Study to Evaluate the Efficacy and Safety of Tamsulosin in Children With Neurogenic Bladder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the Efficacy and Safety of Tamsulosin in Children With Neurogenic Bladder (NCT00796614), a randomized phase 2, phase 3 study. The primary outcome is Response to Treatment Defined as Patients Who Decrease Their Detrusor Leak Point Pressure (LPP) to <40 cm H2O Based Upon Two Evaluations on the Same Day..

2. Clinical Question

The registry lists the study as Phase IIb/III and states that its aim was to evaluate efficacy and safety across a range of tamsulosin doses in children with the described bladder condition. The primary question therefore concerns response rates at the end of treatment, considered separately for each dose level against placebo. The registry does not report a single combined comparison of all tamsulosin doses against placebo.

3. Trial Design

This was a randomized, placebo-controlled, parallel-group study with quadruple masking. The official title describes it as a Phase IIb/III, multi-centre, double-blind, dose-ranging study; the registry fields list Phase II and Phase III and record quadruple masking. Enrollment was 231. The registry records the study as completed, with a start date of 2008-01 and primary completion in 2009-02.

The intervention was tamsulosin hydrochloride at low, medium, and high dose levels, with matching placebo as the comparator. The listed dose ranges were 0.001 - 0.002 mg/kg, 0.002 - 0.004 mg/kg, and 0.004 - 0.008 mg/kg. Participants received the assigned capsules daily for 14 weeks. The official title describes treatment for three months, while the arm descriptions specify 14 weeks; these are the registry’s own descriptions.

The primary outcome was assessed at Week 14. The registry describes the full analysis set-LPP as including treated patients who received at least one dose of randomized treatment, and says it contains the same patients as the treated set. The primary endpoint description specifies that missing data were not replaced or imputed for these analyses. Details about the randomization procedure, allocation ratio, study sites, adherence, or the trial’s original sample-size justification are not reported in the registry record.

The registry lists eight secondary outcomes, including changes in leak point pressure, urine volume, and post-void residual volume, as well as ultrasound-based responses and safety-related measures. The posted quantitative secondary results cover selected outcomes; a complete numerical result for every listed secondary outcome is not reported in the registry record. The listed design features establish the broad comparison but do not, on their own, specify every modeling choice used in the sponsor’s analyses.

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: Full analysis set-LPP (FAS-LPP): Includes all patients in the treated set who received at least one dose of randomised. FAS-LPP contains same patients as TS.

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.

Population: Treated Set (TS): Includes all patients who were documented to have taken at least one dose of randomised treatment.

6. Primary Endpoint

The registry lists the primary outcome as Response to Treatment Defined as Patients Who Decrease Their Detrusor Leak Point Pressure (LPP) to <40 cm H2O Based Upon Two Evaluations on the Same Day., measured over Week 14.

The primary endpoint was the percentage of participants whose detrusor leak point pressure fell below 40 cm H2O at Week 14. A participant had to meet this threshold based on two evaluations performed on the same day. Leak point pressure was measured in cm H2O using a standard urodynamic technique, a cystometrogram, according to the registry description.

This is a binary responder endpoint: each participant is classified according to whether the pressure threshold was reached, and the group result is the percentage meeting that definition. Such an endpoint can make a clinically specified threshold easier to interpret than a group average alone, because it reports how many participants crossed the chosen boundary. As a general statistical point, however, dichotomizing a continuous measurement discards information about how far each participant’s value lies above or below the threshold. Participants close to the boundary may also be classified differently from those whose measurements are far from it, even if their underlying measurements are similar.

The endpoint is used to compare response proportions at the end of treatment across the randomized groups. It does not, by itself, describe the full distribution of pressure values, the duration of any response after treatment, or outcomes beyond Week 14. The registry identifies the threshold and timing but does not report the rationale for choosing the threshold or additional evidence linking this response definition to longer-term outcomes.

7. Results Posted in the Registry

• Tamsulosin - Low Dose Level: 45.7% (16/35) versus 35.3% (12/34) on control; risk difference 10.4 percentage points (95% CI -12.6 to 33.5), risk ratio 1.30 (0.72–2.32); unadjusted two-proportion z-test p = 0.378.
• Tamsulosin - Medium Dose Level: 27.3% (9/33) versus 35.3% (12/34) on control; risk difference -8.0 percentage points (95% CI -30.1 to 14.1), risk ratio 0.77 (0.38–1.59); unadjusted two-proportion z-test p = 0.479.
• Tamsulosin - High Dose Level: 42.4% (14/33) versus 35.3% (12/34) on control; risk difference 7.1 percentage points (95% CI -16.2 to 30.4), risk ratio 1.20 (0.66–2.20); unadjusted two-proportion z-test p = 0.549.

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 in LPP at Week 14 (End of Treatment)

• 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:
  • Tamsulosin - Low Dose Level: mean -17.60 versus -11.40 on control; difference -6.20 (95% CI -18.81 to 6.41), standardized effect d = -0.24; z-test p = 0.335.
  • Tamsulosin - Medium Dose Level: mean -4.60 versus -11.40 on control; difference 6.80 (95% CI -5.68 to 19.28), standardized effect d = 0.27; z-test p = 0.285.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin - Low Dose Level and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin - Medium Dose Level and the control. The interval gives the range of effects that remain compatible with the data.

Percentage Change From Baseline in LPP at Week 14 (End of Treatment)

• 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:
  • Tamsulosin - Low Dose Level: mean -27.40 versus -19.90 on control; difference -7.50 (95% CI -27.46 to 12.46), standardized effect d = -0.19; z-test p = 0.461.
  • Tamsulosin - Medium Dose Level: mean -1.90 versus -19.90 on control; difference 18.00 (95% CI -1.82 to 37.82), standardized effect d = 0.46; z-test p = 0.075.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin - Low Dose Level and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin - Medium Dose Level and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Urine Volume at Week 14

• 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:
  • Tamsulosin - Low Dose Level: mean -32.20 versus -2.30 on control; difference -29.90 (95% CI -70.84 to 11.04), standardized effect d = -0.44; z-test p = 0.152.
  • Tamsulosin - Medium Dose Level: mean 4.40 versus -2.30 on control; difference 6.70 (95% CI -35.41 to 48.81), standardized effect d = 0.10; z-test p = 0.755.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin - Low Dose Level and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tamsulosin - Medium Dose Level and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the description beyond the binary primary response. The posted continuous leak point pressure results show decreases from baseline in the placebo group and in the low- and high-dose groups, while the medium-dose group’s reported mean change was smaller. The percentage-change results show a similar broad ordering of the group summaries. For urine volume, the directions of the reported mean changes vary across groups. Taken together, these results do not present a uniform pattern across dose levels and outcome measures.

These secondary measures are related to the primary endpoint because they assess leak point pressure or other aspects of bladder function, but they are not interchangeable with the primary responder definition. A group mean change does not tell how many individuals crossed the specified pressure threshold. Conversely, a threshold-based response percentage does not describe the average size of pressure change. Differences in measure, analysis population, and number of available observations also matter when comparing results across outcomes.

The registry lists additional secondary measures, including ultrasound-based responses, wetness at catheterisation, safety-related measures, and post-void residual volume. Results for every listed outcome are not reported in the registry record. In addition, the sponsor’s reported analyses for the selected continuous outcomes use ANCOVA, while the posted group summaries and recalculations have their own limits and should not be treated as a complete reconstruction of those models.

Secondary findings generally carry less weight than a prespecified primary result when many outcomes are examined. As a general statistical principle, testing multiple outcomes creates more opportunities for apparently notable results to occur by chance. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of the secondary analyses. These results are therefore best viewed as supporting context and not as independent confirmation of the primary comparison.

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

• Change From Baseline in LPP at Week 14 (End of Treatment)
• Percentage Change From Baseline in LPP at Week 14 (End of Treatment)
• Response With Regard to Hydronephrosis Was Defined as Improvement or Stabilisation Based Upon the Renal Ultrasound Grading at Week 14 (End of Treatment) Compared to Baseline
• Response With Regard to Hydroureter Was Defined as Improvement or Stabilisation Based Upon the Renal Ultrasound at Week 14 (End of Treatment) Compared to Baseline
• Change From Baseline in Urine Volume at Week 14
• Change From Baseline in Number of Times Patient Was Wet at Catheterisation
• Number of Participants With Clinically Relevant Abnormalities for Physical Examination, Vital Signs/Orthostatic Testing, Electorocardiogram (ECG), Laboratory Values, Urinalysis, Treatment Emergent AE's and Cognitive Testing.
• Post Void Residual Volume at Week 14

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because the registry defines each participant as either meeting or not meeting the Week 14 pressure threshold. For a binary outcome, a group response percentage is the number of participants meeting the definition relative to the number analyzed in that group. The posted results give both the analyzed group sizes and response percentages. This summary is direct and readable, but it does not retain all the information in each participant’s measured pressure.

What the recalculated risk difference represents

The recalculated comparison uses the difference between the response proportions in the tamsulosin group and the placebo group. A value above zero indicates a larger observed response proportion in the tamsulosin group; a value below zero indicates a smaller observed response proportion. These are simple, unadjusted recalculations from the posted group summaries, not adjusted estimates from the sponsor’s regression model. For the low-, medium-, and high-dose comparisons, the recalculated values were 0.104, -0.080, and 0.071, respectively.

A risk difference is an absolute measure: it expresses the contrast between the two proportions on the same proportion scale. It is not an odds ratio or a risk ratio. Different effect measures answer related but distinct questions, and their numerical values should not be compared as if they were on the same scale. The recalculated confidence intervals describe uncertainty around these unadjusted differences under the method used for the recalculation.

How to read the confidence intervals and p-values

A confidence interval gives a range of estimates compatible with the observed data under the method’s assumptions. A narrow interval indicates greater precision than a wide interval. For the primary risk-difference comparisons, the intervals extend across zero, the value representing no difference. This means the posted data are compatible with both a decrease and an increase in the response proportion relative to placebo. The intervals are broad, so they do not pin down the direction or size of the underlying contrast precisely.

A p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be under that hypothesis and the model used. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an effect. The unadjusted recalculated p-values are 0.378, 0.479, and 0.549 for low, medium, and high dose versus placebo. These values should be read alongside the estimated differences and their intervals rather than as stand-alone evidence.

Why the sponsor’s model is a separate analysis

The sponsor reported logistic-regression analyses as odds ratios. Logistic regression models the odds of meeting the response definition, whereas the recalculated risk difference compares response proportions directly. The sponsor’s low-, medium-, and high-dose odds ratios were 1.38, 0.59, and 1.41, each with a reported 95% confidence interval. The registry does not provide enough detail to reconstruct all model specifications or identify every covariate used. The reported values should therefore be described as the sponsor’s model-based results, not treated as interchangeable with the unadjusted risk differences.

The sponsor also reported a Cochran-Armitage trend test. In general, this test evaluates whether a binary response changes in an ordered pattern across dose groups. The registry reports p = 0.944. The record does not report the trend test’s detailed assumptions or any additional dose-response modeling.

Continuous secondary outcomes

Some secondary outcomes are continuous rather than binary. For change from baseline in leak point pressure, percentage change in leak point pressure, and urine volume, the registry reports least-squares means and standard errors. A least-squares mean is a model-based mean estimate; it need not be identical to a simple arithmetic mean. A standard error describes the estimated precision of a mean, not the spread of individual participant values. The registry also reports sponsor ANCOVA p-values for selected comparisons. ANCOVA is a general method for comparing outcomes while accounting for baseline measurements or other modeled terms, but the full specification used in these analyses is not reported in the registry record.

The continuous-outcome recalculations use posted group summaries and are described as unadjusted estimates. Where the recalculation uses an approximate standard deviation derived from the reported standard errors, it is an approximation rather than a reconstruction of participant-level data. General statistical caution applies: results based on summary statistics cannot capture every feature of the original data, such as distributions, outliers, or correlations between baseline and follow-up measurements.

Analysis population and missing observations

The registry identifies the primary analysis population as the full analysis set-LPP and defines it as treated patients who received at least one dose of randomized treatment. The endpoint description says observations measured no more than 3 days after stopping treatment were considered on-treatment observations. It also says missing data in these analyses were not replaced or imputed. This describes the recorded handling of missing primary endpoint data, but does not answer how missingness was distributed across groups or how sensitive the result was to alternative assumptions. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference confidence intervals are wide relative to the point estimates. For low dose versus placebo, the recalculated estimate is 0.104 and the 95% confidence interval runs from -0.126 to 0.335. For medium dose, the estimate is -0.080 and the interval runs from -0.301 to 0.141. For high dose, the estimate is 0.071 and the interval runs from -0.162 to 0.304. Each interval includes zero, so the data do not precisely distinguish a positive contrast from a negative one.

In general, a confidence interval is a measure of statistical precision under the analysis method: a wider range leaves more uncertainty about the effect’s magnitude. These intervals allow a range of plausible group differences, including differences in either direction. They should not be read as proving that there is no difference, nor as assigning a probability to any particular value within the interval.

The sponsor’s odds-ratio intervals also span the null value of 1: 0.50 to 3.80 for low dose, 0.20 to 1.76 for medium dose, and 0.50 to 3.97 for high dose. Their breadth reinforces that the model-based effect estimates are not precise. Because odds ratios and risk differences use different scales and methods, their intervals answer different statistical questions.

Precision is constrained in part by the numbers analyzed in each primary comparison: the placebo group had 34 participants, while the dose groups had 35, 33, and 33. These group sizes are the denominators accompanying the posted primary response results, not the overall enrollment count. The registry record does not report a precision target or the original calculation used to choose enrollment.

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 describe participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: the total-events convention applies to time-to-event planning, while these calculations concern a binary response outcome and are expressed as participants per arm. The assumptions listed for this planning illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column uses the same idea with a higher target chance of detection, which generally requires a larger planned sample. Rows labeled 100% of the observed effect use the observed estimate as the planning target; rows labeled 75% or 50% use smaller fractions of that estimate. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions.

These calculations are planning illustrations based on the observed effect, not the trial’s original design calculation. The original sample-size assumptions and justification are not reported in the registry record. This is not observed power: the figures do not establish the probability that the completed trial detected its true effect, and they do not change the uncertainty in the results already observed. They are conditional planning estimates whose meaning depends on the stated assumptions and the effect chosen for planning.

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 = 0.353; treatment proportion p₁ = 0.457; average p̄ = 0.405.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6942 = 1.3607.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6903 = 0.5810.
4. n = (1.3607 + 0.5810)² / (0.1042)² = 347.2, rounded up to 348 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 <- 0.352941176470588                          # control proportion
p1 <- 0.457142857142857                          # 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(796614)
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 = 348 (80% power), 465 (90% power)
 75% of observed effect: n per arm = 612 (80% power), 818 (90% power)
 50% of observed effect: n per arm = 1,360 (80% power), 1,820 (90% power)
power.prop.test: 347.2 
Simulated power at n = 348 per arm: 0.801 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analyses use logistic regression and report odds ratios with 95% confidence intervals and p-values. The recalculated comparisons use unadjusted risk differences derived from the posted response summaries. The two approaches therefore express the group contrast on different scales and do not have to produce numerically matching estimates or p-values.

For low dose versus placebo, the sponsor reported an odds ratio of 1.38, with a 95% confidence interval from 0.50 to 3.80 and p = 0.539. For medium dose, the reported odds ratio was 0.59, with a 95% confidence interval from 0.20 to 1.76 and p = 0.343. For high dose, it was 1.41, with a 95% confidence interval from 0.50 to 3.97 and p = 0.521. The sponsor’s trend-test p-value was 0.944.

The registry does not report enough detail to reproduce the logistic-regression model fully, including all of its specifications. The recalculated risk differences should be read as supplementary, unadjusted summaries rather than replacements for the sponsor’s reported analysis. The posted results do not identify a clear separation from placebo in either presentation, while the intervals indicate considerable uncertainty. No discrepancy between the sponsor’s result and the recalculation is flagged in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, and it reports several pairwise comparisons among dose groups and placebo. When many endpoints or comparisons are examined, the chance of at least one result appearing noteworthy by chance can increase. This is the general statistical issue of multiplicity. Adjustment methods or a prespecified testing hierarchy can help control how multiple results are interpreted, but the registry record does not report whether such a plan was used for the family of primary and secondary comparisons.

The sponsor reports separate logistic-regression comparisons for the low-, medium-, and high-dose groups against placebo, along with a trend test. The record does not state whether the reported p-values were adjusted for these comparisons. The ANCOVA p-values reported for selected secondary outcomes likewise have no stated multiplicity adjustment in the registry record. This absence of information does not establish that no such procedures were used; it means the registry record does not document them.

The primary endpoint description gives some information about analysis population and missingness. The full analysis set-LPP includes treated participants who received at least one dose of randomized treatment. On-treatment observations measured no more than 3 days after stopping treatment were included as on-treatment data, and missing data were not replaced or imputed in the primary analysis. The record does not report the extent or group distribution of missing primary endpoint measurements, reasons for missingness, or sensitivity analyses using alternative missing-data assumptions.

Interim analyses, stopping rules, and the detailed statistical analysis plan are not reported in the registry record. The original sample-size justification and its assumptions are also not reported. These omissions limit how fully an external reader can assess whether every analysis followed a prespecified plan, how multiplicity was handled, and how robust the results are to missing-data assumptions. They do not invalidate the posted estimates, but they are relevant when judging how much evidential weight to place on individual p-values and secondary findings.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: shunt malfunction (2.4%), haematoma (2.4%), death (0.8%).

The registry reports serious adverse events and other adverse events using group-specific numbers at risk. For serious adverse events, the listed counts were 1 among 41 at risk in the placebo group, 1 among 120 at risk in the low-dose group, and 0 among 80 and 40 at risk in the medium- and high-dose groups, respectively. For other adverse events, the listed counts were 13 among 41 at risk for placebo, 19 among 120 at risk for low dose, 14 among 80 at risk for medium dose, and 8 among 40 at risk for high dose.

These are descriptive counts with the denominators recorded in the safety results. The registry does not explain in the posted results why these at-risk denominators differ from the group sizes in the primary efficacy analysis, so the safety and efficacy denominators should not be assumed to represent the same analysis set. The record does not report group-specific death counts. It lists Shunt malfunction and Haematoma at 2.4% each and Death at 0.8% among the top serious-event terms; these term listings do not provide a complete group-by-group account.

Safety event counts alone do not establish whether treatment caused an event or whether differences between groups are reliable. The registry record does not provide the detail needed to infer comparative safety beyond the descriptive counts and terms listed.

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

The primary results show the observed percentage meeting the Week 14 response definition in each randomized group, together with uncertainty around comparisons against placebo. The low- and high-dose groups had higher observed response percentages than placebo, while the medium-dose group had a lower observed percentage. The recalculated risk-difference intervals all include zero and extend in both directions. The sponsor’s reported odds-ratio intervals also include the null value. Thus, the posted results do not precisely establish the direction or size of a difference between any dose group and placebo.

This does not mean the groups are proven equivalent. Equivalence or non-inferiority requires an appropriate design, prespecified margins, and analyses intended to answer those questions; such details are not reported in the registry record. Nor does a result that does not clearly separate from placebo prove that no effect exists. The estimates and their uncertainty should be read together.

The endpoint has a specific scope: a threshold response based on two same-day pressure evaluations at Week 14. It does not describe every aspect of bladder function, the individual trajectory of pressure measurements, or what happened after treatment ended. The registry lists secondary outcomes that address some other measures, but results for every listed outcome are not reported, and the available secondary measures do not replace the primary endpoint.

These findings apply to the analyzed children with neurogenic bladder and elevated detrusor leak point pressure associated with a known neurological deficit, within the treatment period and outcome definition recorded. The registry does not report enough detail to support conclusions about other populations, longer follow-up, or unlisted outcomes. The results are statistical descriptions of the posted trial data, not a basis for individualized medical decisions.

18. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates how a dose-ranging randomized study can produce different-looking results across dose levels without a clear ordered pattern. The observed primary response percentage was not progressively higher across the low, medium, and high dose groups. The sponsor’s trend test also did not indicate an evident ordered trend in the reported analysis. Reading the group percentages alone could suggest a simple ranking, but the uncertainty intervals show why that ranking should be treated cautiously.

The study also shows the importance of distinguishing effect measures. The recalculated risk differences describe absolute contrasts in response proportions, while the sponsor’s logistic-regression odds ratios describe contrasts in odds. Both are legitimate statistical summaries, but they answer different questions and are not interchangeable. Stating the method and scale helps readers understand why estimates may differ without assuming that one is an arithmetic error.

Precision is central to interpreting this trial. The primary group sizes were modest, and the confidence intervals allow effects in either direction. A non-significant p-value is not evidence that the groups are identical; it should be read alongside the interval and the observed estimate. The planning illustrations further show that the number of participants needed depends strongly on the effect size selected for detection, but those illustrations are not the trial’s original design calculation.

Finally, the record highlights the limits of registry reporting for external statistical appraisal. It gives key endpoint and analysis-population details, but does not report the full analysis plan, multiplicity handling, interim analysis details, or the original sample-size justification. Those details shape how a reader assesses prespecification and robustness, particularly when numerous secondary outcomes and comparisons are available.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary response endpoint reduces leak point pressure to a threshold classification. As a general limitation of binary endpoints, this loses information about the distance of each measurement from the threshold and may treat participants with very similar values differently if they fall on opposite sides of it. The registry record does not report the rationale for the threshold or the measurement variability around the two same-day evaluations.

The primary estimates are based on relatively small analyzed groups, and the confidence intervals are wide. This limits precision about both direction and magnitude. The primary endpoint description states that missing data were not imputed, but the registry does not report how many endpoint measurements were missing in each group, why they were missing, or whether alternative missing-data analyses were conducted. These details would help assess whether the analyzed cases represent the randomized groups comparably.

The sponsor’s logistic-regression results are reported as odds ratios, but the model specification is not fully described in the registry record. The recalculated risk differences are unadjusted and based on posted summaries, rather than participant-level data. For selected continuous outcomes, the recalculations are also based on summary information, and approximate standard deviations are used where noted in the underlying results. Such summary-based analyses cannot reproduce all features of the original data or the sponsor’s models.

The registry lists multiple secondary outcomes and analyses, but does not report multiplicity procedures, a testing hierarchy, or the full analysis plan. The original sample-size rationale, interim analysis plan, and details about allocation implementation are not reported in the registry record. Safety denominators also differ from primary efficacy denominators, and the reason is not stated in the posted results. These reporting limitations narrow what can be inferred from the numerical results without implying that unreported procedures were or were not performed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate the Efficacy and Safety of Tamsulosin in Children With Neurogenic Bladder — NCT00796614.
• Registry record last updated 2015-10-29; status last verified 2015-09.
• Results first posted 2012-09-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, placebo-controlled, parallel-group Phase IIb/III study of tamsulosin hydrochloride at low, medium, and high dose levels in children with neurogenic bladder. Enrollment was 231, and treatment was given daily for 14 weeks. The primary endpoint was the percentage of participants reaching detrusor leak point pressure below 40 cm H2O at Week 14 based on two same-day evaluations.

Observed response percentages varied across groups, while the recalculated risk-difference confidence intervals and sponsor-reported odds-ratio confidence intervals were broad and included their respective null values. The posted results therefore leave substantial uncertainty about the size and direction of each dose-versus-placebo contrast. The registry does not report the full statistical analysis plan, original sample-size justification, multiplicity procedures, or detailed missing-data sensitivity analyses.