Study to Treat Patients Who Have Signs and Symptoms of Benign Prostatic Hyperplasia (BPH) With Tadalafil Daily: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Treat Patients Who Have Signs and Symptoms of Benign Prostatic Hyperplasia (BPH) With Tadalafil Daily (NCT00827242), a randomized phase 3 study. The primary outcome is Change From Baseline to 12 Weeks, International Prostate Symptom Score (IPSS).

2. Clinical Question

3. Trial Design

The registry identifies this as a phase 3, randomized, double-blind, placebo-controlled, parallel-design, multinational study of daily tadalafil for 12 weeks in men with BPH signs and symptoms. The listed enrollment is 325. The study is recorded as completed, with a start date of 2009-01 and primary completion in 2009-11. The registry record does not report the countries or sites involved in the information available for these results.

The parallel design assigns participants to a treatment group that is compared with a separate placebo group. Randomization is intended to make the groups comparable on average, while double masking is intended to limit the influence of treatment knowledge on participants’ reports and study assessments. The record identifies the study as randomized and double-blind but does not describe the allocation sequence, masking procedures, or any steps used to assess whether masking was maintained.

For the primary endpoint, the reported analysis included 160 participants in the tadalafil group and 164 in the placebo group. This endpoint’s analysis population was defined as randomized participants who started study medication and had non-missing baseline data and at least one post-baseline visit. Those analysis counts should not be confused with the listed enrollment, which is a separate registry figure. The record says that last observation carried forward (LOCF) was used for missing outcome values in the primary analysis.

The record lists 16 outcome measures and 14 analyses, and reports 15 secondary outcomes. It does not provide the original sample-size justification, the planned allocation ratio, detailed eligibility criteria, or the full statistical analysis plan. These omissions limit what can be inferred about the original design choices from the registry record alone.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population was defined as all subjects who were randomized, started study medication, and had non-missing data at baseline and at least one post-baseline visit. The Last Observation Carried Forward (LOCF) imputation technique was employed.

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 Change From Baseline to 12 Weeks, International Prostate Symptom Score (IPSS), measured over Baseline, 12 weeks.

The primary endpoint is change from baseline to 12 weeks in the International Prostate Symptom Score (IPSS) total score. The IPSS combines responses to Question 1 through Question 7. Each question is scored from 0-5, giving a total score range of 0-35 points. Higher numerical scores indicate greater symptom severity. The endpoint therefore summarizes change in reported urinary symptoms rather than an objective measure of prostate size or a clinical event.

Change scores describe how the measured outcome differs from its baseline value by the endpoint visit. A negative change in this study’s reported scale means the score was lower at the endpoint than at baseline; because higher IPSS scores represent greater symptom severity, a reduction corresponds to improvement on the score itself. That scale interpretation does not, by itself, establish how important a particular change is to participants. The registry record does not report a threshold for a clinically meaningful change.

The primary result is expressed as a least-squares mean change. ANCOVA estimates group means while accounting for the model terms specified in the record: treatment group, region, centered baseline, a centered-baseline-by-treatment interaction, and a treatment-by-region interaction. This adjusted approach can account for baseline and region information in the comparison. The registry record does not give the model coefficients or a detailed explanation for selecting these terms.

7. Results Posted in the Registry

• Tadalafil: mean -5.60 versus -3.60 on control; difference -2.00 (95% CI -3.30 to -0.70), standardized effect d = -0.33; z-test p = 0.003.

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.

Change From Baseline to 4 Weeks, Benign Prostatic Hyperplasia (BPH) Impact Index

• 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 errors.
• Result:
  • Tadalafil: mean -1.80 versus -1.20 on control; difference -0.60 (95% CI -1.10 to -0.10), standardized effect d = -0.26; z-test p = 0.018.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Tadalafil than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline to 12 Weeks, Benign Prostatic Hyperplasia (BPH) Impact Index

• 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 errors.
• Result:
  • Tadalafil: mean -1.80 versus -1.30 on control; difference -0.50 (95% CI -1.08 to 0.08), standardized effect d = -0.19; z-test p = 0.092.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tadalafil and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to 12 Weeks, International Prostate Symptom Score (IPSS) Storage (Irritative) Subscore

• 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 errors.
• Result:
  • Tadalafil: mean -2.30 versus -1.30 on control; difference -1.00 (95% CI -1.60 to -0.40), standardized effect d = -0.37; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Tadalafil than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The reported secondary outcomes cover BPH impact, IPSS symptom components, nocturia, quality of life, and patient- and clinician-rated impressions of improvement. Across the continuous secondary outcomes with posted numerical comparisons, changes generally favor tadalafil in direction, but the strength and consistency of the evidence vary by measure and assessment time. In particular, some comparisons have uncertainty that includes no difference, while others have intervals that do not. This broad pattern is compatible with the primary result but does not establish a uniform effect across all secondary outcomes.

The secondary measures address related but distinct aspects of symptoms and perceived impact. They can help describe whether the primary score’s overall pattern is accompanied by changes in particular symptom domains or in global impressions. They should not be treated as independent confirmations: related measures may capture overlapping experiences, and several analyses increase the opportunity for chance findings.

The record lists 15 secondary outcomes, while the available outcome information includes other measures whose detailed numerical results are not discussed in this narrative. The registry does not report a multiplicity adjustment or a prespecified hierarchy for interpreting the secondary results. Unless a plan accounts for the number of comparisons, unadjusted p-values can overstate the strength of evidence across a family of outcomes. A nominally small p-value for one secondary measure therefore carries less weight than a prespecified primary finding, particularly when considered among many outcome tests.

Secondary results are most useful as supportive context and as signals for further evaluation, rather than as stand-alone proof. Their interpretation depends on whether the outcomes and timepoints were prespecified, how missing values were handled, and whether all planned comparisons are reported. Those details are not fully available in the registry record.

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

• Change From Baseline to 4 Weeks, Benign Prostatic Hyperplasia (BPH) Impact Index
• Change From Baseline to 12 Weeks, Benign Prostatic Hyperplasia (BPH) Impact Index
• Change From Baseline to 12 Weeks, International Prostate Symptom Score (IPSS) Storage (Irritative) Subscore
• Change From Baseline to 12 Weeks, International Prostate Symptom Score (IPSS) Voiding (Obstructive) Subscore
• Change From Baseline to 12 Weeks, International Prostate Symptom Score (IPSS) Nocturia Question
• Change From Baseline to 12 Weeks, International Prostate Symptom Score (IPSS) Quality of Life (QoL) Index
• Patient Global Impression of Improvement (PGI-I), Number of Participants in 7 Response Categories
• Clinical Global Impression of Improvement (CGI-I), Number of Participants in 7 Response Categories

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant’s IPSS total is a numerical score, and the analysis compares average change. A mean provides a summary of the group’s central response, but it can conceal variation among participants. The registry reports least-squares means, which are model-based group means rather than simple arithmetic averages. Their interpretation depends on the ANCOVA model and covariates recorded for the analysis.

What does the ANCOVA do?

ANCOVA compares groups while incorporating covariates that may explain outcome variation. In this trial, the recorded model includes treatment group, region, centered baseline score, a centered-baseline-by-treatment interaction, and a treatment-by-region interaction. Centering baseline means expressing baseline values relative to a reference value used by the model; the record does not state the exact reference. The interaction terms allow the treatment contrast to vary with baseline or region within the specified model. Including these terms does not mean that subgroup-specific effects have been reported.

Adjustment can make a comparison more informative when baseline values or regions are related to the outcome. It also means that the adjusted estimate is not necessarily identical to a direct subtraction of the two posted group means. A model’s estimate depends on its structure and assumptions. The registry record does not report diagnostics, model-fit assessments, or whether alternative models were considered.

What does the standard error describe?

The standard error describes the sampling precision of an estimated mean. It is not the spread of individual participant scores. A smaller standard error generally indicates a more precisely estimated mean, while a larger standard error indicates greater uncertainty from sampling variation. The reported primary standard error is 0.47 in each group. It should not be read as a standard deviation or as a range containing most participants’ results.

How should the recalculation be distinguished from the registry analysis?

The unadjusted recalculation uses the posted group summary statistics to estimate a mean difference in change and its uncertainty. It is a simple comparison and does not reproduce the recorded ANCOVA adjustment. Its confidence interval and p-value are therefore supplementary checks, not replacements for the sponsor’s analysis. The registry’s own result uses ANCOVA and reports a mean difference in final values of -1.9 with p = 0.004. The recalculation estimates -2.0 and reports p = 0.003. The estimates are similar in direction, but they answer slightly different analytic questions.

For recalculated continuous-outcome comparisons, standard deviations may need to be inferred from standard errors and group sizes when the registry reports no standard deviations. The posted primary summary marks this inference as approximate. This matters because the recalculated uncertainty depends on the inferred variability and the assumptions of the unadjusted comparison. The registry’s reported ANCOVA analysis does not depend on that particular reconstruction.

What does a p-value convey?

A p-value measures how inconsistent the observed data are with a specified null hypothesis, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, the probability that the result occurred by chance, or a measure of clinical importance. A smaller p-value can indicate stronger statistical evidence against the null under the model, but it does not resolve concerns about study conduct, outcome selection, missing data, or multiplicity.

The primary reported p-value is 0.004; the unadjusted recalculation reports 0.003. These values accompany different analyses and should be interpreted in that context. Neither value conveys the likely range of effects by itself, which is why an interval estimate is also useful.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when outcome variability is greater than a model assumes. If a model understates variability, its standard errors may be too small and its intervals too narrow, making results appear more precise than warranted. The primary endpoint is analyzed as a continuous score, and the registry record does not report an over-dispersion assessment. The issue is therefore a general modeling consideration, not a finding established for this trial.

Other model assumptions also matter, including whether the selected model adequately represents the relationship between baseline score, region, treatment, and the endpoint. The registry record identifies the ANCOVA terms but does not report residual checks, sensitivity analyses, or the handling of influential observations. The posted estimate should be read as the result of the specified analysis, with those unreported diagnostics remaining unknown.

How does LOCF affect interpretation?

The primary analysis used last observation carried forward to fill missing outcome values. This method substitutes a participant’s last observed score for later missing measurements. It can preserve participants in an analysis when the endpoint visit is missing, but it assumes that the carried-forward value is an adequate representation of the unobserved value. That assumption may not hold if symptoms change after the last recorded visit. The registry record does not report the amount or pattern of missingness, or sensitivity analyses using alternative approaches.

The primary analysis population also required participants to have started medication and to have baseline and at least one post-baseline measurement. This is not identical to including every randomized participant regardless of whether treatment began or outcome data were available. The registry’s definition and LOCF procedure are important context for interpreting the reported group estimates.

11. Confidence Intervals and Precision

The primary registry analysis reports a point estimate and p-value but does not report confidence interval limits for the mean difference. The separate unadjusted recalculation gives a 95% confidence interval for the estimated difference in change. Its reported lower endpoint is -3.303, and its upper endpoint is also below zero. This interval expresses uncertainty about the estimated group-average difference under the recalculation’s assumptions.

A confidence interval is not a prediction interval for individual participants and does not indicate that every plausible value is equally likely. It is a method-based range that reflects sampling uncertainty. Its width depends on the estimated difference, the variability in the outcome, the number of observations, and the analysis assumptions. The recalculated interval uses an approximate reconstruction of variability from the reported standard errors and group sizes, so its precision should be understood as approximate rather than as a direct reproduction of the ANCOVA model.

The fact that the recalculated interval remains below zero is consistent with the negative estimated difference under that analysis. It does not answer whether the difference is large enough to matter to participants; the registry record does not report a threshold for clinical importance. Nor does the interval account for every possible source of uncertainty, such as missing-data assumptions, model selection, or selective reporting.

The reported standard errors of the group means describe uncertainty around those means, not the dispersion of individual scores. The confidence interval for a between-group contrast is the more relevant precision summary for the comparative question. Because the sponsor’s reported ANCOVA result has no confidence limits in the registry record, its precision cannot be described with an equivalent reported interval.

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 the continuous-outcome comparisons in this study, not total events. They are illustrations based on the observed effect rather than the trial’s original design calculation. The registry record does not report the trial’s own sample-size assumptions or justification.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is expressed as a fraction of the observed effect: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. These are hypothetical planning targets, not outcomes observed in a separate study.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true effect. The 90% power column uses a higher probability of detection and therefore generally requires more participants per arm for the same target effect. These statements describe design sensitivity under assumptions; they are not guarantees about a future trial.

For a smaller target effect, more participants are needed to distinguish it from sampling variation at the same significance level and desired power. The values therefore rise as the planned effect is reduced from the full observed effect to a smaller fraction. The estimates rely on a normal approximation and the variability estimated from the trial’s posted summaries, so they should be treated as planning illustrations rather than exact prescriptions.

This is not observed power. It is a forward-looking calculation based on assumed effects and design conditions, not a measure of the probability that the trial’s observed result is true or reproducible. The trial’s original design rationale is 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -2.000; pooled standard deviation σ = 5.983.
2. n = 2 × (1.96 + 0.842)² × 5.983² / -2.000² = 140.5, rounded up to 141 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
delta <- -2                      # observed difference in means
sigma <- 5.9825820678665                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(827242)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 141 (80% power), 189 (90% power)
 75% of observed effect: n per arm = 250 (80% power), 335 (90% power)
 50% of observed effect: n per arm = 562 (80% power), 753 (90% power)
power.t.test: 141.4 
Simulated power at n = 141 per arm: 0.796 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor’s primary ANCOVA analysis as a mean difference in final values of -1.9, with p = 0.004. The unadjusted recalculation from the posted group summaries estimates a difference in change of -2.0, with p = 0.003. The two estimates point in the same direction and are close in magnitude, but they are not identical analyses: the sponsor’s result is model-adjusted, while the recalculation is an unadjusted comparison of summary changes.

The recalculated confidence interval describes the unadjusted comparison and should not be presented as the confidence interval for the sponsor’s ANCOVA result. The registry record does not report confidence limits for the sponsor’s estimate. The p-values likewise belong to their respective analyses and should not be treated as interchangeable.

The record marks no discrepancy between the reported analysis and the recalculation. That means the posted summaries and recalculated result do not flag a discrepancy under the comparison used. It does not mean that both procedures estimate precisely the same quantity or that their assumptions are identical. The sponsor’s ANCOVA remains the trial’s own reported primary analysis; the recalculation is an additional, transparent summary-based check.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity-control procedure for the secondary outcomes, nor does it describe a hierarchy, gatekeeping strategy, or other rule for interpreting multiple comparisons. When several outcomes are tested, the chance of finding at least one apparently notable result can increase even if no true effects exist. Adjustments or prespecified prioritization can address this issue, but the record does not establish that either was used. Secondary p-values should therefore be read as unadjusted evidence unless the record explicitly identifies otherwise.

The record lists 16 outcome measures and 14 analyses, and 15 secondary outcomes. It does not explain why the number of analyses differs from the number of outcome measures, whether every measure was analyzed as planned, or whether any outcomes were added or omitted during the study. The original statistical analysis plan and a detailed account of outcome prespecification are not reported in the registry record. Without those details, it is difficult to assess the scope for selective emphasis among outcomes.

For the primary endpoint, the record defines the analysis population as participants who were randomized, started study medication, and had non-missing baseline data and at least one post-baseline visit. It also states that LOCF was used for missing values. The record does not report the number or reasons for missing measurements, missingness by treatment group, or results from sensitivity analyses under alternative assumptions. LOCF can make an analysis dataset appear complete after imputation, but it does not remove uncertainty about what would have been observed at the endpoint.

The registry record does not report interim analyses, stopping boundaries, or a data-monitoring approach. Their use or absence cannot be inferred from the available entry. It also does not report the original sample-size justification. These missing methodological details limit assessment of whether the reported analyses followed a fully prespecified plan and how robust the findings are to alternative analytic choices.

16. Safety Results

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

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: acute myocardial infarction (0.6%), endocarditis (0.6%).

For serious adverse events, the registry lists 2 affected participants among 161 at risk in the tadalafil group and 0 among 164 at risk in the placebo group. The reported serious-event terms include acute myocardial infarction and endocarditis, each recorded as 0.6%. These figures describe the posted serious-event information; they do not establish that every event was caused by study treatment or provide a complete assessment of comparative safety.

The record also reports other adverse events affecting 41 of 161 participants at risk with tadalafil and 36 of 164 at risk with placebo. Those are separate from the serious adverse event counts. The record does not provide death counts in the fields reported for these results, so deaths are not reported in the registry record rather than confirmed absent.

Adverse-event counts require context about definitions, follow-up, event collection, and exposure. The registry information presented does not give detailed event narratives, timing, duration, severity beyond the serious-event classification, or causal assessments. Small event counts can be imprecise, and an observed difference in counts alone does not determine whether there is a meaningful safety difference. These data should be read as descriptive trial reports, not as a complete safety profile.

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

The primary comparison concerns average change in a symptom score over 12 weeks among the participants included in the analysis. The posted results show a larger decrease in mean IPSS score in the tadalafil group than in the placebo group, and the registry’s adjusted analysis reports a statistically notable between-group comparison. The unadjusted recalculation points in the same direction. This describes the trial’s measured outcome and does not mean that every participant experienced the same change.

The IPSS is a questionnaire-based measure of symptom severity. A change in its total score does not directly show changes in prostate anatomy, long-term disease course, or every aspect of daily functioning. The registry record does not report a threshold for judging whether a score difference is clinically important. Statistical evidence and clinical importance are related but distinct questions: the p-value addresses compatibility with a null model, while importance requires contextual evidence that is not included in this record.

The result is specific to the studied population, daily tadalafil regimen, placebo comparison, analysis population, and 12-week timeframe. It does not establish what would happen with longer treatment, in people outside the study population, or on outcomes that were not measured or reported. It also does not establish the full balance of benefits and harms. Safety counts are limited descriptions of reported events, and the registry record does not provide complete event-level context.

Interpretation also depends on the stated LOCF approach for missing primary outcome data, the ANCOVA model, and the absence of reported multiplicity details for secondary outcomes. The reported primary endpoint is more directly relevant to the study question than unadjusted secondary comparisons, but it remains an estimate with uncertainty. The finding should therefore be understood as evidence about an average score comparison in this trial, not as a universal or individual-level prediction.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of estimand and analysis matters when interpreting a clinical comparison. The registry’s primary result is an ANCOVA estimate, while a summary-based recalculation compares posted changes without the same adjustment. Their close directional agreement is informative, but the estimates and p-values cannot be substituted for one another because they arise from different methods and answer slightly different analytic questions.

It also shows why a point estimate should be read alongside precision. The recalculated confidence interval conveys uncertainty around the unadjusted average difference, while the registry does not report corresponding confidence limits for its ANCOVA estimate. A p-value alone cannot show the range of effect sizes compatible with the data or whether the estimated difference matters to participants.

Missing-data handling is another consequential part of the analysis. The primary population excludes randomized participants who did not start medication or did not meet the outcome-data requirements, and LOCF was used for missing values. These decisions shape the population represented by the result and rely on assumptions about unobserved outcomes. The registry does not provide enough missingness detail to test those assumptions from the posted information.

Finally, the set of secondary outcomes raises the general issue of multiplicity. Related symptom and impact measures can add context, but multiple unadjusted comparisons should not be counted as repeated independent confirmation. The lack of a reported adjustment or outcome hierarchy limits the strength of claims based on secondary p-values. Taken together, the record is a useful example of how design, analysis, precision, missing data, and outcome multiplicity all contribute to interpretation beyond whether a result crosses a conventional statistical threshold.

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 registry record does not report the original sample-size justification, so it is not possible to determine from this entry how the enrollment target was selected or what effect the study was designed to detect. The planning illustrations based on the observed effect are not a substitute for that rationale. The record also does not provide a detailed protocol or statistical analysis plan that would establish the full set of prespecified analyses.

The primary endpoint analysis uses LOCF, but the amount, timing, and reasons for missing data are not reported in the information available. No sensitivity analyses are described to show whether conclusions persist under different missing-data assumptions. The analysis population requires medication initiation and outcome data after baseline, so the estimate does not represent every randomized participant without qualification.

The registry reports an adjusted ANCOVA result without confidence limits. The separate recalculation is unadjusted and relies on an approximate reconstruction of variability from summary statistics. These two sources provide complementary but non-identical information, and the recalculated interval should not be mistaken for the uncertainty interval from the sponsor’s model.

The entry does not report the detailed multiplicity strategy, interim-analysis arrangements, model diagnostics, or full outcome-prespecification history. It also does not provide a clinically meaningful IPSS difference threshold, detailed adverse-event narratives, or reported death counts. The available safety information is therefore descriptive and incomplete for a comprehensive assessment of harms. These limitations constrain the conclusions that can be drawn from the registry record without implying that any unreported procedure or analysis was or was not performed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Treat Patients Who Have Signs and Symptoms of Benign Prostatic Hyperplasia (BPH) With Tadalafil Daily — NCT00827242.
• Registry record last updated 2010-11-17; status last verified 2010-10.
• Results first posted 2010-11-17.
• 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, double-blind, placebo-controlled, parallel phase 3 study of daily tadalafil over 12 weeks in men with signs and symptoms of BPH. Listed enrollment is 325. The primary endpoint is change from baseline in IPSS total score, analyzed using ANCOVA in a defined population of participants who started medication and had baseline and post-baseline data, with LOCF used for missing values.

The sponsor-reported primary analysis gives a mean difference in final values of -1.9 and p = 0.004. An unadjusted recalculation from posted summaries estimates a mean difference in change of -2.0 and p = 0.003, with a 95% confidence interval below zero. These are related but distinct analyses. Secondary measures provide additional symptom and impact context, but multiplicity procedures are not reported. Serious adverse events were recorded in the tadalafil group and none were recorded in the placebo group; death counts are not reported in the registry record.