Comparison of Two Urostomy Bags (2-piece).: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Two Urostomy Bags (2-piece). (NCT00761748), a randomized phase 3 study. The primary outcome is Preference of the Two Urostomy Products.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, open-label crossover study of two-piece urostomy bags. The official title describes the comparison as involving 30 urostomy-operated persons in Germany. Participants were intended to use both products, and preference was elicited at the end of the second crossover period. In a crossover design, participants receive more than one study condition in sequence, so each participant can contribute experience with both products. The registry does not report the sequence assignments, the duration of each period, or whether a washout interval was used; those details are not reported in the registry record.

The study is listed as completed. Its start is recorded as 2008-09 and primary completion as 2009-01. Masking is listed as none, meaning the registry does not describe blinding. The products are devices, and the registry names Coloplast A/S as sponsor. The summary says the sponsor developed a new, improved two-piece product for people with urostomies, but that description is not itself an outcome.

The primary outcome timeframe is 6 weeks. The endpoint description says participants completed a questionnaire at the end of the second crossover period and stated which product they preferred. The endpoint population is described as per protocol, with criteria involving eligibility, protocol adherence, exposure to both products, and evaluability for preference. The record lists 25 for each preference count. Those counts describe the endpoint record and should not be added together to infer a number of distinct participants, particularly given the crossover design. The registry lists no posted analysis records, and details of the statistical plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 39 subjects were enrolled in the study, however 9 subjects were excluded from participating in the study.

First Intervention (21 +/- 3 Days)

Reasons for not completing this period:

Second Intervention (21 +/- 3 Days)

Analysis population for the primary outcome, as defined in the registry: The Per protocol (PP) population is analysed. PP-criteria: Subjects fulfill the inclusion and exclusion criteria, do not seriously violate the protocol, are exposed to both products and are evaluable with respect to the primary endpoint (state preference). \*One drop out was evaluable, as the subject tried both products and stated a preference.

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 Preference of the Two Urostomy Products, measured over 6 weeks.

The primary endpoint counts participants who preferred SenSura Uro 2-piece or the reference Convatec 2-piece. Preference was elicited by questionnaire at the end of the second crossover period, after participants had been exposed to both products. The timeframe is recorded as 6 weeks. The registry describes the endpoint population as per protocol, requiring participants to meet eligibility criteria, avoid serious protocol violations, use both products, and be evaluable for preference.

Preference is useful when the research question concerns which of two devices participants favor after trying them. It captures the participant’s overall stated choice, which may integrate their experience of the products. It is also a subjective, categorical outcome: it records the selected product, rather than the degree of preference or the specific reasons for it. The record does not report reasons for preference, a rating scale, or separate assessments of device features.

The posted endpoint counts are 21 preferring SenSura and 4 preferring Convatec, each with a listed denominator of 25. These counts do not describe how strongly participants preferred one product, whether preferences persisted beyond the assessment, or whether one product performed better on a clinical outcome. The registry does not report a separate missing-data method for the endpoint.

7. Results Posted in the Registry

• Convatec 2 Piece: 16.0% (4/25) versus 84.0% (21/25) on control; risk difference -68.0 percentage points (95% CI -88.3 to -47.7), risk ratio 0.19 (0.08–0.48); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The study is described as randomized and crossover, with no masking. Randomization is intended to assign study sequences by chance, but the sequence allocation details are not reported in the registry record. In a crossover study, participants use more than one condition in sequence. This can make a within-participant comparison informative because each participant experiences both products, but it also creates a dependence between observations from the same person. A statistical analysis should account for that dependence. The registry does not report whether or how its analysis did so.

What does the endpoint count?

The primary outcome is a count of participants stating a preference for one of the two urostomy products. It is a binary choice between the named products, rather than a continuous score. For binary outcomes, the event is the defined response being counted. In this case, the posted counts are 21 for SenSura and 4 for Convatec, each with a denominator of 25. The record does not report a third response category, a method for handling an unanswered questionnaire, or whether the preference question allowed responses beyond the two products.

What does a risk difference express?

A risk difference compares the proportion with an event in one group with the proportion in another. Here the event is preference for the product represented by the comparison. The reported estimate is -0.68 for Convatec relative to the control arm, SenSura. The sign depends on which arm is subtracted from which; it should be interpreted using the stated comparison orientation, not in isolation. A risk difference is an absolute contrast on the proportion scale. It is not a ratio and does not indicate the reasons for a preference.

How should the p-value be understood?

The registry gives an unadjusted p-value of <0.001. In general, a p-value assesses how compatible observed data are with a specified null model, under the assumptions of the statistical procedure. A small p-value is not the probability that the null hypothesis is true, and it does not measure the magnitude or practical importance of an effect. The test, its assumptions, and the exact null hypothesis are not reported in the registry record, so the p-value can be quoted but its calculation cannot be independently assessed from the posted analysis information.

Why does the crossover structure matter?

For a simple comparison of independent groups, methods generally assume that each participant contributes an independent observation to one group. A crossover does not fit that structure automatically: a participant’s answers or measurements under the two products may be related. General crossover analysis can use the paired nature of observations and may consider period and sequence effects. Those concepts explain why the design matters, but they do not establish which method this study used. The registry reports no analysis records and does not describe a paired test, model, sequence adjustment, or period adjustment.

Carryover is another general concern in crossover designs: experience in an earlier period could influence later measurements. Whether carryover is plausible or relevant depends on the intervention and outcome, and whether it was addressed depends on the protocol and analysis. The period lengths, any washout arrangements, and any carryover assessment are not reported in the registry record. It would therefore be inappropriate to assert that carryover occurred or that it was excluded.

What does per protocol mean in this record?

The registry describes the primary analysis population as per protocol. Its stated criteria require participants to meet inclusion and exclusion criteria, not seriously violate the protocol, be exposed to both products, and be evaluable for the primary endpoint. This defines the population by adherence and endpoint availability. Such a population can differ from everyone randomized, and comparisons based on it may be affected if the reasons for non-inclusion are related to outcomes or product experience. The record does not give a complete participant flow or a full explanation of the incomplete dropout statement.

The reported endpoint counts are not an invitation to reconstruct an unreported analysis. The registry does not provide participant-level paired preferences, the randomized sequence counts, missing endpoint counts by sequence, or methods for handling missing observations. Without those details, a reader cannot independently reproduce a crossover-specific estimate or determine whether the posted comparison accounts for within-person dependence.

General statistical guidance is that effect estimates, uncertainty intervals, and analysis methods should be considered together. The estimate conveys direction and magnitude on its scale; the confidence interval conveys a range of values compatible with the data and method; and the p-value addresses a null comparison under assumptions. None can compensate for absent information about the analysis population, missing data, or the handling of the design. In this record, the estimate and p-value are posted, while the statistical plan and detailed analysis are not reported in the registry record.

10. Confidence Intervals and Precision

The reported risk difference is -0.68. Its confidence interval has two negative endpoints, so the interval excludes zero. In general, a confidence interval describes values compatible with the observed data under the analysis method and its assumptions; it is not a range containing a fixed proportion of individual participants’ preferences. A narrower interval indicates greater precision than a wider interval, but precision alone does not establish that an endpoint is clinically important or free of bias.

The interval should be interpreted with the comparison orientation in mind: the posted contrast is Convatec against the SenSura control arm. Its negative direction agrees with the posted preference counts, which record 4 for Convatec and 21 for SenSura. The registry also gives an unadjusted p-value of <0.001. The confidence interval and p-value are related summaries of uncertainty, but they answer different questions: the interval conveys a range of effect estimates, while the p-value assesses compatibility with a specified null model.

The interval’s calculation method is not reported in the registry record. In particular, the record does not say whether uncertainty estimation accounted for within-participant correlation from the crossover design. The stated per-protocol population and incomplete reporting of endpoint availability also affect how broadly the interval can be interpreted. It quantifies precision under the analysis that produced it; it does not account for unreported design or analysis choices.

Because this is a subjective preference endpoint, the interval pertains to the recorded choice comparison, not to a clinical outcome. It should not be read as evidence about device safety, effectiveness for other outcomes, or preferences outside the recorded study population.

11. 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.

Read each planning row as a hypothetical target effect expressed as a fraction of the observed effect. The row for 100% of the observed effect lists 8 participants per arm for 80% power and 10 participants per arm for 90% power. Planning for 75% of the observed effect lists 14 participants per arm for 80% power and 18 participants per arm for 90% power. Planning for 50% of the observed effect lists 29 participants per arm for 80% power and 39 participants per arm for 90% power. These figures are participants per arm, not total events.

The 80% power column gives the planned number per arm for a design with an 80% chance of detecting the stated effect under the listed assumptions, if that effect and the model assumptions are correct. The 90% column expresses the corresponding planning target for 90% power. The assumptions are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The effect to detect is the specified fraction of the observed effect. Smaller effects require more participants in these planning illustrations.

These are planning illustrations based on the observed effect, not the trial’s original design assumptions; those original assumptions are not reported in the registry record. They are not observed power.

12. 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 = 0.840; treatment proportion p₁ = 0.160; average p̄ = 0.500.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3859.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5185 = 0.4363.
4. n = (1.3859 + 0.4363)² / (-0.6800)² = 7.2, rounded up to 8 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 <- 0.84                          # control proportion
p1 <- 0.16                          # 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(761748)
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 = 8 (80% power), 10 (90% power)
 75% of observed effect: n per arm = 14 (80% power), 18 (90% power)
 50% of observed effect: n per arm = 29 (80% power), 39 (90% power)
power.prop.test: 7.2 
Simulated power at n = 8 per arm: 0.901 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and no posted secondary outcomes. It lists zero analysis records. This means the registry record does not provide a fuller set of analysis results with which to assess how many outcomes, contrasts, or tests were examined. The statistical plan, including any prespecified multiplicity strategy, is not reported in the registry record.

Multiplicity is a general issue that arises when several outcomes or comparisons are tested. The more tests considered, the greater the chance that at least one result appears statistically notable by chance if no adjustment or interpretive plan is used. That general concern does not show that multiple tests were conducted in this study; the record does not report enough analysis detail to establish that. The unadjusted p-value is the value posted for the reported comparison, and no adjustment should be inferred.

The registry describes the primary analysis population as per protocol, with eligibility, protocol adherence, exposure to both products, and evaluability as criteria. It mentions one dropout who was evaluable, but the text ends before completing the explanation. A complete account of participant flow, including who was randomized, who contributed endpoint data, and reasons for any missing outcomes, is not reported in the registry record. The endpoint counts each have a listed denominator of 25; the record does not explain the relationship between those counts and the enrollment figure in a complete participant-flow account.

Missing-data methods are also not reported in the registry record. There is no description of imputation, a complete-case rule beyond the per-protocol criteria, sensitivity analyses, or assumptions about missing preference responses. Since the primary outcome depends on an end-of-period questionnaire, knowing how unavailable responses were handled would help assess potential selection effects. It is not possible to infer that missing data were absent merely from the posted counts.

For a crossover comparison, the analysis population and missing-data approach may also affect whether paired information can be used. The registry does not report sequence-specific participation, the number of participants with evaluable responses after both periods, or an analysis model. These omissions limit independent assessment of the estimate and p-value; they do not by themselves demonstrate that the analysis was incorrect.

14. 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: ileus (3.3%).

The adverse-event record lists 30 participants at risk for serious adverse events in each product group. It records 1 serious adverse event for SenSura and 0 for Convatec. For other adverse events, it lists 30 at risk in each group, with 5 affected for SenSura and 0 for Convatec. The registry also names Ileus at 3.3% among the top serious terms. Death counts are not reported in the registry record.

These safety figures are distinct from the primary preference endpoint, whose listed denominators are 25 per product. The adverse-event denominators should not be substituted for the endpoint denominators or treated as a participant-flow account. The registry does not explain the event definitions, ascertainment procedures, severity criteria beyond the serious category, or exposure timing in detail.

Counts of events or affected participants do not by themselves establish a causal relationship to a product. With sparse counts, estimates of comparative safety would be imprecise, and the registry does not post a statistical safety comparison. The reported figures describe what the registry records; they do not establish that an event was caused by either device or that no unlisted event occurred.

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

The result means that, in the registry’s per-protocol endpoint record, more participants selected SenSura than Convatec: 21 preferred SenSura and 4 preferred Convatec, each with a listed denominator of 25. The posted risk difference is -0.68 for Convatec compared with the SenSura control arm, and the registry gives an unadjusted p-value of <0.001. The confidence interval for the risk difference lies below zero. Taken together, these figures describe a difference in recorded stated preference under the study’s assessment.

The result does not show why participants chose one product. The record does not report preference reasons, ratings of particular features, or a measure of how strongly each participant favored a product. Because the study was open-label and the endpoint was a questionnaire response, the outcome is a reported choice rather than a blinded or objective performance measure.

The result does not establish that one product is better for health, safer, more effective, or preferable for all people with urostomies. The registry reports one preference endpoint, with no posted secondary outcomes. The safety counts are separate and do not convert the preference finding into a safety comparison. Nor does the record establish how preferences might vary in other settings, populations, or periods of use.

Interpretation is also limited by the crossover structure and the absence of posted analysis records. The registry does not describe the test, model, sequence handling, period effects, missing-data methods, or full participant flow. The estimate and p-value can be reported as the registry’s results, but they cannot be independently reproduced from the posted summary alone. The conclusion should remain confined to the stated preference counts and the uncertainty attached to their reported comparison.

16. Why This Trial Matters Statistically

This trial illustrates how a clinical device comparison can define its primary question around participant preference rather than a clinical event. That choice can be appropriate when the aim is to learn which of two products people favor after using both, but the resulting endpoint answers a narrower question than one about health outcomes or device performance. Clear separation of preference, safety, and clinical effectiveness is essential when reading the results.

The crossover design makes the comparison potentially informative because participants were intended to experience both products. It also makes the analysis structure important: observations within a participant are related, and order or period could matter. The registry’s lack of posted analysis records means readers cannot determine whether those design features were accounted for statistically. This demonstrates why reporting the analysis method matters alongside an effect estimate and p-value.

The record also shows why population definitions need to be read carefully. The primary endpoint is described as per protocol, while adverse-event denominators are reported separately. Enrollment, endpoint counts, and safety denominators serve different purposes and should not be combined to create an unreported participant total. The incomplete dropout wording and absence of a complete flow description make that distinction especially relevant.

Finally, the sample-size illustrations are based on the observed effect and explicit planning assumptions, not on the original design justification. They can help readers understand how target effect size relates to planning needs, but they do not establish what the investigators planned before the study or how the trial was designed. Keeping observed results, planning illustrations, and unreported design choices distinct supports a more careful statistical reading.

17. 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 limitations are specific to the registry record. The study is open-label, and the primary endpoint is participants’ stated preference on a questionnaire. The record does not describe masking of participants or other ways of reducing influence on responses. The result therefore concerns reported preference in that context, not a blinded assessment.

The crossover description does not include the order in which products were used, period durations, any washout, or sequence-specific results. The statistical method is not reported, so it is unclear whether the posted comparison accounted for paired responses, period effects, sequence effects, or possible carryover. These are unanswered reporting questions, not evidence that a particular bias occurred.

The primary population is per protocol, and its criteria exclude participants who did not meet eligibility requirements, seriously violated protocol, lacked exposure to both products, or could not be evaluated. The record mentions one evaluable dropout but ends before completing the explanation. A full participant flow and missing-data approach are not reported in the registry record. This restricts assessment of how the endpoint counts relate to enrollment.

The registry lists one primary outcome and no posted secondary outcomes, with zero analysis records. A statistical plan, multiplicity strategy, and details of the test behind the unadjusted p-value are not reported. The adverse-event section provides counts but does not describe event definitions or detailed ascertainment. Death counts are not reported in the registry record.

Finally, the posted comparison is specific to preference after exposure to these two products in the study setting in Germany. The record does not report reasons for preference or results for other outcomes that could clarify the experience behind the choice.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Comparison of Two Urostomy Bags (2-piece). — NCT00761748.
• Registry record last updated 2013-01-01; status last verified 2012-11.
• Results first posted 2013-01-01.
• 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.

21. Record Summary

The registry record describes a completed, phase 3 randomized crossover study comparing SenSura Uro 2-piece with Convatec 2-piece among urostomy-operated persons in Germany. The primary endpoint is preference after exposure to both products, assessed by questionnaire at the end of the second crossover period, with a timeframe of 6 weeks. The endpoint population is described as per protocol.

The posted counts record 21 preferences for SenSura and 4 for Convatec, with 25 listed for each. The reported risk difference is -0.68 for Convatec relative to SenSura, with an unadjusted p-value of <0.001. The registry lists adverse-event counts separately and reports no posted secondary outcomes or analysis records.

Important statistical details—including the analysis method, missing-data handling, and crossover-specific adjustments—are not reported in the registry record. The results therefore support a description of the recorded preference comparison, with interpretation limited by the available analysis documentation.