Optimal Duration of Indwelling Urinary Catheter Following Pelvic Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Optimal Duration of Indwelling Urinary Catheter Following Pelvic Surgery (NCT01923129), a randomized na study. The primary outcome is Number of Participants With Acute Urinary Retention.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group trial with no masking reported. The registry records enrollment of 142 participants and 71 participants in each posted arm. The study is marked completed. Its recorded start date is 2012-11-30 and primary completion date is 2017-11-22. The sponsor was Cedars-Sinai Medical Center.

The arms differed in both the timing of catheter removal and the use of prazosin. In the 24-hour arm, participants received prazosin 1 mg by mouth 6 hours before catheter removal. In the other arm, the catheter remained until postoperative day 3, 72 hours after surgery. The study description says that patients undergoing laparoscopic or open pelvic colorectal surgery below the peritoneal reflection for benign or malignant conditions were randomized between these approaches. Detailed eligibility criteria, recruitment procedures, allocation concealment, and the exact randomization procedure are not reported in the registry record.

The primary outcome was the number of participants with acute urinary retention, assessed on postoperative day 1 or postoperative day 3 according to group assignment. The registry defines retention using inability to void 6 hours after catheter discontinuation or voiding with a post-void residual greater than 200 cc. A secondary outcome was the number of participants with a symptomatic urinary tract infection during 1 week of hospitalization before discharge. The registry lists two outcome measures and one posted comparison analysis.

The description explains that there was no general agreement about the optimal duration of postoperative urinary drainage and that earlier research had limitations. It presents the study as a comparison of early removal with medication against delayed removal. The registry does not report a detailed statistical analysis plan or the original sample-size justification.

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: 5 subjects were excluded.

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 Acute Urinary Retention, measured over Postoperative day 1 or postpoperative 3 depending on group randomization.

The primary endpoint counts participants who met the registry definition of acute urinary retention after catheter removal. A participant was classified as having retention if they could not void 6 hours after catheter discontinuation, or if they voided but had a post-void residual greater than 200 cc of urine. Assessment was tied to the assigned removal schedule: postoperative day 1 for the earlier-removal group or postoperative day 3 for the delayed-removal group.

This endpoint focuses on a clinically relevant consequence of stopping urinary drainage: whether the participant can void under the study’s stated criteria. A binary participant count makes it possible to compare the proportion experiencing the defined event in each randomized arm. It does not describe the duration or severity of retention, the amount of residual urine beyond the threshold, or any later urinary outcomes. Those details are not reported in the registry record.

Interpretation should also take account of the endpoint’s timing and definition. The assessment occurred at different postoperative times because catheter removal occurred at different times. The result therefore compares the strategies as assigned, including their different schedules, rather than comparing participants at a single common postoperative assessment time. The registry record does not report additional rules for adjudication, repeat measurements, or handling participants whose outcome could not be assessed.

7. Results Posted in the Registry

• 72 Hour Postoperative Catheter Removal: 9.9% (7/71) versus 8.5% (6/71) on control; risk difference 1.4 percentage points (95% CI -8.1 to 10.9), risk ratio 1.17 (0.41–3.30); unadjusted two-proportion z-test p = 0.771.

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 Participants With a Symptomatic 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:
  • 72 Hour Postoperative Catheter Removal: 11.3% (8/71) versus 0.0% (0/71) on control; risk difference 11.3 percentage points (95% CI 3.9 to 18.6); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for 72 Hour Postoperative Catheter Removal than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcome adds information about symptomatic urinary tract infection during the hospitalization period specified in the registry, but it addresses a different event from acute urinary retention. Its pattern is not a direct confirmation or refutation of the primary endpoint: catheter-removal strategies can have different associations with different outcomes, and the registry does not report a combined outcome that would resolve the results into a single overall measure.

Because this outcome is secondary, it should generally carry less weight than the primary endpoint when drawing conclusions about the main research question. Secondary analyses can be valuable for identifying patterns that deserve further study, but they may not have the same pre-specified priority or statistical protection as the primary analysis. The registry record lists one secondary outcome and a reported chi-squared analysis. It does not report whether other outcomes were considered during analysis or how the chance of false-positive findings across outcomes was handled.

The secondary finding is therefore best treated as a signal within this trial rather than as a stand-alone basis for a broad conclusion. Its interpretation depends on the outcome definition, completeness of follow-up, analysis population, and the stated analysis plan; details on several of these points are not reported in the registry record. The secondary result also cannot compensate for the uncertainty around the primary retention estimate. Each outcome answers a distinct question, and the evidence should remain outcome-specific.

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

• Number of Participants With a Symptomatic Urinary Tract Infection

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison concerns a binary endpoint: each participant either met the definition of acute urinary retention or did not. For a binary outcome, the event count is interpreted in relation to the number of participants in each arm. The registry reports the counts and arm sizes, then expresses the between-arm comparison using a risk difference. The risk difference is the event risk in one arm minus the event risk in the other, with the comparison oriented as 72-hour removal relative to 24-hour removal.

What does a risk difference describe?

A risk difference expresses the absolute separation between the event risks in the two groups. A value of zero corresponds to equal observed risks; values in either direction indicate which arm has the higher observed risk under the specified comparison order. This scale is often useful for clinical interpretation because it describes the absolute contrast rather than a proportional contrast. The posted primary confidence interval includes zero, so the data do not precisely determine the direction of the underlying difference.

What does a confidence interval add?

A confidence interval reflects the uncertainty in an estimated effect under the statistical method used. It is not a range that guarantees the true effect lies within its limits, nor does it give the probability that one particular value is true. A broad interval indicates that the data are consistent with a wide range of possible effects. For the primary result, the interval spans both negative and positive risk differences. This is a reason to avoid treating the non-significant test as proof of no meaningful difference.

What does the p-value test?

The unadjusted p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that null hypothesis and the test’s assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary p-value is not small, but that alone does not show that the strategies are equivalent. A non-inferiority conclusion generally depends on a pre-specified margin and an analysis designed to assess whether the data exclude effects beyond that margin. Such a primary margin and plan are not reported in the registry record.

The registry also gives relative-risk and odds-ratio measures for the primary outcome. These compare event risks or odds on relative scales, whereas the risk difference describes an absolute contrast. Relative measures can be useful for different questions, but they do not replace the need to consider the event counts and uncertainty. None of these measures can by itself establish clinical importance or eliminate uncertainty in a study with relatively few observed events.

Why can an unadjusted comparison be limited?

An unadjusted comparison uses the posted group-level outcome information without accounting for other variables. Randomization is intended to support fair group comparisons, but it does not guarantee that every prognostic feature is balanced in a particular trial. The registry does not report an adjusted primary analysis or details of any covariates used in analysis. Therefore, the posted primary comparison should be understood as an unadjusted comparison of the reported groups, not as an estimate adjusted for participant characteristics.

The secondary symptomatic urinary tract infection result includes a reported chi-squared analysis. A chi-squared test assesses whether observed counts across categories are inconsistent with a null association, subject to its assumptions. The registry’s listed analysis is classified as non-inferiority, but the record does not give a non-inferiority margin or enough detail to establish how that classification was implemented. That reported label should not be taken as a substitute for a stated margin and analysis plan.

Over-dispersion is a general concern in some statistical models for counts when variation exceeds the model’s expected variation. It is not the central issue for the posted primary endpoint, which is analyzed as a binary participant outcome rather than a rate of repeated events. The registry does not report a model-based count analysis for this endpoint. More generally, choosing an analysis method depends on the outcome definition, trial design, and assumptions; the record does not provide enough detail to assess unreported modeling choices.

General statistical interpretation also distinguishes statistical evidence from clinical importance. A p-value describes compatibility with a null model, while an effect estimate and its interval describe direction, magnitude, and precision on the selected scale. Even when a test is not statistically significant, a sufficiently wide interval may leave substantial possibilities open. Conversely, a statistically significant secondary result does not automatically establish a reliable or clinically important effect, particularly when multiple outcomes are considered and adjustment is not reported.

11. Confidence Intervals and Precision

The primary risk-difference estimate is uncertain. Its posted confidence interval extends from a negative value to a positive value, crossing zero. In practical terms, the observed data do not pin down whether the underlying event risk is higher with the 72-hour strategy or with the 24-hour strategy. The interval also permits effects that may matter, so the result should not be summarized simply as “no difference.”

The primary event counts are small relative to the arm sizes, and a small number of events can make estimates sensitive to each observed outcome. The registry reports 6 events in the 24-hour group and 7 in the 72-hour group. The unadjusted p-value is 0.771, but this test result should be considered alongside the confidence interval rather than in isolation. A non-significant result may reflect uncertainty as well as similarity between the observed groups.

Confidence intervals are useful because they show a range of effect estimates compatible with the data under the method’s assumptions. They do not account for every possible source of uncertainty, including limitations in outcome ascertainment, missing information, or analysis choices that are not documented. The registry record does not report the primary analysis population, missing-data handling, or a clinically meaningful equivalence or non-inferiority margin. Those omissions make it difficult to judge whether the interval is sufficiently precise for a formal claim about non-inferiority.

The secondary outcome has a different posted pattern, but its estimate also needs to be considered with the outcome’s secondary status and the unreported multiplicity plan. Precision is not determined by a p-value alone: it depends on the range of plausible effects and the study’s design and data. The figures should therefore be read as estimates with uncertainty, not as definitive proof for or against either catheter-removal strategy.

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 are participants per arm for 80% power and participants per arm for 90% power. They are illustrations based on the observed primary effect, not the original trial’s reported design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect.

For planning at 100% of the observed effect, the figures are 6,581 participants per arm for 80% power and 8,809 participants per arm for 90% power. For planning at 75% of the observed effect, the figures are 11,497 participants per arm for 80% power and 15,390 participants per arm for 90% power. For planning at 50% of the observed effect, the figures are 25,410 participants per arm for 80% power and 34,016 participants per arm for 90% power.

In plain language, 80% power is the probability, under the planning assumptions and if the chosen effect is real, of obtaining a statistically significant result using the specified test. The 90% column represents a higher planned chance of detecting that effect, and therefore calls for more participants per arm. Smaller effects need more participants because they are harder to distinguish from random variation. These are planning illustrations, not observed power, and the trial’s original sample-size assumptions are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.085; treatment proportion p₁ = 0.099; average p̄ = 0.092.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4078 = 0.7994.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4077 = 0.3431.
4. n = (0.7994 + 0.3431)² / (0.0141)² = 6,580.1, rounded up to 6,581 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 <- 0.0845070422535211                          # control proportion
p1 <- 0.0985915492957746                          # 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(1923129)
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 = 6,581 (80% power), 8,809 (90% power)
 75% of observed effect: n per arm = 11,497 (80% power), 15,390 (90% power)
 50% of observed effect: n per arm = 25,410 (80% power), 34,016 (90% power)
power.prop.test: 6580.1 
Simulated power at n = 6,581 per arm: 0.801 (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 record does not report whether the statistical plan adjusted for multiple comparisons. Multiplicity matters when several outcomes or analyses are tested: as the number of tests increases, the chance of observing at least one nominally significant result by chance can increase. This is a general statistical consideration, not evidence that any particular posted result is false. The registry lists a primary outcome and a secondary symptomatic urinary tract infection outcome, but it does not describe a hierarchy, adjustment procedure, or strategy for interpreting multiple tests.

Missing-data handling is also not reported in the registry record. The posted arm sizes and outcome counts are available, but the record does not explain whether every randomized participant had an outcome assessed, how unavailable outcomes were treated, or whether any participants were excluded from an analysis. Without those details, the analysis population cannot be characterized as intention-to-treat, per-protocol, or another specified population. These distinctions can matter, especially for a non-inferiority question, where exclusions and deviations may affect interpretation.

The registry record does not report the original sample-size justification, a primary non-inferiority margin, or a detailed statistical analysis plan. It also does not report whether interim analyses were planned or conducted. Those points cannot be inferred from the posted effect estimate, p-value, or planning illustrations. The secondary analysis is labeled non-inferiority in the registry, but the margin and methods supporting that label are not reported in the registry record.

These omissions limit independent assessment of whether the analyses followed pre-specified choices and how robust the conclusions are to alternative handling of outcomes. They do not establish that the analyses were inappropriate; they mean that the relevant details are unavailable in the registry record.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event figures list zero serious adverse events in each arm and zero deaths in each arm. The record also lists 6 other adverse events in the 24-hour catheter-removal arm and 0 in the 72-hour arm. These are the registry’s posted figures; the record does not provide further detail about the events, their severity, timing, relationship to the study medication, or the method used to collect them.

Zero reported serious events does not establish that serious harms are impossible or that the approaches have identical safety profiles. With a limited number of participants, uncommon events may not be observed, and the record does not describe the completeness of safety follow-up beyond the information posted. The six other events should not be interpreted as necessarily caused by the intervention: the registry does not report causal attribution or event descriptions.

These figures are descriptive safety information, not a formal comparison demonstrating safety equivalence. The record does not report a dedicated statistical analysis of adverse events or a specified safety margin. Interpretation should remain limited to the events and counts that are posted.

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

The primary data show similar observed counts of acute urinary retention in the two randomized arms, with an unadjusted p-value that is not statistically significant. The confidence interval for the risk difference crosses zero and is broad enough to leave uncertainty about both direction and magnitude. Together, these features mean the posted primary result does not provide precise evidence that one strategy has a different retention risk, but it also does not demonstrate that the strategies are equivalent.

The distinction is particularly important because the study description frames the question around whether early removal with prazosin can be used without a statistically significant difference. A non-significant test does not prove that no meaningful difference exists. A formal non-inferiority conclusion requires a pre-specified margin and analysis; the primary margin and plan are not reported in the registry record.

The trial compares two bundled approaches: removal at 24 hours with prazosin and removal at 72 hours. It cannot isolate the contribution of prazosin from the contribution of earlier catheter removal based on this comparison alone. The posted results also do not establish whether the same pattern would apply to other surgical populations, other catheter schedules, or settings beyond those described in the registry.

The secondary urinary tract infection finding is a separate result and should be interpreted with its secondary status and the absence of reported multiplicity handling in mind. It does not resolve the primary endpoint’s uncertainty. The adverse-event counts are likewise descriptive and do not establish comparative safety.

Overall, the registry record supports a cautious description of the observed data, not a treatment recommendation. The data should be understood in light of the limited event counts, imprecise primary estimate, unreported analysis details, and the specific population and intervention combination described in the study.

17. Why This Trial Matters Statistically

This trial raises a practical statistical challenge: a result with no statistically significant difference is not automatically evidence that two strategies are sufficiently similar. That distinction matters when the research question is framed around whether an earlier intervention can be used without an unacceptable increase in an adverse outcome. The answer depends not only on a p-value, but also on the effect estimate, its precision, and a clinically justified margin for non-inferiority or equivalence.

The primary outcome is binary and relatively few events were observed. In that setting, the estimated contrast can remain uncertain even when the two observed counts look close. Confidence intervals help expose that uncertainty by showing that the primary data remain compatible with effects in either direction. This is more informative than treating a non-significant test as proof of no difference.

The comparison also illustrates why trial design and analysis details matter. The intervention combines medication with a different removal time, and the endpoint is assessed at different postoperative times according to assignment. A clear pre-specified analysis plan, a defined non-inferiority margin, and transparent reporting of analysis populations and missing data would help readers evaluate the intended claim. These details are not reported in the registry record.

Finally, the secondary outcome demonstrates why multiple outcomes should be interpreted in context. A notable secondary pattern can inform further research, but it does not replace the primary comparison or remove uncertainty about it. The trial is statistically informative as an example of how effect estimates, uncertainty, endpoint priority, and reporting completeness jointly shape interpretation.

18. Limitations

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

Several limitations specific to this trial affect interpretation. The primary endpoint had 6 events in the early-removal arm and 7 in the delayed-removal arm, leaving the primary estimate imprecise. The posted confidence interval spans both sides of zero, so the data do not establish the direction of the underlying difference or exclude potentially relevant effects.

The intervention is a combination of prazosin and catheter removal at 24 hours, while the comparator involves removal at 72 hours. The randomized comparison therefore cannot determine whether any outcome difference is attributable to medication, removal timing, or their combination. In addition, the primary outcome was assessed on postoperative day 1 or day 3 depending on assignment, so the assessment time differs between arms as part of the strategies being compared.

The registry record does not report a primary non-inferiority margin, original sample-size justification, detailed statistical analysis plan, handling of missing data, or analysis population. These omissions constrain assessment of whether the study was designed and analyzed to support a formal non-inferiority conclusion. The record also does not report participant characteristics or detailed eligibility criteria beyond the broad surgical description, limiting assessment of how the enrolled population relates to other clinical settings.

The trial was unmasked, and the record does not describe outcome adjudication or whether assessment was conducted independently of treatment assignment. The secondary endpoint is subject to the additional limitation that multiplicity handling is not reported. Safety information is sparse in the registry record and lacks event descriptions or attribution. These limitations do not negate the posted results, but they narrow the claims that can be made from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Optimal Duration of Indwelling Urinary Catheter Following Pelvic Surgery — NCT01923129.
• Registry record last updated 2019-02-20; status last verified 2019-01.
• Results first posted 2019-02-20.
• 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

NCT01923129 is a completed randomized, parallel-group, unmasked study of postoperative urinary catheter timing following infraperitoneal colorectal surgery. Enrollment was 142, with 71 participants in each posted arm. The study compared catheter removal 24 hours after surgery with prazosin 1 mg given 6 hours beforehand against removal 72 hours after surgery.

The primary outcome was acute urinary retention, defined by inability to void 6 hours after removal or a post-void residual greater than 200 cc. The posted counts were 6 in the 24-hour arm and 7 in the 72-hour arm; the unadjusted p-value was 0.771. The primary result is imprecise and does not establish equivalence or non-inferiority. A secondary symptomatic urinary tract infection outcome and adverse-event figures are also reported. The registry does not report a primary non-inferiority margin, original sample-size justification, missing-data methods, or a detailed analysis plan.