Urinary Retention After Total Laparoscopic Hysterectomy With Immediate Foley Catheter Removal Versus Backfill Void Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Urinary Retention After Total Laparoscopic Hysterectomy With Immediate Foley Catheter Removal Versus Backfill Void Trial (NCT03141372), a randomized na study. The primary outcome is Number of Participants With Void Trial Failure Rate.

2. Clinical Question

The clinical question is whether the method used to assess voiding after total laparoscopic hysterectomy is associated with a different rate of void trial failure. The registry describes a comparison between an autofill void trial and a backfill void trial, with failure assessed after surgery.

The registry describes failure in relation to the voiding assessment and a PVR threshold of > 100 mL in the available arm descriptions. Those descriptions end before all criteria are stated, so the full failure definition is not reported in the registry record. The question is about the comparative rate of this short-term endpoint, not a broader measure of long-term bladder function.

3. Trial Design

This was a randomized, parallel-group trial with no masking. The registry lists enrollment of 84 and a completed status. The posted primary endpoint results are reported for 42 participants in the autofill arm and 40 in the backfill arm. The registry record does not explain how the enrollment figure relates to the endpoint denominators.

The comparison was between two post-operative void trial approaches following total laparoscopic hysterectomy. In the autofill arm, participants were allowed to urinate within the first 3 hours after surgery. The description says the amount urinated was recorded using a commode specimen collection measurer and that PVR was measured. In the backfill arm, about 300 mL of fluid was instilled into the bladder, the Foley catheter was removed, and participants had up to 1 hour to urinate; the amount and PVR were then recorded. The descriptions of both arms are incomplete in the registry record, so additional details of the procedures and failure criteria are not reported in the registry record.

The primary endpoint was the number of participants with void trial failure, assessed post-operatively, about 4 hours after surgery. The registry also lists outcomes involving urinary retention, post-operative urinary tract infection, satisfaction, time to discharge, quality of bladder function, and perception of bladder condition. Results are posted for some, but not all, of these secondary outcomes.

The registry record does not report the randomization sequence method, allocation concealment, sample-size justification for the original trial, or a detailed statistical analysis plan. The record also does not report an analysis population definition or the handling of missing outcome data. These omissions limit assessment of how the study was planned and how participants with unavailable outcomes were handled.

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

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 Void Trial Failure Rate, measured over post-operative day, about 4 hours post-surgery.

The primary endpoint counts participants whose void trial was classified as a failure after total laparoscopic hysterectomy. The endpoint was assessed post-operatively, about 4 hours after surgery. Its purpose is to capture whether a participant met the study’s stated criteria for successfully completing the void trial, making it a direct measure of the immediate post-operative bladder challenge being compared.

The registry’s objective frames the endpoint as a comparison of failure rates between the autofill and backfill methods. The available arm descriptions mention measuring PVR and identify a threshold of > 100 mL, but the descriptions are incomplete. The full criteria for failure are therefore not reported in the registry record. Interpretation should remain tied to the posted endpoint rather than assuming that it represents every aspect of urinary function.

A count of participants with failure can be compared across randomized groups as a binary outcome: each participant is classified as having or not having the event. The posted counts are 7 among 42 in the autofill arm and 11 among 40 in the backfill arm. These counts describe the trial observations; by themselves, they do not establish the size or precision of a difference in the broader population. The comparison estimate and its confidence interval provide additional information about that uncertainty.

7. Results Posted in the Registry

• Backfill Void Trial: 27.5% (11/40) versus 16.7% (7/42) on control; risk difference 10.8 percentage points (95% CI -7.0 to 28.7), risk ratio 1.65 (0.71–3.83); unadjusted two-proportion z-test p = 0.236.

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 Urinary Retention

• 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:
  • Backfill Void Trial: 2.5% (1/40) versus 2.4% (1/42) on control; risk difference 0.1 percentage points (95% CI -6.6 to 6.8), risk ratio 1.05 (0.07–16.23); unadjusted two-proportion z-test p = 0.972.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Backfill Void Trial and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Post-Operative Urinary Tract Infection

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Backfill Void Trial: 2.5% (1/40) versus 4.8% (2/42) on control; risk difference -2.3 percentage points (95% CI -10.3 to 5.8), risk ratio 0.53 (0.05–5.57); unadjusted two-proportion z-test p = 0.586.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Backfill Void Trial and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Satisfied or Very Satisfied With Void Trial Using 5 Point Lickert Scale

• 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:
  • Backfill Void Trial: 75.0% (30/40) versus 92.9% (39/42) on control; risk difference -17.9 percentage points (95% CI -33.4 to -2.3), risk ratio 0.81 (0.66–0.98); unadjusted two-proportion z-test p = 0.027.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Backfill Void Trial than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the focus beyond immediate void trial failure. They include later urinary retention, post-operative urinary tract infection, satisfaction with the void trial, time to discharge, quality of bladder function, and perceived bladder condition. The registry lists six secondary outcomes, but results are posted for only three of them in the record represented by these results. Results for time to discharge, quality of bladder function using the Incontinence Impact Questionnaire, and patient perception of bladder condition are not reported in the registry record.

Across the secondary outcomes with posted values, the pattern is not uniform: some comparisons show very little separation in the observed counts, while another shows a more noticeable difference in participant-reported satisfaction. This variation does not form a single consistent signal that independently resolves the primary comparison. The outcomes concern different events, experiences, and follow-up times, so they should not be treated as interchangeable measures of one underlying result.

These secondary findings relate to the primary endpoint by offering additional information about follow-up and participant experience, but they do not answer the same question as post-operative void trial failure. Their interpretation also depends on endpoint definitions, data completeness, and analysis choices that are not fully described in the registry record. No reported secondary analyses are listed, and the record does not report a prespecified testing hierarchy or a multiplicity adjustment.

When several outcomes are examined, the chance of seeing an apparently unusual result somewhere among them can increase. In general, multiplicity procedures or a clearly prespecified hierarchy can help distinguish confirmatory tests from exploratory comparisons. Without those details, unadjusted secondary results carry less weight than a single prespecified primary endpoint and should be treated as hypothesis-generating rather than as definitive evidence. This does not mean the findings are uninformative; it means their uncertainty and the possibility of chance findings should remain visible in interpretation.

Unreported secondary outcomes should not be assumed to have had null results or to have been omitted for a particular reason. Their results and the reasons they are absent are not reported in the registry record.

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

• Time to Discharge
• Number of Patients With Urinary Retention
• Number of Participants With Post-Operative Urinary Tract Infection
• Quality of Bladder Function Using the Incontinence Impact Questionnaire
• Patient Perception of Bladder Condition Score
• Number of Participants Satisfied or Very Satisfied With Void Trial Using 5 Point Lickert Scale

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: a participant either had a void trial failure recorded or did not. A natural comparison for a binary endpoint is the difference between the two groups’ event proportions. The posted risk difference compares backfill with autofill and is 0.108. A positive value means the observed event proportion is higher in the backfill group under this comparison’s direction; it is a descriptive contrast, not a statement that the method caused an outcome for any individual participant.

A confidence interval expresses the uncertainty around an estimated contrast. In general, it gives a range of values that are reasonably compatible with the observed data under the statistical procedure used. The primary interval runs from -0.070 to 0.287. Because it includes zero, it includes no difference as one compatible possibility. It also spans positive and negative values, so it leaves uncertainty about both the direction and magnitude of the underlying contrast. The registry record does not report the confidence-interval method or the analysis model used to obtain the posted estimate.

A p-value measures how incompatible the observed data are with a specified null hypothesis under a statistical model. It is not the probability that the null hypothesis is true, nor is it a measure of the clinical importance of an estimate. The posted primary unadjusted p-value is 0.236. The record does not report a statistical analysis plan specifying the test, sidedness, or any adjustment for covariates. The p-value should therefore be read as the posted unadjusted comparison rather than as a complete account of the analysis strategy.

What does a risk difference express?

In general, a risk difference is the event proportion in one group minus the event proportion in the other, with the group order determining the sign. It keeps the contrast on an absolute scale: it describes how far apart the observed proportions are, rather than how many times one is the other. Here, the recorded comparison is backfill relative to autofill. The reported point estimate and interval should be read using that direction. No additional calculation is needed to interpret the sign.

How should the interval and p-value be read together?

The confidence interval displays a range of plausible effect values, while the p-value summarizes compatibility with a particular null hypothesis under a test. They are related but do not answer identical questions. A result can be imprecise even when its point estimate is not zero. In this trial, the interval covers zero and values in both directions, and the posted p-value is 0.236. Neither quantity establishes that the methods are the same. Demonstrating equivalence or non-inferiority would require a prespecified margin and analysis framework, which are not reported in the registry record.

What can randomization contribute?

In general, random assignment is intended to make comparison groups similar, on average, with respect to factors that could influence the outcome. That design can support causal interpretation when assignment is implemented appropriately, outcome data are handled transparently, and analysis follows a suitable plan. The registry identifies the study as randomized, but details about sequence generation and allocation concealment are not reported in the registry record. It also does not report the analysis population or missing-data procedures. Randomization is relevant to interpretation, but the label alone does not resolve these unanswered questions.

Why does the event-count scale matter?

With binary outcomes, each participant contributes an event status rather than a measured value on a continuous scale. The precision of a group comparison depends on the number of participants and on how frequently the event occurs. When events are uncommon, the observed count can change noticeably with only a small number of participants changing status. The primary groups contain 42 and 40 participants, and the event counts are 7 and 11. These counts give the context needed to understand why the interval is not narrow; they do not justify a conclusion about the outcome beyond the observed comparison.

Other reported measures include risk ratios and odds ratios for some endpoints. In general, these are relative measures: they compare event occurrence using a ratio rather than an absolute difference. Relative measures can look more or less striking depending on the event frequency, so they should be interpreted alongside event counts and absolute measures. For the primary endpoint, the registry’s posted comparison is framed as a risk difference; a sponsor-reported primary analysis model is not reported in the registry record.

Planning calculations use a different purpose from outcome analysis. In general, they estimate how many participants might be required under chosen assumptions to detect a specified effect with a chosen power and significance level. They are not measurements of what happened in the trial and cannot repair imprecision in the observed result. The planning assumptions listed for this record are a two-sided significance level of 0.05, equal allocation between arms, a normal approximation, and an effect set to a stated fraction of the observed effect. The trial’s original design assumptions are not reported in the registry record.

The registry lists no reported analyses for the posted secondary outcomes. A blank or absent analysis record does not mean no analysis was conducted; it means the analysis details are not reported in the registry record. In particular, the statistical tests, confidence-interval methods, missing-data rules, and any multiplicity strategy for those outcomes are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.108 for backfill relative to autofill, with a 95% confidence interval from -0.070 to 0.287. The interval crosses zero and extends in both directions, so the observed data are compatible with no difference as well as with differences favoring either group. The point estimate alone should not be treated as the definitive size of the underlying effect.

In general, a confidence interval communicates sampling uncertainty: a wide interval signals that the data do not locate the underlying effect precisely. The primary interval is broad enough to include appreciable effects in either direction, so the posted result cannot tightly constrain what the group difference might be beyond this trial. The registry record does not state the confidence-interval construction method, which limits assessment of the assumptions behind that interval.

The event counts help explain why precision matters. There were 7 failures among 42 participants in the autofill group and 11 among 40 in the backfill group. With event counts of this size, the estimated contrast is sensitive to the pattern of observed events, and uncertainty remains substantial. The confidence interval should be considered together with the counts rather than replaced by a threshold judgment based only on the p-value.

For the secondary outcomes, intervals are also broad for several comparisons. In general, an interval that spans the null value indicates that the data do not rule out no difference under the stated measure and method. Such intervals should not be interpreted as proof of equal outcomes. Conversely, an interval that excludes the null does not on its own establish a robust finding when multiple outcomes are examined without a reported adjustment or prespecified hierarchy.

Precision is distinct from importance. The registry does not report a threshold for a clinically meaningful difference, so the posted interval cannot be evaluated against such a threshold. The result is best characterized as an uncertain estimate, not as a precise estimate of no difference.

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 planning figures describe participants per arm for the binary outcomes in this record; they are not total event counts. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The registry’s original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that a planning calculation estimates would be needed to have an 80% chance of detecting the selected effect under the stated assumptions, if that effect and those assumptions applied. The 90% power column uses a higher probability of detecting the selected effect, and therefore generally calls for more participants per arm. These are prospective planning interpretations, not descriptions of the enrollment achieved in this trial.

The rows use the observed effect at its full size, then at 75% and 50% of that effect. Smaller target effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm. The very large figures for some outcomes reflect the small observed differences used as planning targets; they should not be treated as evidence that those targets are stable or clinically important.

These calculations are illustrations based on the observed effect, not the trial’s own original design calculation. They are not observed power. They do not tell whether the trial’s result is true, whether a method is effective, or whether a future study will reproduce the observed effect. Their meaning depends on the assumptions listed and on the effect size chosen for planning.

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 = 0.167; treatment proportion p₁ = 0.275; average p̄ = 0.221.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5866 = 1.1498.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5816 = 0.4895.
4. n = (1.1498 + 0.4895)² / (0.1083)² = 229.0, rounded up to 229 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 <- 0.166666666666667                          # control proportion
p1 <- 0.275                          # 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(3141372)
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 = 229 (80% power), 307 (90% power)
 75% of observed effect: n per arm = 390 (80% power), 522 (90% power)
 50% of observed effect: n per arm = 835 (80% power), 1,117 (90% power)
power.prop.test: 229 
Simulated power at n = 229 per arm: 0.804 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists multiple secondary outcomes. Examining multiple outcomes can increase the chance of at least one result appearing notable by chance, even if no single comparison provides strong evidence. In general, a prespecified testing hierarchy or multiplicity adjustment can clarify which tests are confirmatory and how the overall error rate is handled. Neither a hierarchy nor an adjustment is reported in the registry record.

The registry record lists no reported analyses for the primary endpoint and no reported analyses for the secondary outcomes. This does not establish that no statistical work was done; it means the analysis details are not reported in the registry record. The record does not specify the primary test, the confidence-interval method, whether covariates were included, or whether any sensitivity analyses were planned or performed. It also does not report interim analyses or stopping rules.

Analysis populations are another important part of interpretation. The record lists enrollment of 84, while the primary endpoint arm counts are 42 and 40. It does not explain the relationship between enrollment and those outcome denominators. The record also does not state whether the analysis followed intention-to-treat, per-protocol, or another population definition. It does not report how participants with missing endpoint data were handled or whether any imputation was used. No reason for the difference in listed participant totals should be inferred.

Missing-data handling can affect estimates when outcome availability differs across participants or groups. In general, excluding participants with unavailable outcomes can change the groups represented in the analysis, while assumptions used to fill in missing values can also influence results. Without a description of outcome completeness and the analysis population, readers cannot assess whether the posted comparison may be sensitive to missingness.

The registry’s abbreviated procedural descriptions also limit assessment of how failure was classified in every circumstance. The available text mentions a PVR threshold but does not show the complete criteria. Together, the unreported analysis plan, missing-data procedures, population definition, multiplicity strategy, and complete endpoint rules constrain how far the posted findings can be interpreted.

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 42 participants at risk in the autofill arm and 40 in the backfill arm. The posted number affected by serious adverse events is 0 in each arm, and deaths are listed as 0 in each arm. The other adverse event counts are also listed as 0 for both groups.

These figures describe the events recorded in the registry for the reported groups. They do not demonstrate that no adverse events of any kind occurred outside the categories or reporting period captured in the record. The registry does not provide serious adverse event terms, and no serious event terms are listed. The available safety data should therefore be read as a description of the posted counts, not as proof of an absence of risk.

In general, safety comparisons are difficult to interpret when events are uncommon and group sizes are limited. A zero count is an observed count, not a guarantee that an event cannot occur. The registry record does not provide additional detail about adverse-event collection procedures or the period covered for these figures, so those details are not reported in the registry record.

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

The posted primary result describes a comparison of immediate post-operative void trial failure between two randomized groups. Failure was recorded for 7 participants in the autofill group and 11 in the backfill group. The risk-difference estimate is 0.108 for backfill relative to autofill, and its 95% confidence interval ranges from -0.070 to 0.287. The estimate is uncertain: the interval includes no difference and values in either direction.

This finding does not establish that one method is better, worse, or equivalent to the other. A non-small p-value is not proof of no effect, while a point estimate favoring one direction is not sufficient evidence that the underlying effect has that direction. The record does not provide a clinically meaningful difference threshold or an equivalence framework. Those omissions prevent a conclusion about whether any possible difference would matter in practice.

The endpoint is a short-term measure, assessed about 4 hours after surgery. It should not be interpreted as a complete measure of longer-term bladder function. The registry lists later urinary retention and participant-reported outcomes, but several listed outcomes do not have posted results. Even the outcomes with posted results have their own definitions and timeframes, and should not be substituted for the primary endpoint.

Randomization is a strength of the design in principle because it is intended to support comparable groups. However, details about randomization implementation, outcome completeness, and analysis populations are not reported in the registry record. The difference between the enrollment figure and primary outcome denominators is unexplained. These limitations leave uncertainty about how fully the posted comparison represents all enrolled participants.

The results apply to the trial groups and endpoints described in the registry record. They do not by themselves establish what would occur in other settings or populations, and they do not provide a basis for individual medical decisions. The appropriate statistical conclusion is limited: the observed primary comparison is imprecise and does not clearly distinguish the groups, while the available registry entries leave important questions about methods and missing data unanswered.

17. Why This Trial Matters Statistically

This trial addresses a design question with a practical statistical feature: two methods for conducting a post-operative void trial are compared using a binary failure outcome. Randomization makes the comparison more informative than an uncontrolled observation in principle, because it is intended to reduce systematic differences between groups. The posted results also make it possible to examine an absolute contrast and its uncertainty rather than relying only on event counts.

The primary estimate illustrates why interpretation should not stop at the direction of the point estimate or at a single p-value. The risk-difference interval crosses zero and includes values on both sides, so the data do not sharply determine the direction or magnitude of a difference. This is an important distinction between failing to establish a difference and establishing that two methods are equivalent. The latter requires a planned framework and margin, neither of which is reported in the registry record.

The secondary outcomes also show why a trial needs a transparent outcome hierarchy. Multiple endpoints can address different parts of the participant experience, but unadjusted comparisons across several outcomes are more vulnerable to chance findings. Without a reported multiplicity plan, secondary results are useful context but have less confirmatory weight.

Finally, clear reporting of denominators, analysis populations, missing data, and endpoint definitions is essential for assessing precision and possible bias. The record lists enrollment of 84, while the primary endpoint counts use 42 and 40 participants, without explaining the difference. The abbreviated failure criteria and absent analysis details further limit interpretation. These reporting gaps matter statistically because they shape how readers judge the reliability and scope of an estimate, not merely how it is presented.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations are specific to the information available for this trial. The registry lists enrollment of 84, whereas the primary endpoint is reported for 42 participants in the autofill group and 40 in the backfill group. The reason for the difference is not reported in the registry record. Without an accounting of participants and outcome availability, it is not possible to determine whether the primary comparison includes all enrolled participants or how any unavailable outcomes were handled.

The description of the primary endpoint population is empty, and the registry does not report an analysis population definition. It does not specify whether all randomized participants were analyzed in their assigned groups or whether another approach was used. The full criteria for void trial failure are also not reported in the registry record; the available arm descriptions are truncated after mentioning PVR criteria.

Details that would help evaluate trial conduct and analysis are absent. The randomization sequence and allocation concealment methods are not reported in the registry record. The sample-size justification for the original trial, statistical analysis plan, specific analysis methods, multiplicity strategy, interim analysis plan, and missing-data approach are also not reported. No sponsor-reported analysis record is listed for the primary endpoint, and no analyses are listed for the secondary outcomes.

Results are not posted for all the listed secondary outcomes. Time to discharge, bladder-function quality, and perception of bladder condition results are not reported in the registry record. This prevents a complete assessment of the range of outcomes that the trial intended to address. The absence of these results should not be interpreted as evidence of no effect or as evidence of a particular reason for non-reporting.

The primary confidence interval is broad, and the group event counts are limited. That imprecision means the estimate is not a precise description of the difference that might be expected beyond the observed participants. The record also does not state a threshold for clinical importance, limiting evaluation of the practical meaning of the range of possible effects.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Urinary Retention After Total Laparoscopic Hysterectomy With Immediate Foley Catheter Removal Versus Backfill Void Trial — NCT03141372.
• Registry record last updated 2018-10-11; status last verified 2018-10.
• Results first posted 2018-10-11.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, randomized, unmasked, parallel-group trial comparing autofill and backfill void trials after total laparoscopic hysterectomy. Enrollment is listed as 84. The primary endpoint was the number of participants with void trial failure, assessed post-operatively, about 4 hours after surgery.

Primary results were reported for 42 participants in the autofill group and 40 in the backfill group, with 7 and 11 failures, respectively. The posted risk difference for backfill relative to autofill is 0.108, with a 95% confidence interval from -0.070 to 0.287 and an unadjusted p-value of 0.236. The interval includes no difference and values in either direction.

The registry lists six secondary outcomes, with results posted for three. The original sample-size justification, detailed analysis plan, analysis population, missing-data handling, and reason for the enrollment and endpoint denominator difference are not reported in the registry record. The results therefore support a description of the observed comparisons, but leave substantial uncertainty about precision and analysis details.