Decreasing Rates of Intraurethral Catheterization Postoperatively in Spine Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Decreasing Rates of Intraurethral Catheterization Postoperatively in Spine Surgery (NCT02919436), a randomized phase 4 study. The primary outcome is Number of Patients Who Undergo Postoperative Catheterization for Urinary Retention.

2. Clinical Question

This question concerns a defined postoperative event rather than every possible urinary symptom or every measure of bladder function. The endpoint definition is based on a need for postoperative urinary catheterization for acute retention. Under the hospital protocol described in the record, failure to void 6 hours after surgery or development of bladder discomfort led to a bladder scan, and catheterization was performed if bladder volume exceeded 300 cc. These procedural details determine which events counted toward the primary outcome; they do not establish how consistently the protocol was applied to every participant.

3. Trial Design

The registry describes a randomized, parallel-group, phase 4 trial with triple masking. The brief summary says male patients over age 50 undergoing elective spine surgery were randomized 1:1 to tamsulosin or placebo. The placebo capsule was described as identical in appearance to the tamsulosin capsule. The registry lists 610 participants as the enrollment and marks the study completed. The start is listed as 2016-03 and primary completion as 2020-01.

The treatment schedule was five days before surgery and two days after surgery. Participants assigned to tamsulosin were to receive 0.4 mg/day; those assigned to placebo were to receive the matching placebo capsule. The record identifies the sponsor as Anand Rughani, MD. It does not report further details about how the random sequence was generated, how allocation was concealed, or which roles were masked; these details are not reported in the registry record.

For the primary outcome, the posted arm denominators are 245 for tamsulosin and 252 for placebo. These are not the same as the registry’s overall enrollment figure. The reason for the difference, including whether it reflects eligibility, follow-up, outcome availability, or another analysis-population definition, is not reported in the registry record. The record lists three outcome measures and one analysis for the primary comparison. It does not provide a protocol-level account of the planned analysis population or explain whether participants were analyzed according to their randomized assignment.

The trial design establishes a randomized comparison, but randomization alone does not answer every question about conduct or analysis. Details such as adherence, treatment discontinuation, crossover, and handling of missing outcomes are not reported in the registry record. Those omissions matter when interpreting how closely the posted arm results represent the full randomized groups.

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: Patients not enrolled included those who did not meet entry criteria (n=150), those who declined to participate (n=140) and those who were not enrolled for other reasons (n=151).

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 Who Undergo Postoperative Catheterization for Urinary Retention, measured over Within 2 days after surgery.

The primary endpoint is the number of participants who underwent postoperative catheterization for urinary retention within 2 days after surgery. The record defines postoperative urinary retention as the need for any postoperative urinary catheterization for acute retention. It also describes the hospital protocol: failure to void 6 hours after surgery or development of bladder discomfort required a bladder scan, and a bladder volume exceeding 300 cc led to catheterization.

This endpoint turns a clinical process into a count of participants with an event. Counting participants rather than catheterization episodes means the endpoint concerns whether a participant met the stated criterion, not how many times catheterization occurred. The record does not report a separate count of catheterization episodes or a graded measure of retention severity.

Such a defined endpoint can support a direct comparison between randomized groups when the event definition is applied consistently. It is also tied to local care procedures: the trigger for scanning and the stated threshold for catheterization are part of what determines which participants become events. The record does not report whether adherence to this protocol was assessed or whether endpoint events were adjudicated independently.

The endpoint was assessed within 2 days after surgery. It therefore addresses the specified early postoperative period, not urinary outcomes beyond that timeframe. The primary measure does not by itself characterize length of stay, preoperative bladder function, or other postoperative complications. Those are distinct outcomes and should not be substituted for the primary event count.

7. Results Posted in the Registry

• Tamsulosin: 9.4% (23/245) versus 9.9% (25/252) on control; risk difference -0.5 percentage points (95% CI -5.7 to 4.7), risk ratio 0.95 (0.55–1.62); unadjusted two-proportion z-test p = 0.841.

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 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 0.90 versus 0.70 on control; difference 0.20 (95% CI 0.01 to 0.39), standardized effect d = 0.19; z-test p = 0.036.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Tamsulosin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The record lists length of stay and postoperative urinary retention according to preoperative post-void residual as secondary outcomes. The posted detailed numerical results include length of stay, but detailed results for the post-void-residual outcome are not reported in the registry record. The secondary evidence is therefore incomplete: it cannot support a full comparison across all listed secondary outcomes.

Length of stay is a distinct outcome from the primary catheterization endpoint. Its recalculated group comparison has an unadjusted p-value of 0.036, while the primary comparison’s registry-reported test has p = .96. These findings address different questions and should not be combined into a single summary claim. A secondary difference in average length of stay neither changes the observed primary event counts nor resolves the uncertainty around the primary risk difference.

Secondary outcomes are often useful for describing additional aspects of a trial, but they generally carry less confirmatory weight when the analysis plan, outcome hierarchy, and multiplicity handling are not available. Testing several outcomes increases the chance that at least one result appears statistically notable by chance. Adjustment methods or a clearly prespecified hierarchy can address this issue, but such a plan is not reported in the registry record. The unadjusted secondary p-value should accordingly be treated as exploratory evidence rather than a standalone conclusion.

The registry lists three outcome measures and one analysis for the primary comparison. It does not clarify which secondary analyses were prespecified, whether all planned results were posted, or how missing secondary measurements were handled. Those gaps prevent a comprehensive assessment of selective reporting or the family of statistical tests. The overall secondary pattern can therefore be described only cautiously: one posted secondary comparison has a nominal unadjusted result, while another listed secondary outcome lacks detailed results. Neither provides a reason to reinterpret the primary outcome as a positive or negative finding.

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

• Length of Stay
• Number of Participants With or Without Postoperative Urinary Retention Based on Preoperative Post-void Residual

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: the endpoint records whether a participant underwent catheterization for acute postoperative urinary retention within the stated timeframe. For a binary outcome, one basic comparison is the difference between the event risks in two groups. A risk difference of zero corresponds to equal observed risks; values below zero for tamsulosin minus placebo indicate a lower observed risk in the tamsulosin arm, while values above zero indicate a higher observed risk. This sign convention is useful for interpreting the estimate but does not by itself say whether a difference is important.

What does the risk difference describe?

The recalculated risk difference is -0.005, with interval limits of -0.057 and 0.047. This is an unadjusted comparison calculated from the posted arm counts and denominators. It does not adjust for other participant characteristics or account for a model beyond the simple group comparison. The interval describes uncertainty around that estimate under the calculation’s assumptions. Since its limits extend to both sides of zero, the data do not narrowly locate the direction or size of the group difference.

Other relative effect measures can also be used for binary outcomes. A risk ratio compares the event risks as a ratio; an odds ratio compares event odds. These measures use different scales and can be less intuitive than a risk difference. Their interpretation depends on which arm is placed in the numerator and on the stated reference group. The registry’s own primary analysis is not reported as a risk ratio or odds ratio: it is a corrected chi-squared test. The recalculated risk difference is a separate descriptive statistical comparison.

What does the chi-squared test do?

A chi-squared test assesses whether observed group counts are inconsistent with a null model of no association between treatment group and outcome. The registry labels its method Chi-squared, Corrected and reports p = .96. The particular correction is not described in the registry record, so its precise implementation cannot be inferred. The p-value summarizes the compatibility of the observed counts with the test’s null model; it is not an effect-size estimate and does not measure the probability that the null hypothesis is true.

The recalculated p-value of 0.841 comes from a simple unadjusted comparison and is not a replacement for the registry analysis. Differences between p-values may reflect differences in calculation and method. In this case, the record does not signal a discrepancy, but the sponsor’s own analysis remains the trial’s reported inferential result. Reporting the two values with their methods keeps the distinction clear.

Why does an interval matter?

An estimate alone gives a point on the effect scale, but it does not communicate how precisely the data locate that point. An interval gives a range of values compatible with the data under a specified procedure and its assumptions. Wider intervals indicate less precision; narrower intervals indicate greater precision. An interval that includes zero for a risk difference does not prove there is no difference. It means the data do not exclude zero at the interval’s associated confidence level. The confidence level for the recalculated interval is not stated in the registry record, so it is not assigned a level.

Precision is influenced by the number of observed participants and events, as well as the variability inherent in the outcome. When events are uncommon, the number of events can constrain how finely a group difference is estimated even when the participant counts are substantial. The primary counts are 23 and 25, with denominators of 245 and 252, respectively. Those observed data yield an interval that permits appreciable differences in either direction.

How should the secondary mean comparison be read?

Length of stay is a continuous outcome summarized by means and standard deviations. The posted means are 0.9 days for tamsulosin and 0.7 days for placebo, with standard deviations of 1.2 and 0.9 days. The recalculated unadjusted mean difference is 0.2 days, with interval limits of 0.013 and 0.387 and p = 0.036. A mean difference describes a contrast in group averages, not a change experienced by every participant. Standard deviations describe participant-level spread around the means; they are not the uncertainty interval for the mean difference.

These calculations are unadjusted and should be interpreted as separate secondary findings. A p-value from one outcome does not account for testing other outcomes. The registry does not report a multiplicity plan or adjustment, and the detailed analysis for the other listed secondary outcome is not posted. The number of inferential questions considered therefore cannot be fully reconstructed from the record.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.005, with interval limits of -0.057 and 0.047. The interval is broad in relation to the point estimate and crosses zero. It permits a range of possible group differences, including values favoring tamsulosin and values favoring placebo. The interval therefore conveys limited precision about the direction and magnitude of the difference, despite the point estimate being close to zero.

An interval is not a guarantee that the true effect lies within its limits. In general, a confidence interval is produced by a procedure that, across repeated studies under its assumptions, has a stated coverage property. The confidence level for the recalculated primary interval is not reported in the registry record. The interval should therefore be read as an uncertainty summary for the recalculation without assigning an unreported confidence level.

The event counts and denominators matter to that uncertainty. The primary comparison is based on 23 events among 245 participants in the tamsulosin arm and 25 among 252 in the placebo arm. The registry enrollment is 610, and the reason the posted outcome denominators differ from that enrollment is not reported in the registry record. The available record does not explain whether the difference reflects missing outcome data, a defined analysis population, or another reason.

For length of stay, the recalculated mean difference is 0.2 days, with interval limits of 0.013 and 0.387. That interval is for a different outcome and effect scale; it should not be compared directly with the risk-difference interval. Its positive limits and the unadjusted p-value of 0.036 describe the recalculated group mean comparison, but do not address multiplicity or establish the importance of the difference.

Precision is distinct from statistical significance. A result can have an interval that includes zero yet still be compatible with meaningful differences in either direction, depending on context and any prespecified clinical thresholds. No threshold for a clinically important primary difference is reported in the registry record. The posted estimates therefore support an assessment of statistical uncertainty, not a definitive judgment of clinical equivalence or importance.

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 illustrative calculations based on the observed effect, not the trial’s original design. For the binary primary outcome, the figures are participants per arm. For the continuous length-of-stay outcome, they are also participants per arm. The record states that the planning calculations use a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect set to the stated fraction of the observed effect. These are planning assumptions for the illustration; the trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are conditional design calculations, not guarantees about a future study’s result. The values change with the effect size being targeted and with the assumed design conditions.

Each planning row uses a fraction of the observed effect: 100%, 75%, or 50%. A smaller effect is harder to distinguish from random variation, so the calculation requires more participants per arm as the target effect becomes smaller. The primary-outcome illustration consequently has much larger planning counts than the length-of-stay illustration. That contrast reflects the observed effect scales and their variability; it is not a direct ranking of clinical importance.

These calculations are not observed power. They do not describe the probability that the completed trial detected its actual effect, nor do they repair uncertainty in the observed estimates. They are planning illustrations based on an effect estimated from the same posted results, and they should be interpreted as sensitivity to different effect targets rather than as a retrospective verdict on the trial.

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 = 0.099; treatment proportion p₁ = 0.094; average p̄ = 0.097.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4177 = 0.8186.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4176 = 0.3515.
4. n = (0.8186 + 0.3515)² / (-0.0053)² = 48,216.2, rounded up to 48,217 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 <- 0.0992063492063492                          # control proportion
p1 <- 0.0938775510204082                          # 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(2919436)
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 = 48,217 (80% power), 64,548 (90% power)
 75% of observed effect: n per arm = 86,247 (80% power), 115,459 (90% power)
 50% of observed effect: n per arm = 195,242 (80% power), 261,373 (90% power)
power.prop.test: 48216.2 
Simulated power at n = 48,217 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. Analyses Reported by the Sponsor

The registry reports the primary comparison as a corrected chi-squared test with p = .96. The recalculated unadjusted comparison gives p = 0.841 and a risk difference of -0.005, with interval limits of -0.057 and 0.047. The calculations are not identical: the sponsor’s result is the analysis recorded by the trial, while the recalculation is a simple comparison from the posted counts and denominators.

The registry does not report an effect estimate or interval alongside its primary p-value. The recalculation adds an estimate and uncertainty interval on the risk-difference scale, but it does not supersede the sponsor’s analysis. The record indicates no discrepancy between the posted and recalculated analysis, so there is no reported conflict requiring resolution. Even so, the sponsor’s own analysis takes precedence when describing the trial’s reported inferential result.

The different p-values should not be interpreted as contradictory evidence. A test result depends on its method and assumptions, and the registry identifies a correction for its chi-squared analysis without detailing that correction. The recalculated value is explicitly unadjusted. Neither p-value measures the size or clinical importance of the effect. For that, the effect estimate and its uncertainty should be considered alongside the event counts and the endpoint definition.

The primary event counts are close, but the recalculated interval remains wide enough to include differences in either direction. The registry’s p-value does not eliminate that uncertainty. The record does not provide additional details about the sponsor’s analysis population, missing-data handling, or prespecified decision thresholds.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, timepoints, or subgroup questions are assessed. Even if each test uses the same decision threshold, conducting multiple tests can increase the chance of at least one apparently unusual result under null conditions. Common responses include prespecifying a primary outcome, defining a testing hierarchy, or adjusting inference across a family of tests. The appropriate approach depends on the protocol and aims of the trial.

The record identifies a primary outcome and lists secondary outcomes, but it does not report a multiplicity strategy. It also does not report whether the secondary outcomes were arranged in a prespecified hierarchy or whether any adjustment was applied. The unadjusted length-of-stay p-value should therefore not be read as though it were protected from the broader set of analyses. The other listed secondary outcome has no detailed result in the registry record, so the full set of reported and planned tests cannot be established.

Missing-data methods are also not described. The registry reports overall enrollment of 610 and primary-outcome denominators of 245 and 252. The record does not explain the difference, describe the status of participants without posted outcome data, or state whether imputation or another method was used. It also does not report whether the analysis followed intention-to-treat principles, a per-protocol definition, or another analysis-population rule. These details are important because exclusions or missing outcomes can affect the comparability preserved by randomization.

The record does not describe interim analyses, stopping rules, or the original statistical analysis plan. These details are not reported in the registry record and should not be inferred from the completed status or the posted results. It is also not reported whether analyses were adjusted for baseline characteristics, whether subgroup analyses were planned, or how deviations from the assigned treatment were handled.

These omissions do not prove that the trial lacked such procedures; they mean the registry record does not document them. Interpretation should remain anchored to what is posted: a primary corrected chi-squared result, a recalculated unadjusted contrast, and incomplete detail about analysis populations, multiplicity, and missing outcomes.

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: infection (0.8%), other (0.8%), ileus (0.4%), postop neurosurgical complication (0.4%), myocardial infarction (0.4%).

The registry lists serious adverse events for 5 participants at risk in the tamsulosin arm and 4 in the placebo arm. The corresponding groups at risk are 245 and 252. Other adverse events are listed for 25 participants in the tamsulosin arm and 15 in the placebo arm. The record also lists 1 death in the tamsulosin arm and 0 in the placebo arm.

The serious-event terms with reported percentages are Infection at 0.8%, Other at 0.8%, Ileus at 0.4%, Postop neurosurgical complication at 0.4%, and Myocardial infarction at 0.4%. The record does not identify arm-specific attribution for these top serious terms in the information posted here, so they should not be assigned to an arm. The listed term Other is a registry category and does not provide a clinical description.

These counts describe events recorded in the registry; they do not establish that an event was caused by a study treatment. The record does not provide additional details about event severity beyond the serious-event classification, timing, relatedness assessment, or participant-level overlap among categories. Counts should not be added across categories, since the record does not state whether participants could contribute to more than one category. The safety figures are descriptive and do not replace a full assessment of event narratives or attribution.

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

The primary result describes a comparison of observed postoperative catheterization events between two randomized arms. The counts were 23 among 245 participants assigned to tamsulosin and 25 among 252 assigned to placebo. The registry’s corrected chi-squared analysis reports p = .96. The recalculated unadjusted risk difference is -0.005, with interval limits of -0.057 and 0.047. Together, these statistics indicate that the observed counts were close, while the recalculated estimate remains imprecise enough to allow differences in either direction.

The result does not establish that the two strategies are equivalent. Equivalence or noninferiority requires a prespecified margin and a design and analysis suited to that question. Such a margin is not reported in the registry record. A non-small p-value is not proof of no effect, and the interval’s inclusion of zero does not show that the true difference is exactly zero.

The finding is specific to the stated population, treatment schedule, outcome definition, and assessment timeframe. It concerns male patients over age 50 undergoing elective spine surgery, the stated tamsulosin or placebo schedule, and catheterization for acute urinary retention within 2 days after surgery. It does not directly describe other patient groups, other procedures, other dosing schedules, or outcomes outside the stated period.

The registry’s endpoint depends on the hospital protocol for bladder scans and catheterization. The posted results do not establish whether practice was consistent across participants or sites, and the record does not report endpoint adjudication. The difference between overall enrollment and posted outcome denominators is also unexplained. These limitations constrain how confidently the observed counts can be generalized to all enrolled participants.

The secondary length-of-stay comparison is separate and unadjusted. It does not change the meaning of the primary endpoint or justify a broad conclusion across all trial outcomes. The trial record is informative about the posted comparison, but it leaves important details about the original design assumptions, analysis populations, and missing data unreported.

18. Why This Trial Matters Statistically

This trial illustrates why a p-value should not stand in for an effect estimate. The registry reports a corrected chi-squared p-value of .96, while the recalculated risk difference is -0.005 and its interval spans values on both sides of zero. The p-value alone does not show the magnitude or precision of the contrast. Reporting event counts, denominators, an effect estimate, and an interval gives a more complete statistical account.

It also illustrates the distinction between failure to find a statistically notable difference and evidence of equivalence. The primary comparison does not provide a narrow estimate around zero, and the record does not report an equivalence margin. Without such a margin, a reader cannot judge the result as demonstrating equivalence. This is a general statistical distinction, not a clinical recommendation.

The posted data also show why endpoint definitions matter. Catheterization was the counted event, and the registry specifies a pathway involving failure to void or bladder discomfort, a bladder scan, and a volume threshold. The endpoint is therefore shaped both by the clinical event and by the protocol used to identify and manage it. Knowing that definition helps readers understand what the counts represent.

Finally, the record provides a useful example of limits in registry reporting. The primary analysis method and p-value are listed, but details of sample-size justification, missing-data handling, multiplicity, and analysis populations are not reported in the registry record. The secondary results are not complete. Statistical interpretation must reflect both the numerical estimates and these reporting gaps, rather than treating a completed trial entry as a full account of its protocol and analysis.

19. Limitations

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

The posted primary outcome denominators are 245 and 252, while the registry lists enrollment of 610. The record does not explain the difference or clarify the analysis population. Without that information, it is not possible to determine from the registry record whether every randomized participant contributed to the primary analysis or how unavailable outcomes were handled.

The original sample-size justification and the trial’s own design assumptions are not reported in the registry record. The planning calculations are illustrations based on the observed effect and should not be mistaken for the trial’s planned power calculation. The record also does not report interim analyses, stopping rules, or the original statistical analysis plan.

Details about random-sequence generation, allocation concealment, the roles covered by triple masking, treatment adherence, discontinuation, and crossover are not reported in the registry record. Nor does it state whether outcome events were independently adjudicated or whether the hospital protocol was followed consistently. These omissions limit assessment of conduct and measurement, but do not establish that the procedures were inadequate.

The registry lists secondary outcomes but provides detailed numerical results for only length of stay among the secondary measures described. It does not report a multiplicity plan or explain whether the secondary analyses were prespecified. The unadjusted secondary comparison therefore has limited confirmatory weight. The record also does not give a clinical importance threshold for the primary effect, so statistical estimates cannot be mapped to a stated decision threshold.

Safety reporting is limited to aggregate counts, selected serious-event terms, and the listed death counts. Relatedness, timing, participant-level overlap, and arm attribution for the top serious-event terms are not detailed. The results should be read as registry summaries rather than a complete account of individual safety events.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Decreasing Rates of Intraurethral Catheterization Postoperatively in Spine Surgery — NCT02919436.
• Registry record last updated 2022-02-17; status last verified 2022-01.
• Results first posted 2022-02-17.
• 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

The registry record describes a completed, randomized, parallel-group, triple-masked phase 4 trial of tamsulosin versus placebo in male patients over age 50 undergoing elective spine surgery. The stated regimen was tamsulosin 0.4 mg/day or matching placebo for five days before surgery and two days after surgery. Enrollment is listed as 610.

The primary endpoint was the number of participants catheterized for acute postoperative urinary retention within 2 days after surgery. The posted counts were 23 among 245 participants in the tamsulosin arm and 25 among 252 in the placebo arm. The registry reports a corrected chi-squared analysis with p = .96. An unadjusted recalculation gives a risk difference of -0.005, with interval limits of -0.057 and 0.047.

Length of stay is the secondary outcome with detailed numerical results posted; the other listed secondary outcome lacks detailed results in the registry record. The record does not report the original sample-size justification, missing-data handling, analysis-population definition, or multiplicity plan. Interpretation should therefore distinguish the recorded trial analysis from the unadjusted recalculations and account for the uncertainty and reporting gaps.