.8% (18/107) on control; risk difference -15.0 percentage points (95% CI -22.5 to -7.4), risk ratio 0.11 (0.03–0.47); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Cystoinflation Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Fever

• 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:
  • Cystoinflation Group: 1.9% (2/107) versus 12.1% (13/107) on control; risk difference -10.3 percentage points (95% CI -17.0 to -3.6), risk ratio 0.15 (0.04–0.67); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Cystoinflation Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover postoperative blood counts, urine culture, fever, and other measures of urinary function, catheterization, hospital stay, and fistula formation. For the secondary outcomes with posted numerical results, the cystoinflation group has lower recorded values or event counts than the control group. This broad direction is consistent with, but does not independently establish, the primary comparison’s direction. The record lists more secondary outcomes than it provides detailed numerical results for, so the overall pattern cannot be evaluated across every planned or recorded outcome.

Secondary outcomes can help describe the wider course of recovery and potential complications, but they differ in definition, measurement scale, and follow-up timing. A postoperative laboratory measurement is not equivalent to a participant-level clinical event, and an outcome assessed over a longer period is not directly interchangeable with an intraoperative injury endpoint. Their findings therefore add context rather than serving as substitutes for the primary result.

The registry record does not report a multiplicity adjustment or explain whether these secondary comparisons were prespecified. When many outcomes are examined, some may appear statistically notable by chance, especially if each is assessed with an unadjusted test. For that reason, the secondary findings carry less confirmatory weight than a clearly prespecified primary analysis. The record also does not report how missing data were handled for each outcome, which limits comparison across endpoints and follow-up times.

The stated summaries for Parts 2 and 3 were to be provided after publication; they are not included in the posted results. The available secondary outcomes therefore should not be taken as a complete account of all three parts of the study.

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

• White Blood Cells Count Per High Power Feild
• Urine Culture Report for Micro-organisms
• Fever
• Postmicturition Bladder Volume After C-section
• Composite Micturition Problems During Hospital Stay
• Duration of Urinary Catheterization
• Duration of Hospital Stay
• Number of Subjects With Urinary Fistula Formation

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant is classified according to whether a bladder injury was recorded. For such an outcome, the observed event count is interpreted relative to the number of participants in the group. The comparison reported as a risk difference subtracts the control-group risk from the cystoinflation-group risk. A negative value means the observed risk was lower in the cystoinflation group; a value of zero would represent equal observed risks. The estimate of -0.178 is an absolute contrast on the risk scale, not an odds ratio.

What does the confidence interval describe?

A confidence interval expresses the statistical uncertainty around an estimated group contrast under the assumptions of the method used. For the primary risk difference, the 95% interval runs from -0.260 to -0.095. Its endpoints represent values of the underlying contrast compatible with the observed data and calculation method at the stated confidence level. The interval does not describe the range of individual participant outcomes, and it does not account automatically for potential bias, missing outcome data, or choices made in an analysis plan.

The unadjusted p-value for the recalculated primary comparison is p < 0.001. In general, a p-value measures how incompatible the observed data are with a specified null hypothesis under the statistical model; it is not the probability that the null hypothesis is true, nor a measure of the size or importance of an effect. The registry’s sponsor analysis reports p < .0001. Differences in precision or method can affect reported p-values, so the two results should be described as the posted sponsor analysis and the unadjusted re-calculation rather than merged into a single result.

Why use an absolute contrast?

The risk difference communicates the between-group contrast in the probability of an event on an absolute scale. Relative measures such as a risk ratio or odds ratio compare groups on multiplicative scales. These measures can be useful, but they can appear more or less striking depending on the baseline risk and do not substitute for the underlying event counts. The group counts and denominator are therefore important context for understanding any summary measure.

The recalculated comparison is unadjusted: it uses the posted summary counts and does not control for other variables. Randomization is intended to balance prognostic factors across groups, but the registry record does not provide a baseline table or details sufficient to assess balance. The record labels the sponsor’s method “Regression, Linear” and its parameter “Odds Ratio (OR).” The estimate and confidence limits are negative, which is not the usual scale for an odds ratio. The registry record does not clarify the parameterization, so the reported label should be retained as a description of the record rather than taken as proof that the estimate is an odds ratio.

What can the secondary analyses add?

The registry posts secondary outcomes measured on different scales and at different times. For continuous measurements, such as the white blood cell count, a mean difference compares group averages. For binary outcomes, such as positive urine culture or fever, event counts and risk differences compare the proportion of participants with an event. These are distinct outcome types, and their estimates should not be read as if they were interchangeable. Each estimate also has its own uncertainty and can be affected by the way the outcome was measured.

General statistical consideration: when a study examines multiple outcomes, the chance of obtaining one or more apparently unusual results can increase if every comparison is tested separately without adjustment. The registry does not report a multiplicity strategy. Consequently, unadjusted secondary p-values should be viewed as exploratory evidence rather than as definitive confirmation. The record also does not report whether the secondary analyses were prespecified, how missing values were handled, or whether any model assumptions were checked.

What is not established by the posted analysis?

The registry record does not report the original sample-size justification, interim analyses, or a complete statistical analysis plan. It also does not report the analysis population definition, handling of withdrawals, or whether all randomized participants contributed to each outcome. These details are needed to judge the analysis fully. The simple recalculation is transparent about its basis—the posted group summaries—but it cannot recover individual-level information or substitute for details that are not reported in the registry record.

11. Confidence Intervals and Precision

For the primary risk difference, the 95% confidence interval extends from -0.260 to -0.095 around the estimate of -0.178. Because the interval stays below zero, the posted summary counts support a lower observed risk in the cystoinflation group under the unadjusted calculation. The interval also makes clear that the estimate is not exact: a range of contrasts remains compatible with the data and method.

Confidence intervals describe sampling uncertainty, not all sources of uncertainty. They do not account for systematic differences in how injuries were detected, errors in data entry, unreported exclusions, missing outcomes, or departures from the planned protocol. The registry record does not provide enough information to evaluate these issues. The endpoint was assessed by direct visualization, but the record does not describe who assessed injuries or whether that assessment was masked to group.

The sponsor’s interval is reported as -.261 to -.094 with a 95% confidence level, and its estimate is -.178. These values are close to the recalculated risk-difference estimate and interval, but the sponsor analysis is labeled as an odds ratio despite the negative scale. This labeling ambiguity limits direct interpretation of the sponsor statistic. The posted count-based re-calculation is expressed as a risk difference, which makes its direction and scale explicit.

Precision should not be judged from a p-value alone. A small p-value does not mean that the estimate has negligible uncertainty or that the result is free from bias. Conversely, an interval communicates both the direction and a range of plausible effect sizes under the calculation assumptions. The event counts, interval, and reporting limitations together provide a more complete account of what the primary data can support.

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 justification. For these binary outcomes, the listed values 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 planned number of participants per arm for a design with an 80% chance of detecting the specified effect if that effect is the true one, under the planning assumptions. The 90% power column gives the corresponding number for a 90% chance. These are design probabilities under assumptions, not probabilities that the observed result is correct. For the primary outcome, the planning illustration lists 51 participants per arm for 80% power and 67 for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, it lists 105 and 140; for 50%, 269 and 359.

The pattern reflects a general principle: smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants. The figures are conditional on the stated assumptions and the observed effect used as a reference. They should not be read as evidence that the completed trial had a particular probability of success. This is not observed power.

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 = 0.206; treatment proportion p₁ = 0.028; average p̄ = 0.117.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4543 = 0.8903.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4366 = 0.3674.
4. n = (0.8903 + 0.3674)² / (-0.1776)² = 50.2, rounded up to 51 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 <- 0.205607476635514                          # control proportion
p1 <- 0.0280373831775701                          # 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(4302545)
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 = 51 (80% power), 67 (90% power)
 75% of observed effect: n per arm = 105 (80% power), 140 (90% power)
 50% of observed effect: n per arm = 269 (80% power), 359 (90% power)
power.prop.test: 50.2 
Simulated power at n = 51 per arm: 0.853 (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’s sponsor-reported primary analysis lists “Regression, Linear,” labels the parameter “Odds Ratio (OR),” and gives an estimate of -.178, a 95% confidence interval from -.261 to -.094, and p < .0001. The negative estimate and negative interval do not have the usual scale of an odds ratio, which is ordinarily positive. The registry record does not explain this mismatch, so the displayed parameter label and numerical result cannot be reconciled from the record alone.

The simple unadjusted re-calculation from the posted group counts gives a risk difference of -0.178, a 95% confidence interval from -0.260 to -0.095, and p < 0.001. Its estimate and interval are close to the sponsor-reported numerical values, but the re-calculation is explicitly on the risk-difference scale. The registry’s discrepancy flag is false, and the reported values are broadly aligned numerically; that does not remove the scale-label ambiguity.

The sponsor analysis is the registry’s own analysis, while the re-calculation is an unadjusted calculation from the posted summary statistics. The registry does not report enough model detail to determine whether the sponsor analysis adjusted for covariates or used a different parameterization. Accordingly, these results should be described separately rather than treating the sponsor estimate as a conventional odds ratio or assuming that the two analyses are identical.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and several secondary outcomes, but it does not report a multiplicity strategy. Multiplicity arises when several outcomes or comparisons are tested: if each test is judged independently using the same threshold, the chance of at least one apparently significant result can rise. General statistical practice may address this through prespecified outcome hierarchies, adjusted thresholds, or a clearly exploratory interpretation. Which, if any, approach was used in this trial is not reported in the registry record.

The record lists 12 outcome measures and 11 analyses, while detailed posted results include the primary outcome and some secondary outcomes. It does not explain why the analysis count differs from the outcome-measure count, which endpoints were analyzed but not reported, or whether the set of reported results is complete. These gaps make it difficult to assess selective outcome reporting or to understand how the analyses relate to the original plan.

Missing-data handling is also not reported. The record does not state whether every randomized participant was included in each analysis, whether any participants withdrew or had incomplete measurements, or how missing outcomes were treated. Nor does it define an intention-to-treat or per-protocol analysis population. Without these details, the posted group denominators cannot by themselves establish that all randomized participants contributed to every outcome.

The registry describes randomization and double masking, but operational details are not reported. Allocation concealment, the masking process, and the role of masked assessors are not described. The original sample-size justification, interim analyses, and full statistical analysis plan are also not reported in the registry record. These are reporting limitations; they do not prove that the methods were inadequate, but they prevent a full assessment of prespecification, analysis conduct, and the risk of bias.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: bladder injury (20.6%).

The adverse-event record lists serious adverse events in 3 of 107 participants in the Cystoinflation Group and 22 of 107 participants in the Control Group. Bladder injury is the leading serious-event term listed, at 20.6%. The serious-event counts align with the primary outcome counts, but the registry does not explain the relationship between the adverse-event classification and the primary endpoint beyond the shared injury description.

Other adverse events are listed for 0 of 107 participants in the cystoinflation group and 1 of 107 in the control group. No deaths are listed in either group. These figures describe the events recorded in the registry, not every possible adverse effect or the full safety profile of the procedure. The record does not give detailed definitions, severity grading, relatedness assessment, or information on how adverse events were collected. The different event counts should be interpreted in the context of those reporting limits and the study population.

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

The posted primary data show fewer recorded bladder injuries in the cystoinflation group than in the control group among the outcome groups reported for repeat cesarean section. The unadjusted risk difference is -0.178, with a 95% confidence interval from -0.260 to -0.095. This is a comparison of the observed groups, not a prediction for every individual or every surgical setting.

The trial’s randomized design can support a causal comparison in principle, but confidence in that interpretation depends on conduct and analysis details that are not reported in the registry record. In particular, the record does not clarify the analysis population, missing-data handling, masking procedures, or the complete prespecified statistical plan. The estimates also reflect the posted outcome groups and should not automatically be generalized to the other parts of the trial, since results for abdominal hysterectomy and placenta accreta spectrum management are not included in the posted summaries.

The result does not establish why the groups differed, whether the same contrast would occur in other hospitals or patient populations, or how the procedure compares with alternatives not studied in this randomized comparison. It also does not settle every relevant outcome: bladder injury is the primary endpoint, while urinary, postoperative, and other outcomes have distinct definitions and levels of reporting. Statistical evidence of a group difference is not the same as a complete account of benefit, harm, feasibility, or clinical importance.

General interpretation: an estimate is most useful when read with its uncertainty, the design, the outcome definition, and the quality of reporting. Here, the event counts and risk-difference interval point in the same direction, but unreported methodological details and the limited posted results constrain how broadly the result can be applied.

18. Why This Trial Matters Statistically

This trial presents a useful statistical example of a randomized comparison with a binary surgical outcome. The group counts are easy to understand, while the risk difference expresses the absolute contrast and the confidence interval shows uncertainty around it. Reading these together is more informative than relying on a significance threshold alone.

It also illustrates why effect-measure labels matter. The sponsor’s analysis is labeled as an odds ratio, but its estimate and confidence limits are negative. Those values are not on the usual odds-ratio scale, while the unadjusted recalculation is explicitly a risk difference. Clear naming of the estimand and model would make the result easier to interpret and reproduce.

The record includes multiple outcome measures and results from only part of a multi-part study. This makes transparency about prespecification, multiplicity, missing data, and analysis populations especially important. Without these details, readers can describe the posted comparisons but cannot fully judge whether all planned analyses are represented or how strongly secondary findings should be treated.

Finally, the sample-size illustrations show how planning depends on the effect a future study aims to detect. Planning for a smaller effect requires more participants than planning around the full observed contrast. These calculations are informative as conditional design examples, but they are distinct from the trial’s original sample-size rationale, which is not reported in the registry record.

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 posted primary outcome results cover the repeat cesarean section part of a study whose official title also includes abdominal hysterectomy and placenta accreta spectrum management. The brief summary says information for Parts 2 and 3 would be provided after publication, and their results are not included in the posted material. The findings described for this comparison therefore cannot be assumed to represent those other surgical settings.

The registry does not report how the overall enrollment of 564 relates to the 107.0 participants in each primary-outcome group. It also does not state how many participants had dense adhesions, whether any randomized participants were excluded from the outcome analysis, or whether the denominators reflect all randomized participants. This limits assessment of the analysis population and generalizability.

Details that would help assess potential bias are absent, including the randomization sequence and concealment, how double masking was maintained during a procedure, who assessed injury, and whether outcome assessors were masked. Missing-data handling, withdrawals, protocol deviations, interim analyses, and the original sample-size justification are not reported in the registry record. The record also does not provide a complete statistical analysis plan or a multiplicity strategy.

The sponsor’s reported primary analysis is labeled as an odds ratio but gives a negative estimate and negative confidence limits, leaving the effect-measure scale unclear. The unadjusted recalculation from group counts is interpretable as a risk difference, but it cannot resolve the sponsor analysis’s parameterization or recover adjustments that may have been used. Secondary outcomes also have incomplete posted coverage, and the record does not describe the completeness of outcome reporting.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Cystoinflation to Prevent Bladder Injury in Obstetrics and Gynaecology Surgery — NCT04302545.
• Registry record last updated 2024-09-04; status last verified 2024-08.
• Results first posted 2021-09-28.
• 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

NCT04302545 is a completed randomized, double-masked, parallel-group study of cystoinflation to prevent bladder injury in obstetrics and gynecology surgery. The record lists overall enrollment of 564 and includes three study parts. The posted primary comparison concerns repeat cesarean section among women with dense pelvic adhesions: cystoinflation with 300cc saline retrofill versus adhesiolysis without retrofill.

Bladder injury was assessed by direct visualization during adhesiolysis before delivery. The posted outcome groups each include 107.0 participants, with 3.0 injuries in the cystoinflation group and 22.0 in control. The unadjusted risk difference is -0.178, with a 95% confidence interval from -0.260 to -0.095 and p < 0.001. The registry’s sponsor analysis reports a numerically similar estimate but labels it as an odds ratio despite a negative scale.

Results for the other study parts, original design assumptions, full analysis plan, and key details about missing data and analysis populations are not reported in the registry record.