A Study of Tadalafil Use With Finasteride in Men With Enlarged Prostates and Urinary Symptoms: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Tadalafil Use With Finasteride in Men With Enlarged Prostates and Urinary Symptoms (NCT01139762), a randomized phase 3 study. The primary outcome is Change in Total International Prostate Symptom Score (IPSS) From Baseline to 12 Weeks.

2. Clinical Question

The clinical question is about the difference in average symptom-score change between randomized groups, not simply whether scores changed within either group. A negative change represents a lower score than baseline, and the comparison asks whether the amount of change differed between groups. The registry record also includes outcomes concerning symptom scores at other visits, quality of life, sexual-function domains, treatment satisfaction, and post-void residual volume. Those outcomes broaden the study's scope, but the primary question is specifically the between-group comparison at 12 weeks.

The record identifies a Phase 3b, randomized, double-blind, placebo-controlled, parallel-design study. It does not report the tadalafil or finasteride doses, the detailed comparator regimen, or the full eligibility criteria. The question should therefore be read in the context of the population and treatment descriptions actually recorded, rather than as a claim about every person with prostate enlargement or urinary symptoms.

3. Trial Design

The registry record describes a Phase 3b, randomized, double-blind, placebo-controlled, parallel-design study of tadalafil co-administered with finasteride in men with lower urinary tract symptoms and prostate enlargement associated with benign prostatic hyperplasia. The study status is completed. Enrollment was 696, and the recorded study period ran from 2010-09 to primary completion in 2012-02.

Participants were assigned to parallel groups identified as tadalafil and placebo. The registry lists finasteride as an intervention and describes the study purpose as evaluating tadalafil taken with finasteride. Detailed descriptions of the individual arm regimens are not reported in the registry record. The record identifies quadruple masking, but it does not explain which participant, clinical, or study roles were masked or how masking was implemented. The allocation sequence and the method used to conceal assignment are also not reported in the registry record.

The primary outcome was change in total IPSS from baseline to 12 weeks. The primary analysis population was defined as randomized participants who received at least one dose of study drug and had both a baseline and at least one post-baseline IPSS measurement. The primary analysis included 345 participants in the tadalafil group and 350 in the placebo group. Enrollment and analysis counts refer to different stages or definitions in the registry; the record does not give a participant flow accounting for the difference.

The broader assessment included outcomes scheduled at 4, 12, and 26 weeks, including IPSS measures and several International Index of Erectile Function domains. The record lists 14 outcome measures, with 13 secondary outcomes posted. It does not report the full protocol, a formal sample-size justification for the original trial, the randomization ratio, study-drug doses, adherence, or a detailed schedule of assessments beyond the outcome descriptions. These omissions limit how fully the operational design can be reconstructed from 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: The study consisted of 3 periods: a 4-week washout period, a 4-week, single-blind, placebo lead-in period, and a 26-week double-blind randomized active treatment period. Participants who did not complete the washout and placebo lead-in period were considered screen failures.

Washout and Placebo Lead-In Period

Reasons for not completing this period:

Double-Blind Randomized Active Treatment

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least 1 dose of the study drug, had baseline and at least 1 post-baseline IPSS measurement.

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

The primary endpoint is change in total International Prostate Symptom Score from baseline to 12 weeks. IPSS is a seven-component questionnaire for lower urinary tract symptom severity. Each question is scored from 0, meaning none or no symptoms, to 5, meaning frequent symptoms; the total score ranges from 0 to 35. Higher scores represent greater symptom severity. A change score compares a participant's follow-up score with the baseline score, so a negative value indicates a reduction in the measured score.

This endpoint is useful for the stated research question because it turns reported urinary symptoms into a defined numerical outcome that can be compared between randomized groups. The comparison is between the groups' average changes, rather than a comparison of their follow-up scores alone. The primary outcome uses least-squares means from a mixed model repeated measures analysis. Such model-based means can account for specified covariates and repeated outcome measurements; the registry record states that the model included treatment, region, visit, baseline total IPSS, and a visit-by-treatment interaction.

The endpoint reflects questionnaire-measured symptom severity, not every aspect of benign prostatic hyperplasia or urinary function. It also does not, by itself, describe treatment satisfaction, sexual function, post-void residual volume, safety, or longer-term outcomes. Those topics appear among the other recorded outcomes, but they answer different questions. The primary endpoint's 12-week timeframe is distinct from the study's six-month treatment description and from secondary outcomes measured through 26 weeks.

In general, choosing one primary endpoint helps identify the main comparison on which the study's central statistical conclusion is based. It does not make other outcomes unimportant; rather, each additional measure supplies a different piece of evidence and must be interpreted in light of its own measurement scale, timing, analysis method, and role in the study.

7. Results Posted in the Registry

• Tadalafil: mean -5.18 versus -3.76 on control; difference -1.42 (95% CI -2.31 to -0.53), standardized effect d = -0.24; z-test p = 0.002.

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.

Treatment Satisfaction Scale - Benign Prostatic Hyperplasia (TSS-BPH) at 26 Weeks

• 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:
  • Tadalafil: mean 2.00 versus 2.10 on control; difference -0.10 (95% CI -0.20 to 0.00), standardized effect d = -0.16; z-test p = 0.059.
• 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 in Post Void Residual (PVR) Volume From Baseline to 26 Weeks

• 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:
  • Tadalafil: mean -24.80 versus -23.10 on control; difference -1.70 (95% CI -12.84 to 9.44), standardized effect d = -0.02; z-test p = 0.765.
• 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.

The secondary outcome program covers several domains rather than repeating the primary question alone. It includes IPSS total scores and subscores at later or earlier visits, an IPSS quality-of-life index, multiple domains of the International Index of Erectile Function, treatment satisfaction, and post-void residual volume. These measures address different aspects of symptoms, function, satisfaction, and urinary volume, and they are recorded at different timepoints.

The posted secondary results do not establish one uniform pattern across all those domains. The record gives detailed results for selected outcomes, while it lists 13 secondary outcomes as posted. It does not provide a single overall secondary-outcome summary or a combined estimate across those measures. Consequently, a broad claim that secondary outcomes consistently support or contradict the primary finding would go beyond the record.

Secondary results can complement the primary IPSS comparison by describing related outcomes and later assessments. They cannot be treated as direct substitutes for the 12-week primary endpoint: each has its own scale, timing, analysis method, and interpretation. In particular, a rank-based test result is not interchangeable with an estimated mean difference. The record's mix of methods also means the evidence should be considered outcome by outcome rather than compressed into a single conclusion.

In general, testing many outcomes creates more opportunities for apparently notable results to arise by chance. A multiplicity strategy can specify how a study accounts for that family of comparisons, but such a strategy is not reported in the registry record. Without it, unadjusted secondary results carry less weight as confirmatory evidence than the prespecified primary comparison. They remain informative as exploratory or contextual findings, but their statistical interpretation should reflect the number of outcomes examined and the absence of a reported multiplicity plan.

The secondary findings also do not by themselves show whether any difference is important to participants. The registry does not report thresholds for clinically important changes across the secondary scales. The outcomes therefore provide additional measurements, but the posted record alone does not establish an overall benefit-harm judgment or a single summary of how the treatment groups differed across all domains.

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

• Change in Total International Prostate Symptom Score (IPSS) From Baseline to 4 and 26 Weeks
• Change in International Prostate Symptom Score (IPSS) Subscores Index From Baseline to 4, 12, and 26 Weeks
• Change in International Prostate Symptom Score (IPSS) Quality of Life Index From Baseline to 4, 12, and 26 Weeks
• Change in International Index of Erectile Function (IIEF) - Erectile Function Domain Scores From Baseline to 4, 12, and 26 Weeks
• Change in International Index of Erectile Function (IIEF) - Overall Satisfaction Domain Scores From Baseline to 4, 12, and 26 Weeks
• Change in International Index of Erectile Function (IIEF) - Intercourse Satisfaction Domain Scores From Baseline to 4, 12, and 26 Weeks
• Change in International Index of Erectile Function (IIEF) - Orgasmic Function Domain Scores From Baseline to 4, 12, and 26 Weeks
• Change in International Index of Erectile Function (IIEF) - Sexual Desire Domain Scores From Baseline to 4, 12, and 26 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison is reported as a mixed model repeated measures analysis. In general, this class of model analyzes repeated measurements while representing the association among measurements from the same participant. It can estimate adjusted group means at a visit while incorporating the variables specified in the model. The registry record names treatment, region, visit, baseline total IPSS, and a visit-by-treatment interaction as model terms. It does not report further details such as the covariance structure, estimation method, degrees-of-freedom method, or how missing measurements were handled.

What does a least-squares mean represent?

A least-squares mean is a model-based group estimate, adjusted according to the covariates and terms in the fitted model. It is not necessarily the same as a simple arithmetic average of the observed values. The primary arm estimates are reported as -5.18 for tadalafil and -3.76 for placebo, with a standard error of 0.32 for each. The reported between-group least-squares mean difference is -1.41. Because the model includes visit and a visit-by-treatment interaction, its estimated contrast is tied to the specified visit and model rather than being a generic comparison across all follow-up times.

What does the confidence interval add?

In general, a confidence interval describes the range of estimates compatible with the data and the model at a stated confidence level, under the method's assumptions. The reported 95% interval for the primary difference extends from -2.27 to -0.55. Its position below zero indicates that the reported interval does not include no group difference. The interval also communicates uncertainty about the size of the difference; a single estimate alone would not show that uncertainty. The registry record's inferential result uses its model-based interval, whereas the recalculation has its own interval from unadjusted summary statistics.

How should the p-value be understood?

In general, a p-value describes how incompatible the observed result, or a result more extreme, would be with a specified null hypothesis under the analysis assumptions. The sponsor-reported primary p-value is 0.001. It is not the probability that the null hypothesis is true, nor does it describe the size or importance of the difference. The registry also reports a recalculated unadjusted p-value of 0.002; it accompanies a simpler comparison and should not be substituted for the reported repeated-measures analysis.

Why are there different analyses for different outcomes?

The secondary outcomes do not all use the primary analysis method. For treatment satisfaction, the registry reports a Van Elteren test. In general, this is a rank-based method that can compare groups while accounting for strata. The registry record does not specify the strata used or provide an effect estimate and confidence interval for that test. For post-void residual volume, it reports a Wilcoxon rank-sum test. In general, this test compares the distributions of ranks between groups and does not, by itself, estimate a difference in means. The record does not provide the details needed to translate either test result into a model-adjusted mean contrast.

The recalculated comparisons for continuous outcomes are simple, unadjusted comparisons derived from the posted arm summary statistics. They are useful as checks on the reported values, but they do not reproduce a repeated-measures model or the rank-based sponsor analyses. For the primary outcome, the recalculation estimates the difference between arm-level changes and uses an approximate pooled standard deviation derived from the reported standard errors and sample sizes. That approximation is identified as such in the calculation. Its interval and p-value consequently answer a simpler question under different assumptions than the sponsor's adjusted MMRM analysis.

In general, over-dispersion matters when count data vary more than a chosen count model expects: uncertainty can then be understated if the extra variation is ignored. The primary endpoint is continuous, not a count outcome, so this issue does not explain the primary result. The registry does not report an over-dispersion analysis for the primary endpoint. More broadly, each method relies on assumptions, and the registry record does not provide every diagnostic or modeling detail needed to assess them independently.

The primary analysis population is explicitly defined by treatment exposure and availability of baseline and at least one post-baseline IPSS measure. That definition is not identical to all randomized participants. In general, excluding participants without the required outcome measurements can affect the population represented by the estimate, depending on why data are missing and how missingness is handled. The record does not report the number excluded for each reason or the missing-data assumptions and procedures, so the effect of missingness cannot be evaluated from the posted description alone.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is -1.41 IPSS units, with a 95% confidence interval from -2.27 to -0.55. The interval is entirely negative, indicating that the model-based estimate favors a larger reduction in score in the tadalafil group than in the placebo group. Its width shows that the result is not a single precisely known value: the data and model are compatible with a range of between-group differences. The registry reports a p-value of 0.001 alongside this estimate.

In general, a confidence interval conveys precision as well as direction. A narrower interval indicates less statistical uncertainty about the estimated quantity under the model; a wider interval indicates more. It does not guarantee that the true value lies within the interval, and it does not account for unreported sources of uncertainty such as an unreported multiplicity strategy or model misspecification. The interval is conditional on the analysis and assumptions used to calculate it.

The recalculated unadjusted comparison has an estimate of -1.42 and a 95% interval from -2.307 to -0.533. That interval is also below zero, but it is based on a different, simpler calculation. Its extra decimal places reflect the numbers as recorded for that recalculation and should not be mistaken for greater certainty. The two estimates are close, but comparison of precision should recognize that their methods differ.

The arm-level standard errors for the primary least-squares mean changes are each 0.32. A standard error describes uncertainty in an estimated mean, not the spread of individual participant outcomes. The registry does not provide confidence intervals for the arm-level means in the posted primary outcome data. The group sample sizes and standard errors therefore do not show the complete distribution of individual changes.

No clinically important difference threshold is reported in the registry record. Statistical precision can show whether the estimated difference is distinguishable from zero under a model, but it cannot decide whether a difference is important to patients or clinicians. That judgment would require a prespecified or otherwise justified interpretive threshold and context that the registry record does not provide.

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 illustrations based on the observed effect, not the original trial's design calculation. For these continuous-outcome calculations, the figures are participants per arm, not total events. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The calculation considers effects equal to 100%, 75%, and 50% of the observed effect.

The 80% power column means the estimated number of participants per arm that the planning calculation indicates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect and model assumptions were correct. The 90% power column applies the same interpretation at a higher target chance of detection. These are prospective planning quantities. They are not a measure of the probability that the study's observed result is true and do not describe the probability that the trial succeeded.

As the assumed effect becomes smaller, more participants are needed to distinguish it from random variation at the same significance and power targets. This explains why the rows for smaller fractions of the observed effect have larger planning counts. The counts are sensitive to the estimated effect used as their starting point; an observed estimate can be unstable and may not be a suitable design target in a future study.

The trial's own original sample-size justification and design assumptions are not reported in the registry record. The planning figures should therefore not be read as the enrollment target that investigators used, nor as evidence that the trial was or was not adequately powered. They are planning illustrations based on the stated assumptions, not observed power.

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 = -1.420; pooled standard deviation σ = 5.965.
2. n = 2 × (1.96 + 0.842)² × 5.965² / -1.420² = 277.0, rounded up to 278 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 <- -1.42                      # observed difference in means
sigma <- 5.96538741758212                     # 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(1139762)
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 = 278 (80% power), 371 (90% power)
 75% of observed effect: n per arm = 493 (80% power), 660 (90% power)
 50% of observed effect: n per arm = 1,109 (80% power), 1,484 (90% power)
power.t.test: 278 
Simulated power at n = 278 per arm: 0.800 (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 sponsor's reported primary analysis is a mixed model repeated measures comparison. It gives a least-squares mean difference of -1.41, a 95% confidence interval from -2.27 to -0.55, and a p-value of 0.001. These are the registry's reported inferential results for the primary endpoint.

The recalculated comparison uses the posted group summaries to estimate an unadjusted difference of -1.42, with a 95% confidence interval from -2.307 to -0.533 and an unadjusted p-value of 0.002. Its purpose is a straightforward check based on summary statistics, not a reproduction of the sponsor's model. It does not incorporate the stated MMRM terms in the same way, and it does not use the sponsor's repeated-measures data analysis.

The estimates are similar in direction and magnitude, and both intervals exclude zero. Their small numerical differences should not be interpreted as a conflict: the approaches differ in adjustment and analysis structure. The registry does not flag a discrepancy between the reported and recalculated primary results. The sponsor's model-based analysis remains the study's reported analysis, while the recalculation is supplementary and unadjusted.

For secondary outcomes, sponsor-reported tests also differ in method from the simple mean-based recalculations. A rank-based test and a mean-difference calculation need not produce the same inferential result, because they use the data differently and may target different features of the outcome distribution. The available record does not provide enough methodological detail to reconcile every such difference beyond recognizing that the methods are not identical.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and lists multiple secondary outcomes, including measures taken at several visits and multiple domains of sexual function. It does not report whether the study used a hierarchy of hypotheses, an adjustment for multiple comparisons, or another multiplicity strategy. That missing information matters because interpretation of a primary result differs from interpretation of a collection of secondary tests considered together.

In general, when many hypotheses are tested, the chance of at least one apparently unusual result can increase if each test is interpreted without adjustment. A prespecified testing order or adjustment can help control that issue, but the record does not say whether either was used. The primary p-value can be described as reported, while the degree to which it was protected against testing across other endpoints cannot be established from the registry record. Secondary p-values should be treated cautiously in the absence of a reported plan.

The primary analysis population includes randomized participants who received at least one dose and had a baseline and at least one post-baseline IPSS measurement. This is the population specified for the primary outcome; it is not described as every randomized participant. The registry does not report a full participant flow, the number with missing measurements, reasons for missingness, or analyses comparing included and excluded participants.

The MMRM description names its model terms but does not report the assumptions or procedures used to handle missing repeated measurements. In general, repeated-measures models can use available observations under specified assumptions, but the validity of inference depends on how missingness relates to observed and unobserved outcomes and on the model's adequacy. The record does not provide enough information to assess those conditions or determine whether sensitivity analyses were performed.

The original sample-size justification, interim analyses, and detailed statistical analysis plan are not reported in the registry record. It is therefore not possible to determine from this record whether the analysis population, endpoint hierarchy, missing-data procedures, and multiplicity approach followed a prespecified protocol. This is a limitation of what can be established from the registry entry, not proof that such procedures were absent from the trial itself.

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: cholangitis (0.3%), device related infection (0.3%), gastroenteritis (0.3%), hyperglycaemia (0.3%), back pain (0.3%).

The adverse-event record lists serious adverse events for 9 participants among 345 at risk in the tadalafil group and 5 among 350 at risk in the placebo group. It lists other adverse events for 105 participants in the tadalafil group and 94 in the placebo group. These counts describe participants recorded with events in the registry's groups; they do not by themselves establish that an event was caused by study treatment.

A separate screening-washout and placebo lead-in group lists 1 participant with a serious adverse event and 153 with other adverse events among 1070 at risk. That group is distinct from the two treatment groups and should not be combined with them as if it were a randomized comparison arm. The registry lists several serious-event terms at 0.3% each: cholangitis, device related infection, gastroenteritis, hyperglycaemia, back pain, and intervertebral disc protrusion.

In general, adverse-event counts need context about definitions, exposure time, event severity, and causal assessment. The record does not provide a comparative statistical analysis of these counts, detailed event narratives, or a causal attribution for the listed events. Death counts are not reported in the registry record. The figures therefore describe the posted safety observations but do not alone determine comparative risk or establish the cause of any event.

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

The primary result estimates a difference in average change in IPSS between the randomized groups at 12 weeks. The reported MMRM estimate is -1.41 units, with a 95% confidence interval from -2.27 to -0.55 and p = 0.001. The direction indicates a larger mean reduction in the tadalafil group's score than in the placebo group's score under the reported model. The interval communicates uncertainty around the estimated difference, and the p-value describes evidence against a zero-difference hypothesis under the analysis assumptions.

This result does not mean that every participant's symptoms changed by the group average, or that all participants experienced a reduction. A group mean can conceal variation in individual responses. Nor does a statistically distinguishable difference establish that the difference is clinically important. The registry record does not report a threshold for a clinically important between-group IPSS change, so the size should be interpreted on the stated score scale without assigning an unsupported importance category.

The finding applies to the recorded analysis population, endpoint, timepoint, and model. It does not by itself establish what would occur in populations with different characteristics, under different dosing, or over time beyond the recorded follow-up. The registry record does not provide enough detail about eligibility, treatment adherence, missing-data handling, or participant flow to extend the estimate beyond that defined context.

It also does not answer every question about the intervention. The primary outcome concerns symptom-score change; it does not settle the results for sexual-function domains, satisfaction, post-void residual volume, safety, or other outcomes. Those measures have distinct scales and analysis methods. The record's secondary findings should be read separately, particularly because a multiplicity plan is not reported.

Finally, this statistical interpretation is not medical advice and does not determine an individual's treatment choice. It describes what the registry reports for this comparison and how precisely the primary difference was estimated. Clinical decisions require evidence and considerations beyond this one outcome and study record.

18. Why This Trial Matters Statistically

This trial illustrates why a between-group comparison is more informative than looking only at whether each group changed from baseline. Both primary arm estimates are negative, but the research question concerns whether average change differed between randomized groups. The reported model directly addresses that contrast and supplies an interval that conveys its statistical uncertainty.

It also illustrates the distinction between a model-based analysis and a summary-statistic recalculation. The sponsor's repeated-measures analysis adjusts for terms named in the registry record and uses repeated observations. The recalculation is unadjusted and based on posted summaries. Their similar primary estimates provide a useful cross-check, but the methods remain different and answer the comparison through different analytical routes.

The secondary outcome program shows why clinical trials may measure several domains: symptom severity is not the only outcome relevant to describing a study. At the same time, multiple outcomes and visits complicate interpretation. Without a reported multiplicity strategy, secondary tests should not be treated as equally confirmatory or combined into a single broad claim. A clear distinction between primary and secondary evidence helps keep conclusions aligned with the trial's stated central question.

The record also highlights the value of transparent analysis-population definitions and missing-data reporting. The primary population is defined, but participant flow and missing-data procedures are not reported in the registry record. Those details matter for understanding who contributes to an estimate and how incomplete follow-up may affect it. Likewise, a numerical result can be statistically precise without establishing clinical importance when an interpretive threshold is absent.

For biostatisticians and clinical researchers, the study is a practical example of reading an endpoint, analysis model, uncertainty interval, secondary testing, and safety counts together without confusing their roles. Each piece answers a different question; none should be asked to support more than the record establishes.

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.

Several trial-specific details needed to fully assess the result are not reported in the registry record. These include the detailed treatment regimens and doses, the full eligibility criteria, the randomization method, the allocation ratio, and the practical steps used to implement quadruple masking. The arm descriptions contain no further regimen details. These omissions limit assessment of how the study was conducted and how closely its intervention can be reproduced from the registry description.

The primary analysis uses a defined population requiring treatment exposure and at least one post-baseline IPSS measurement. The registry does not report participant flow by reason, the amount or pattern of missing data, or sensitivity analyses for missing outcomes. It also does not give the detailed MMRM specification, including its covariance structure or estimation details. These gaps prevent a full independent assessment of the primary model and the consequences of incomplete measurements.

The record does not report the trial's original sample-size justification, interim analyses, multiplicity procedures, or full statistical analysis plan. Therefore, the planning illustrations based on the observed effect cannot establish what assumptions guided the original enrollment target. The unreported multiplicity approach also limits how confidently secondary tests can be treated as confirmatory.

The outcome record spans symptom, quality-of-life, sexual-function, satisfaction, and volume measures, but it does not provide a unified summary across these domains. The primary outcome is at 12 weeks while the broader study description covers six months; this analysis should not be read as a full account of all outcomes through the full study period. The record also does not report a clinically important difference threshold for IPSS, limiting interpretation of the practical importance of the estimated contrast.

Safety counts are descriptive in the posted record. Detailed exposure-adjusted comparisons, causal assessments, and death counts are not reported in the registry record. These limitations concern what can be concluded from this record and do not establish that additional information was not collected elsewhere.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Tadalafil Use With Finasteride in Men With Enlarged Prostates and Urinary Symptoms — NCT01139762.
• Registry record last updated 2013-02-27; status last verified 2013-01.
• Results first posted 2013-02-27.
• 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 describes a completed Phase 3b, randomized, double-blind, placebo-controlled, parallel-design study of tadalafil co-administered with finasteride in men with lower urinary tract symptoms and prostate enlargement associated with benign prostatic hyperplasia. Enrollment was 696. The primary endpoint was change in total IPSS from baseline to 12 weeks among randomized participants who received at least one dose and had baseline and at least one post-baseline IPSS measurement.

The sponsor-reported MMRM analysis estimated a tadalafil-versus-placebo difference of -1.41 IPSS units, with a 95% confidence interval from -2.27 to -0.55 and p = 0.001. The unadjusted recalculation from posted summary statistics was similar but used a different method. The registry lists secondary measures across symptoms, quality of life, sexual-function domains, satisfaction, and post-void residual volume. It also reports adverse-event counts for the treatment groups and a separate lead-in group.

The registry does not report the original sample-size justification, multiplicity plan, detailed missing-data procedures, or several operational design details. The primary result is therefore best interpreted in the context of its stated endpoint, analysis population, and reported model, without extending it beyond those limits.