Trial of Prophylactic Tamsulosin for Postoperative Urinary Retention in Primary Total Hip and Knee Arthroplasty Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of Prophylactic Tamsulosin for Postoperative Urinary Retention in Primary Total Hip and Knee Arthroplasty Patients (NCT02518971), a randomized phase 3 study. The primary outcome is Number of Patients to Develop Postoperative Urinary Retention (POUR).

2. Clinical Question

The trial addressed a specific perioperative prevention question: whether assigning prophylactic tamsulosin was associated with a different incidence of postoperative urinary retention after primary hip or knee arthroplasty than assigning placebo. The endpoint definition focused on whether patients achieved two consecutive spontaneous urine voids with residual volume below 200 mL, measured by bladder scan or straight catheterization. Patients who did not achieve those two voids were classified as having developed retention.

The primary comparison included 18 participants in the tamsulosin group and 24 in the placebo group. The registry reports the analyzed group sizes as 64 and 67, respectively. The unadjusted risk difference, defined as the tamsulosin group risk minus the placebo group risk, was -0.077, with a confidence interval that includes no difference. The posted chi-squared analysis reported p = 0.345. These data describe the observed groups and the uncertainty around their comparison; they do not establish that the treatments are equivalent.

3. Trial Design

The registry describes a phase 3, randomized, double-blind, parallel-group, placebo-controlled trial sponsored by the University of Michigan. Its official title identifies the study as prospective. The intervention was tamsulosin and the comparator was placebo. The tamsulosin regimen was 0.4 mg daily for five days preoperatively through postoperative day one, seven total days. The placebo regimen was one capsule daily over the same stated period.

The registry lists enrollment as 176 and the status as terminated. The primary completion date is 2018-06-05, and the study start is recorded as 2015-08. The record does not report why the study was terminated, whether enrollment stopped earlier than planned, or how the enrolled participants were distributed across reasons for discontinuation. It also does not report the original target sample size or the study's original design assumptions.

For the primary outcome, the posted results give 64 participants in the tamsulosin group and 67 in the placebo group. The observed event counts were 18 and 24, respectively. The registry also lists two participants in a “Not Randomized” category for adverse-event reporting; that category is separate from the two randomized treatment groups and should not be treated as an outcome arm.

Six outcome measures are listed, with five secondary outcomes posted. These include length of hospital stay, discharge to a skilled nursing facility, surgical site infection, acute postoperative pain medication dosages, and postoperative complications. Analysis methods for the primary outcome and several secondary outcomes are identified in the reported results, but a full statistical analysis plan, analysis-population definitions, and detailed allocation procedures are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 176 subjects were enrolled in the study. 174 were randomized to either the active tamsulosin group or placebo group and 2 subjects were withdrawn prior to randomization. 43 additional patients were withdrawn after randomization.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients to Develop Postoperative Urinary Retention (POUR), measured over Postop day 1.

The primary endpoint was the number of patients who developed postoperative urinary retention (POUR) by postoperative day one. The registry’s operational definition classified a patient as not having POUR only after two consecutive spontaneous voids with residual volume below 200 mL. Residual volume was determined by bladder scan or straight catheterization. Patients who did not complete those two qualifying voids were considered to have developed POUR.

This endpoint turns a clinical status into a binary outcome for each participant: retention or no retention under the stated definition and timeframe. Counting participants with the event makes it possible to compare the observed incidence between the randomized groups. The registry says that the incidence was compared statistically between participants taking and not taking tamsulosin at surgery.

Such a definition matters because the endpoint depends on both a threshold and an assessment procedure. The registry record specifies the residual-volume threshold, the required sequence of voids, the assessment methods, and the postoperative time point. It does not report additional details about how measurements were timed, whether assessors used a standardized schedule, or how participants with incomplete assessments were handled. Those details could affect how consistently the classification was applied, but they are not available in the registry record.

The observed counts were 18 participants with POUR in the tamsulosin group and 24 in the placebo group. These counts are the event data used in the primary comparison; they should be read alongside the group sizes and the uncertainty interval, rather than as evidence on their own.

7. Results Posted in the Registry

• Tamsulosin: 28.1% (18/64) versus 35.8% (24/67) on control; risk difference -7.7 percentage points (95% CI -23.6 to 8.2), risk ratio 0.79 (0.47–1.30); unadjusted two-proportion z-test p = 0.345.

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.

Length of Hospital Stay

• 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:
  • Tamsulosin: mean 1.12 versus 1.21 on control; difference -0.08 (95% CI -0.27 to 0.10), standardized effect d = -0.15; z-test p = 0.372.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Discharge to a Skilled Nursing Facility

• 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:
  • Tamsulosin: 1.6% (1/64) versus 1.5% (1/67) on control; risk difference 0.1 percentage points (95% CI -4.1 to 4.3), risk ratio 1.05 (0.07–16.38); unadjusted two-proportion z-test p = 0.974.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Surgical Site 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:
  • Tamsulosin: 0.0% (0/64) versus 3.1% (2/64) on control; risk difference -3.1 percentage points (95% CI -7.4 to 1.1); unadjusted two-proportion z-test p = 0.154.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover several aspects of the postoperative course, including hospital stay, discharge destination, surgical site infection, pain medication dosages, and postoperative complications. The available numeric comparisons for some of these outcomes are imprecise, particularly where events are sparse. The registry lists five posted secondary outcomes, but numerical results are not available in this record for every item in the list. The secondary-outcome content should therefore be read as a partial set of findings rather than a complete account of every listed measure.

Across the posted numeric comparisons, the results do not present a clear, consistent pattern of separation between the randomized groups. For instance, hospital stay has an estimated mean difference with an interval including no difference, and the comparisons for discharge destination and surgical site infection also have uncertainty compatible with no difference. These patterns do not add a strong, precise signal that changes the interpretation of the primary endpoint. They also do not establish that all outcomes are equivalent.

Secondary outcomes are related to the primary question because they describe other consequences or features of the postoperative course, but they are distinct endpoints with their own definitions and timeframes. A result for one cannot be substituted for the primary measure of POUR. Nor can a set of non-significant secondary tests be treated as proof that there are no differences across all outcomes.

Unadjusted secondary results carry less weight when many outcomes are examined because, in general, the chance of finding an apparently unusual result increases as the number of comparisons grows. A multiplicity adjustment or a prespecified hierarchy can address this issue, but neither is reported in the registry record. The secondary outcomes may also be exploratory, but the record does not state their planned status. They are best treated as supportive context, with attention to the definitions, timeframes, event counts, and uncertainty for each measure.

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

• Length of Hospital Stay
• Incidence of Discharge to a Skilled Nursing Facility
• Incidence of Surgical Site Infection
• Acute Postoperative Pain Medication Dosages
• Incidence of Postoperative Complications

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

The risk difference is the event proportion in one group minus the event proportion in the other. For the primary outcome, the comparison is tamsulosin minus placebo, and the estimate is -0.077. Its negative direction reflects a lower observed event proportion in the tamsulosin group. Unlike a relative measure, a risk difference expresses the contrast on the absolute probability scale. The estimate is unadjusted: it is based on the posted group summaries, without an adjustment for other variables.

What does the confidence interval add?

General: A confidence interval describes the uncertainty around an estimate under the statistical method used. It is not a guarantee that the true value lies inside the interval, and it does not measure the probability that a particular treatment effect is true. For this primary comparison, the interval crosses zero. Zero is the value corresponding to no risk difference, so the interval indicates that no difference remains compatible with the data, along with differences in either direction.

What does the p-value answer?

The registry reports a chi-squared test for the primary comparison, with p = 0.345. General: A p-value measures how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The reported value does not meet common thresholds for statistical significance, but that fact alone cannot establish equivalence or absence of an effect.

Why use a chi-squared test?

General: A chi-squared test is commonly used to compare categorical outcomes across groups. Here the primary outcome is a count of participants who did or did not meet the registry’s POUR definition. The record identifies the sponsor’s method as chi-squared. It does not provide further details about variants of the test, continuity corrections, or any adjustment for covariates. Those details are not reported in the registry record.

What is the role of recalculation?

The recalculated primary risk difference and unadjusted p-value are derived from the posted summary statistics, rather than from participant-level data. The recalculated p-value is 0.345, matching the registry’s reported p-value. This agreement indicates that the basic unadjusted comparison can be reproduced from the posted counts. It does not verify other aspects of the trial analysis, such as eligibility decisions, missing-outcome handling, or any analyses not displayed in the record.

Why might over-dispersion matter in other settings?

General: Over-dispersion occurs when observed variability exceeds what a statistical model assumes. If ignored, standard errors and confidence intervals can be misleading. It is particularly relevant to some count-data models, where events may vary more than a basic model allows. The primary outcome is reported as participants with an event, and the registry identifies a chi-squared analysis; it does not report an over-dispersion assessment or a count model. It would therefore be inappropriate to infer that such an assessment was performed.

What cannot be reconstructed from summaries?

The available summary counts support a simple unadjusted comparison, but they do not reproduce a full analysis plan. Participant-level records would be needed to check covariate-adjusted models, detailed missing-data procedures, and how any protocol deviations were handled. The registry record does not report the planned primary analysis population, a strategy for missing primary outcomes, interim analyses, or multiplicity control. Their absence from the record should not be interpreted as proof that a procedure was or was not used; the procedures are simply not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the effect estimate. The primary risk-difference estimate is -0.077, but its confidence interval crosses zero and extends in both directions. This means that the sample does not pin down the direction or size of the underlying difference with much certainty. The point estimate is one plausible summary of the observed comparison, not a precise forecast of what would occur in another sample.

The event counts were 18 in the tamsulosin group and 24 in the placebo group, with analyzed group sizes of 64 and 67. In a binary outcome, the amount of information depends in part on the number of participants and the number of events. Here, the interval’s breadth signals that substantial uncertainty remains. The point estimate should therefore not be read as a definitive estimate of the treatment contrast.

General: A confidence interval reflects sampling uncertainty under the analysis method and assumptions. It does not account automatically for every source of uncertainty, such as bias from missing outcomes, deviations from intended allocation, or limitations in how the endpoint was measured. The registry record does not report enough detail to assess all of those possibilities.

The interval includes no difference, but that does not demonstrate equivalence. An equivalence conclusion would require a prespecified margin defining what differences are acceptably small and an analysis designed to test that question. Such a margin and an equivalence analysis are not reported in the registry record. The proper reading is that the primary estimate is uncertain and the data do not rule out either no difference or effects in either direction.

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 own original design assumptions. For these non-time-to-event outcomes, the figures are participants per arm, not total events. The stated planning 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. The original trial’s 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 the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column uses a higher target probability of detecting that effect, and therefore calls for more participants per arm. These are conditional planning quantities: they depend on the selected effect size and the listed statistical assumptions.

The rows vary the effect used for planning: 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the planning illustration requires more participants per arm as the assumed effect becomes smaller. In this case the observed effect is estimated from a relatively small set of outcome groups, and planning directly from it should be interpreted cautiously. The figures are not observed power.

The illustration is not a reconstruction of the protocol’s sample-size rationale. The registry record does not report the original target effect, anticipated event rate, power target, or other original design choices. It also does not report whether any planned assumptions changed during the trial. The figures should therefore be read as hypothetical sample-size planning under the stated assumptions, rather than as evidence about what the investigators intended or achieved.

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 = 0.358; treatment proportion p₁ = 0.281; average p̄ = 0.320.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6595 = 1.2927.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6573 = 0.5532.
4. n = (1.2927 + 0.5532)² / (-0.0770)² = 575.3, rounded up to 576 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 <- 0.358208955223881                          # control proportion
p1 <- 0.28125                          # 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(2518971)
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 = 576 (80% power), 770 (90% power)
 75% of observed effect: n per arm = 1,040 (80% power), 1,392 (90% power)
 50% of observed effect: n per arm = 2,375 (80% power), 3,179 (90% power)
power.prop.test: 575.3 
Simulated power at n = 576 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

For the primary outcome, the registry reports a chi-squared test with p = 0.345. The unadjusted recalculation from the posted summary counts also gives p = 0.345, and the recalculated risk difference is -0.077. The matching p-values show that the reported primary comparison is consistent with a simple unadjusted analysis of the counts available in the registry. This does not establish that all analytic details can be reproduced, since participant-level data and a complete analysis plan are not reported.

The registry reports other sponsor analyses for secondary outcomes, including a Student T-Test for length of hospital stay with p = .378, and Fisher Exact tests for discharge to a skilled nursing facility with p = 1.0 and surgical site infection with p = .497. Recalculated unadjusted results may differ from sponsor-reported results because the calculations and available summaries need not use identical methods. The registry does not report enough detail to resolve every method difference.

For the primary result, the recalculation agrees with the reported p-value, so there is no primary p-value discrepancy to explain. A recalculation from posted summary statistics remains a limited check: it cannot substitute for the sponsor’s full analysis or account for information not contained in the summary record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and five posted secondary outcomes. Testing multiple outcomes raises a multiplicity question: if each is assessed separately, the overall chance of at least one apparently unusual result can increase. General: Statistical plans may control this through an adjustment to significance thresholds, a hierarchy of hypotheses, or another prespecified strategy. The registry record does not report whether any such strategy was specified or used.

There is also no complete description of how missing outcome data were handled. The record does not report the number of participants with missing primary endpoint assessments, the reasons for missingness, or whether any imputation or sensitivity analysis was used. Without those details, the posted group counts alone cannot show whether all participants assigned to the treatment groups contributed to the endpoint analysis.

The analysis populations are not defined in detail. The registry does not state whether the primary analysis followed an intention-to-treat principle, used a per-protocol population, or applied another rule. It also does not report how protocol deviations, withdrawals, or crossovers were treated. The outcome group sizes are recorded as 64 and 67, while enrollment is listed as 176, but the record does not explain this relationship. No assumptions about exclusions or missing data should be inferred from the difference in these entries.

The registry reports a p-value for the primary chi-squared analysis but does not provide a full statistical analysis plan or participant-level data. It does not report interim analyses, stopping rules, or the timing and rationale for the terminated status. The absence of these details limits the ability to assess prespecification and potential analytical flexibility. These are limits of the registry record, not evidence that a particular procedure was omitted.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: floppy iris syndrome (3.1%).

The adverse-event record lists serious adverse events in 2 of 64 participants at risk in the tamsulosin group and 0 of 67 participants at risk in the placebo group. Deaths are listed as 0 in both randomized groups. The record also lists 2 participants under “Not Randomized,” with no serious adverse events, other adverse events, or deaths reported for that category.

The registry identifies “Floppy Iris Syndrome” among the top serious adverse-event terms and gives 3.1%. The record does not provide enough detail in this summary to establish how that term relates to the serious-event count or to assess the clinical circumstances of individual events. It should not be assumed that every serious event in the tamsulosin group had this term.

These counts describe what the registry reports, not the comparative safety of the treatments in general. With a small number of serious events, the estimates are uncertain, and zero recorded events in one group does not establish that the risk is absent. The record does not provide detailed event narratives, relatedness assessments, or the full follow-up context for adverse events.

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

The primary result describes an observed difference in postoperative urinary retention classifications between the two randomized groups. The event count was lower in the tamsulosin group than in the placebo group, and the unadjusted risk-difference estimate was -0.077. However, the confidence interval includes no difference and extends to values on either side of zero. The reported p-value, 0.345, likewise does not provide strong evidence against the no-difference hypothesis.

This does not mean the treatments have been shown to be identical. A non-significant result is not an equivalence finding, and the registry record does not report an equivalence margin or an equivalence design. The uncertainty is important: the study results do not precisely identify the size or direction of the underlying contrast. Conversely, the lower observed event proportion in the tamsulosin group does not, by itself, demonstrate a reliable treatment effect.

The result applies to the endpoint and timeframe as defined in the record: POUR assessed by postoperative day one using two consecutive spontaneous voids with residual volume below 200 mL. It does not directly answer questions about later urinary outcomes, duration of retention, or other definitions of retention. Results for secondary outcomes are separate and cannot be used to replace the primary comparison.

The registry record also leaves important interpretive details unreported, including the complete analysis population, missing-data handling, original design assumptions, and the reason the study was terminated. These unknowns limit what can be inferred from the posted summary. The result is best understood as an uncertain comparison in the analyzed groups, rather than a definitive conclusion about the presence or absence of an effect.

This statistical interpretation is not medical advice. It describes the posted data and their precision, without making a recommendation about treatment.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary endpoint is a binary clinical outcome with a clear operational definition and a direct two-group comparison. The definition specifies the assessment timeframe, the requirement for consecutive spontaneous voids, and the residual-volume threshold. Those elements show how a clinical concept is translated into a measurable endpoint for analysis.

The result also illustrates why an effect estimate, an uncertainty interval, and a p-value answer different questions. The point estimate records the direction and magnitude of the observed contrast. The confidence interval shows that the estimate remains uncertain, including no difference. The p-value summarizes the primary test under its null model, but cannot establish equivalence or determine clinical importance by itself.

Sample-size planning provides another useful statistical lesson. Planning illustrations based on an observed effect can grow substantially as the assumed effect becomes smaller. Such calculations depend on their assumptions and should not be confused with the original trial rationale or with observed power. The registry record does not report the original design assumptions, so the illustrative calculations cannot explain why the study was sized or terminated as it was.

Finally, the record demonstrates the value of distinguishing primary from secondary outcomes and of noting what is not reported. A collection of secondary comparisons does not automatically strengthen a primary result, particularly when multiplicity handling and analysis populations are undocumented. Careful interpretation separates the observed data from claims that the record cannot support.

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 primary analysis is based on 64 participants in the tamsulosin group and 67 in the placebo group, with 18 and 24 primary events. The resulting confidence interval includes no difference and allows effects in either direction. This limits precision and makes the point estimate an uncertain summary. The registry’s total enrollment is 176, but the record does not explain why the primary outcome group sizes are smaller or how participants without posted primary outcome data were handled.

The endpoint is specific to postoperative day one and to the registry’s voiding criteria. It does not capture other definitions of retention or later outcomes. The record does not report detailed measurement schedules, assessment masking procedures, or how incomplete assessments were classified. Although the trial is described as double-blind, the registry does not provide additional operational details about masking or its maintenance.

The status is terminated, but the reason is not reported in the registry record. The original target sample size and sample-size justification are also not reported. Consequently, the posted results cannot establish whether the study reached its intended enrollment or whether termination affected the amount of information available. The planning illustrations are not the trial’s own design calculations.

The analysis-population definitions, missing-data strategy, multiplicity plan, and interim-analysis procedures are not reported in the registry record. Several secondary outcomes are listed, but numerical results are not present for every listed measure. Adverse-event summaries have limited detail, and the small serious-event counts do not support precise comparisons. These trial-specific limitations constrain interpretation without determining what the unreported procedures were.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Trial of Prophylactic Tamsulosin for Postoperative Urinary Retention in Primary Total Hip and Knee Arthroplasty Patients — NCT02518971.
• Registry record last updated 2019-04-12; status last verified 2019-03.
• Results first posted 2019-04-12.
• 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

NCT02518971 is a terminated, randomized, double-blind, parallel-group, placebo-controlled phase 3 trial sponsored by the University of Michigan. It evaluated prophylactic tamsulosin against placebo in patients undergoing primary total hip or knee arthroplasty. The registry lists enrollment of 176, a start date of 2015-08, and primary completion on 2018-06-05.

The primary endpoint was the number of participants developing postoperative urinary retention by postoperative day one. The reported counts were 18 among 64 participants assigned tamsulosin and 24 among 67 assigned placebo. The unadjusted risk difference was -0.077, and the reported chi-squared p-value was 0.345. The confidence interval includes no difference, leaving substantial uncertainty about the size and direction of the underlying contrast.

The registry lists five secondary outcomes and reports some secondary comparisons. It also records serious adverse events in 2 tamsulosin participants and 0 placebo participants, with 0 deaths in both groups. The reason for termination, original design assumptions, analysis-population definitions, missing-data handling, and multiplicity procedures are not reported in the registry record.