Investigation of a New 1-piece Convex Ostomy Product: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Investigation of a New 1-piece Convex Ostomy Product (NCT02043782), a randomized na study. The primary outcome is Degree of Leakage.

2. Clinical Question

3. Trial Design

This completed study was a randomized, unmasked crossover investigation of an ostomy product. The registry identifies the allocation as randomized, the masking as none, and the model as crossover. Enrollment was 38. The listed conditions were stoma ileostomy and stoma colostomy, and the stated purpose was to investigate the performance and safety of a new ostomy product.

Three products were included: the Coloplast Test Product, each participant’s own product, and a competitor soft convex product. The arm descriptions say participants were randomized 1:1:1 into six possible treatment groups to allocate treatments to periods. The descriptions then specify a first product and a subsequent product selected from the other listed options. These descriptions establish that treatment order was randomized, but the registry record does not give a complete period-by-period protocol or explain the six sequences in further detail.

In a crossover design, participants can contribute observations under more than one product. This differs from a design in which each participant is assigned to just one product for the entire study. Consequently, the posted counts beside the product summaries should be read as the counts associated with those product observations, not assumed to be independent groups of distinct people. The registry reports 37 observations for the test product, 38 for own product, and 37 for the competitor product.

The primary outcome was degree of leakage, assessed over 14 +/- 3 days. The registry lists one outcome measure and no posted secondary outcomes. The start and primary completion dates were 2014-01 and 2014-04. The record gives no detailed account of treatment-period duration beyond the outcome timeframe, washout arrangements, adherence, or the process used to collect outcome ratings.

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.

Period 1

Reasons for not completing this period:

Period 2

Period 3

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 Degree of Leakage, measured over 14 +/- 3 days.

The primary endpoint was degree of leakage, a continuous measure recorded on a 32-point scale. The scale includes 0 for no leakage and 32 for the worst leakage, so lower values correspond to less leakage on the stated scale. The registry reports the mean and standard deviation for each product, with the outcome assessed over 14 +/- 3 days.

A continuous score can retain gradations of experience rather than reducing each observation to a simple yes-or-no outcome. Comparing mean scores therefore describes the average recorded leakage level in each product group. The standard deviation describes how spread out individual scores were around each group’s mean; it is not a confidence interval and does not express the precision of the mean by itself.

The endpoint is relevant to the stated purpose because leakage is the outcome named in the registry as the primary measure of product performance. However, the record does not explain how the scale was developed, whether it was validated, how ratings were collected, or what size of score difference would be important to participants. Those details are not reported in the registry record. The mean scores therefore describe the posted scale results, but do not alone establish the practical importance of a difference or capture other aspects of product performance and safety.

7. Results Posted in the Registry

• Own Product: mean 4.80 versus 2.60 on control; difference 2.20 (95% CI -0.18 to 4.58), standardized effect d = 0.42; z-test p = 0.070.
• Competitor Soft Convex: mean 2.50 versus 2.60 on control; difference -0.10 (95% CI -2.18 to 1.98), standardized effect d = -0.02; z-test p = 0.925.

8. Statistical Interpretation

9. Statistical Methods Explained

What do the means and standard deviations describe?

The endpoint is continuous, so the registry summarizes each product’s observations with a mean and standard deviation. A mean is the arithmetic average of the recorded leakage scores. The standard deviation describes the spread of scores around that mean: a larger value indicates more variability in the observed scores. It does not give the range of scores, the uncertainty around a treatment contrast, or the expected score for every participant.

The posted means were 2.6 for the test product, 4.8 for Own Product, and 2.5 for Competitor Soft Convex. The corresponding standard deviations were 4.8, 5.7, and 4.3. Since 0 represents no leakage and 32 the worst leakage, the score’s direction is clear: higher scores represent worse leakage on the scale. A mean is still only a summary, and it can conceal differences in the shape or distribution of individual scores.

How should the mean differences be read?

The reported comparisons use the test product as the reference. The recalculated estimate for Own Product is 2.2, based on its mean score of 4.8 compared with 2.6 for the test product. The estimate for Competitor Soft Convex is -0.1, based on its mean score of 2.5 compared with 2.6 for the test product. Positive values indicate a higher mean score for the comparator; negative values indicate a lower comparator mean. This interpretation follows the score direction, but does not determine whether a difference matters to participants.

These are unadjusted recalculations from the posted summary statistics. In general, a simple difference between means is most straightforward to interpret when the observations and design meet the assumptions of the calculation. Here, the study is described as a crossover, so observations from the same participant under different products may be related. A comparison that treats product groups as independent may not represent that within-participant structure. The registry record does not report an analysis that addresses it.

What does the confidence interval add?

General explanation: a confidence interval expresses uncertainty around an estimate under a particular statistical method. It gives a range of values that are compatible with the data and method; it is not a guarantee that the true value lies within that range, nor does it show the range of individual participant scores. The interval’s width indicates precision: a narrower interval represents greater precision, while a wider interval leaves more uncertainty about the size and direction of the contrast.

For Own Product, the recalculated 95% confidence interval is -0.182 to 4.583. For Competitor Soft Convex, it is -2.176 to 1.976. Both include no difference. The first allows a range from a small negative contrast to a larger positive contrast; the second allows contrasts in either direction. These intervals make clear why the point estimates alone are not enough to determine the comparative result.

What does the p-value convey?

The unadjusted p-values are 0.07 for Own Product and 0.925 for Competitor Soft Convex. General explanation: a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. A p-value also does not account for a design feature or analysis choice that is absent from the calculation.

Because these p-values are labelled unadjusted and the registry record does not report the primary analysis plan, they should not be treated as a complete account of inferential testing. The record lists one primary outcome, no posted secondary outcomes, and zero analyses. It does not report whether there were multiple planned comparisons, how any multiplicity was handled, or which comparison was designated as the principal contrast.

Why does crossover structure matter?

General explanation: crossover studies can use within-participant comparisons, which may account for stable differences between participants. At the same time, valid interpretation can depend on treatment order, period effects, and whether outcomes under one product are related to outcomes under another. The approach should reflect the randomized sequence and repeated observations. A summary-statistics recalculation that does not model those features cannot show how the trial’s intended analysis handled them.

The registry describes six possible treatment groups and random assignment of treatment order, but does not report a statistical model, handling of period or sequence, or a method for within-participant correlation. Those elements of the statistical plan are not reported in the registry record. The posted recalculations are therefore best treated as simple descriptive contrasts rather than as a reconstruction of the trial’s intended crossover analysis.

Why can over-dispersion matter?

General explanation: over-dispersion means that observed variability is greater than a statistical model expects. When a model understates variability, standard errors can be too small and confidence intervals too narrow. For this continuous endpoint, the posted standard deviations describe variation in the scores, but the registry does not report a formal assessment of model fit or over-dispersion. More generally, the variability and dependence structure should be represented appropriately in any analysis; the record does not establish how that was done.

The posted estimates, intervals, and p-values should thus be understood in relation to the simple calculation used and the information available in the record. They quantify uncertainty under that calculation, not every source of uncertainty about the study’s design, endpoint measurement, missing observations, or analysis choices.

10. Confidence Intervals and Precision

The recalculated confidence intervals show substantial uncertainty around both mean differences. For Own Product compared with the test product, the estimate is 2.2 and the 95% confidence interval extends from -0.182 to 4.583. For Competitor Soft Convex compared with the test product, the estimate is -0.1 and the 95% confidence interval extends from -2.176 to 1.976. Each interval includes no difference, and each permits values in more than one direction.

General explanation: a confidence interval is a measure of statistical precision around an estimate, conditional on the method and its assumptions. It should not be read as an interval containing most individual scores, nor as a probability statement about the true effect. A point estimate is the single best value from a calculation; the interval communicates that other values are also compatible with the data and method.

The intervals are based on unadjusted recalculations from product-level summary statistics. The registry describes a crossover design, but does not report a confidence-interval method that accounts for repeated observations within participants, treatment sequence, or periods. The intervals therefore characterize these simple recalculations, not necessarily the uncertainty under an analysis fully aligned with the trial design.

The standard deviations of 4.8, 5.7, and 4.3 show that observed scores varied within each product summary. The posted counts were 37 for the test product, 38 for Own Product, and 37 for Competitor Soft Convex. The registry does not describe how missing outcome data were handled or whether all randomized participants contributed to each comparison. These omissions limit interpretation of precision beyond the arithmetic uncertainty captured by the recalculated intervals.

Precision and practical importance are separate questions. The record does not identify a threshold for a meaningful score difference. Even a more precise estimate would need to be interpreted against such a threshold and the clinical context; the posted intervals alone cannot answer that question.

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.

The sample-size illustrations are planning calculations based on the observed differences, not the trial’s original design justification. The assumptions stated for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect. The original design assumptions, including any target effect or planned sample size rationale, are not reported in the registry record.

The values are participants per arm for 80% power and participants per arm for 90% power; they are not total sample sizes. The outcome is continuous, so the figures represent participants per arm, not total events. In plain terms, the 80% power column gives the number per arm in a hypothetical study designed to have an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column does the same for a higher chance of detection, which generally requires more participants per arm.

Each comparison has separate illustrations. For planning for 100% of the observed effect, the Own Product comparison lists 91 participants per arm for 80% power and 121 for 90% power. The Competitor Soft Convex comparison lists 32,597 per arm for 80% power and 43,638 for 90% power. The latter values are very large because the observed mean difference used for that illustration is close to zero. These figures are not estimates of the enrollment needed for a clinically meaningful effect unless that effect is the chosen planning target.

The table also considers planning for 75% and 50% of the observed effect. Smaller effects need more participants to detect under the same assumptions, so the illustrative counts increase as the effect being targeted becomes smaller. A curve presents the same general relationship visually: sample-size requirements rise as the target effect becomes smaller. These calculations are planning illustrations, not observed power for the completed trial.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 2.200; pooled standard deviation σ = 5.275.
2. n = 2 × (1.96 + 0.842)² × 5.275² / 2.200² = 90.3, rounded up to 91 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 2.2                      # observed difference in means
sigma <- 5.2753887086543                     # 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(2043782)
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 = 91 (80% power), 121 (90% power)
 75% of observed effect: n per arm = 161 (80% power), 215 (90% power)
 50% of observed effect: n per arm = 362 (80% power), 484 (90% power)
power.t.test: 91.2 
Simulated power at n = 91 per arm: 0.797 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure, degree of leakage, and zero analyses. It lists no posted secondary outcomes. It does not report a prespecified statistical analysis plan, a primary comparison, or whether additional comparisons were planned. The multiplicity strategy, if any, is not reported in the registry record.

Multiplicity arises when several hypotheses or comparisons are examined. General explanation: conducting multiple tests can increase the chance that at least one result appears notable by chance, so a study may specify a primary contrast or use an adjustment strategy. The two recalculated comparisons in the posted results are unadjusted. They should not be interpreted as though a multiplicity adjustment had been applied. The record does not establish whether the trial had additional planned analyses beyond the comparisons available in the posted summaries.

The registry does not report an analysis population, such as which randomized participants were included in the primary analysis or how participants with incomplete product periods were handled. It also does not describe adherence, exclusions after randomization, or missing outcome data. These matters are not reported in the registry record. As a result, the posted product counts cannot establish how many participants were randomized, completed every intended treatment period, or contributed to a particular analysis.

Missing data can affect both estimates and precision. General explanation: if outcome availability is related to participants’ scores, the observed cases may not represent all randomized participants; methods that address missingness depend on its amount, pattern, and reason. No missing-data method or sensitivity analysis is reported in the registry record. It is therefore not possible to assess whether missingness influenced the posted summaries.

For a crossover study, it is also important to know how repeated observations, treatment sequence, and period are handled. The registry describes randomized treatment order but does not report the statistical model or analysis population used for the primary outcome. These gaps prevent a full reconstruction of the trial’s inferential analysis and limit the conclusions that can be drawn from unadjusted summary-statistic comparisons.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cystitis (2.7%).

The registry reports serious adverse events for each product group as counts among those at risk. For the Coloplast Test Product, 1 of 37 participants was affected; for Own Product, 1 of 38 was affected; and for Competitor Soft Convex, 0 of 37 were affected. These are the serious-event counts posted for the respective product groups.

The registry also lists cystitis as a top serious adverse-event term, with 2.7%. This is a registry-listed percentage and is reproduced as reported. The record does not give enough detail to connect that term to a specific product-group count or to describe its timing or clinical course.

These counts are descriptive. They do not establish that an event was caused by a product, and the registry record does not report a comparative statistical analysis of serious adverse events. The crossover design also means that participants may contribute to more than one product group, so the group counts should not be assumed to represent independent sets of people.

Other adverse events affected 22 of 37 participants in the test product group, 12 of 38 in the Own Product group, and 23 of 37 in the Competitor Soft Convex group. Deaths are not reported in the registry record. The posted counts do not by themselves explain event definitions, severity beyond the serious classification, exposure duration, or whether all events were collected and coded in the same way across products.

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

The registry record describes a randomized, unmasked crossover investigation and posts mean leakage scores for three products. The test product mean was 2.6, the Own Product mean was 4.8, and the Competitor Soft Convex mean was 2.5 on a scale where 0 is no leakage and 32 is the worst leakage. The simple recalculated comparisons estimate a mean difference of 2.2 for Own Product relative to the test product and -0.1 for Competitor Soft Convex relative to the test product.

The associated confidence intervals are broad enough to include no difference and values in either direction. They express uncertainty under the unadjusted recalculation, not certainty about the products’ true comparative performance. The record does not report a crossover-aware analysis of the primary outcome, so these estimates should not be treated as the trial’s definitive inferential results.

These data do not establish superiority, equivalence, or non-inferiority. Equivalence and non-inferiority require prespecified margins and analyses; no such margins or analyses are reported in the registry record. A p-value near or far from a conventional threshold does not establish equivalence or lack of an effect. The record also does not report a threshold that would identify a meaningful difference on the leakage scale.

The findings do not describe every dimension of product performance. The posted primary endpoint concerns leakage, and the registry’s brief summary states that performance and safety were investigated. The registry record does not provide detail on other performance outcomes, participant preferences, adherence, or the experience of using each product. Its adverse-event counts are descriptive and do not establish causality or comparative safety.

The appropriate reading is limited to the posted summaries and the uncertainty around simple comparisons. Interpretation is further constrained by missing information about the analysis plan, crossover modeling, missing data, and analysis populations. These are limits of what the registry record allows a reader to conclude, rather than evidence that any unreported method or result was absent from the conduct of the investigation.

16. Why This Trial Matters Statistically

This investigation is statistically notable because it uses a randomized crossover design to compare products within a study involving participants with ileostomy or colostomy. Crossover designs can be useful when participants can use more than one intervention, because within-participant information may help distinguish product-related variation from stable differences among people. That potential advantage depends on the analysis matching the repeated-measures structure and the randomized treatment order.

The record makes the design recognizable but leaves important analytical details unspecified. It describes randomization into six possible treatment groups and gives sequences involving the test product, Own Product, and Competitor Soft Convex. It does not report how the primary comparison accounted for sequence, period, or correlation among observations from the same participant. The simple recalculated mean differences provide a transparent descriptive reference, while illustrating why design-aware analysis details matter.

The trial also illustrates the distinction between an estimated effect and its precision. The Own Product comparison has a positive point estimate, while the Competitor Soft Convex estimate is close to zero; both confidence intervals include no difference. The estimates alone therefore do not resolve the comparisons. A p-value cannot replace the interval, the endpoint’s interpretation, or a prespecified threshold for meaningful change.

Finally, planning calculations based on observed effects can vary sharply with the effect chosen. The observed effect for one comparison is close to zero, resulting in very large sample-size illustrations under the stated assumptions. This makes the illustrations useful for understanding how the planning target affects required enrollment, but not as a record of the study’s original design. The registry does not report that original justification.

For clinical researchers and biostatisticians, the record offers a practical example of how registry summaries can support descriptive interpretation while leaving key questions unanswered. Clear reporting of analysis populations, outcome handling, crossover models, and planned comparisons is important for judging how posted estimates relate to the randomized design.

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 specific to this study are apparent from the registry record. Although the design is identified as crossover, the record does not provide the complete schedule of treatment periods, explain all six possible treatment groups, or describe any washout arrangements. It therefore does not allow a reader to assess how treatment order or carryover was addressed.

The primary outcome description gives the score’s range and anchors, but does not report how leakage was assessed, who recorded the score, whether assessment was standardized, or whether the scale was validated. The outcome timeframe is 14 +/- 3 days, but the record does not give more detail about the timing or frequency of ratings. A mean score alone does not reveal the distribution of individual outcomes.

The registry reports product-level counts, means, and standard deviations, but does not report a crossover-aware primary analysis. It also does not identify the analysis population or explain missing data, exclusions, or incomplete treatment periods. These omissions make it difficult to determine how closely the posted summaries reflect all randomized participants and how uncertainty should be evaluated under the study design.

The study was unmasked, according to the registry. The record does not describe safeguards for outcome assessment or whether participants and assessors were aware of product identity. The potential relevance of awareness depends on how the outcome was collected, which is not reported.

The registry lists adverse-event counts but does not detail exposure time, event ascertainment, severity beyond serious classification, or comparative safety methods. It also does not report deaths. These constraints mean the safety figures are descriptive and do not establish causation. The record does not report a clinically meaningful threshold for the primary scale or the original sample-size rationale, further limiting interpretation of the observed differences.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Investigation of a New 1-piece Convex Ostomy Product — NCT02043782.
• Registry record last updated 2016-05-04; status last verified 2016-03.
• Results first posted 2015-12-08.
• 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

NCT02043782 is a completed, randomized, unmasked crossover investigation titled Investigation of a New 1-piece Convex Ostomy Product. The registry lists 38 enrolled participants with ileostomy or colostomy. The products were the Coloplast Test Product, Own Product, and Competitor Soft Convex.

The primary outcome was degree of leakage on a 32-point scale, with 0 indicating no leakage and 32 the worst leakage, assessed over 14 +/- 3 days. Posted means were 2.6 for the test product, 4.8 for Own Product, and 2.5 for Competitor Soft Convex. Recalculated unadjusted comparisons have confidence intervals that include no difference.

The record lists one outcome measure and zero analyses. A crossover-aware primary analysis, analysis population, missing-data method, multiplicity strategy, and original sample-size justification are not reported in the registry record. Serious adverse-event counts were 1 of 37, 1 of 38, and 0 of 37 across the respective product groups.