PleuraSeal Post Market Study (Europe): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PleuraSeal Post Market Study (Europe) (NCT00704171), a randomized phase 4 study. The primary outcome is Percentage of Subjects Remaining Air Leak Free From Time of Skin Closure to Hospital Discharge..

2. Clinical Question

The registry describes a prospective, multicenter, randomized post-market study. In statistical terms, the central comparison is between proportions: the fraction of participants meeting the air-leak-free outcome in one randomized arm versus the fraction in the other. The endpoint is clinically connected to the purpose of the device, while the trial's randomized allocation is intended to make the comparison between assigned groups interpretable. The registry record does not report the randomization procedure, details of concealment, or which people were masked.

3. Trial Design

This was the PleuraSeal Post Market Study (Europe), a completed Phase 4, prospective, multicenter, randomized study with a parallel-group model and single masking. It enrolled 121 participants. The registry lists a start date of 2008-01 and primary completion in 2008-12. Its official title describes evaluation of the PleuraSeal Sealant System as an adjunct to standard closure techniques to control visceral pleural air leaks following elective pulmonary resection via open thoracotomy.

Participants were assigned to PleuraSeal or standard of care. The PleuraSeal arm received the PleuraSeal Lung Sealant System; the control arm received standard tissue closure techniques, specified as sutures or staples only. The brief description identifies elective pulmonary lobectomy and segmentectomy via open thoracotomy as the operative setting. Arm denominators for the primary outcome were 62 and 59, respectively. These are the posted outcome denominators and should not be read as a description of every analysis population in the trial.

Randomization and a parallel-arm structure make the arm comparison the main design feature to consider when reading the results. Random assignment can reduce systematic differences at baseline on average, although the registry material does not provide baseline characteristics or the method used to generate and conceal assignments. Single masking is recorded, but the identity of the masked parties and the masking procedures are not reported in the registry record. The protocol's planned enrollment target, original sample-size rationale, and planned statistical methods are not reported in the registry record.

The registry lists six outcome measures and seven analyses. Besides the primary air-leak-free endpoint, secondary outcomes include intra-operative air-leak sealing success, time from skin closure to the last observable air leak, duration of chest drainage, and duration of hospitalization. Results are posted for only four of the secondary outcomes. Details of the two secondary outcomes without posted results are not reported in the registry record. This distinction matters: the design describes what the study set out to assess, while the posted results determine what can be evaluated from this 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: Subjects were evaluated for pre-operative and intra-operative eligibility criteria. Randomization occurred intra-operatively.

Overall Study

Reasons for not completing this period:

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 Percentage of Subjects Remaining Air Leak Free From Time of Skin Closure to Hospital Discharge., measured over 30 days.

The primary endpoint is the percentage of participants remaining air-leak free from the time of skin closure to hospital discharge. The registry gives a timeframe of 30 days. This is a binary outcome at the participant level: each person either met the definition of remaining air-leak free over the stated period or did not. The measure is therefore a proportion, not a measure of the number or duration of individual leaks.

As a general statistical concept, a binary endpoint can make an event-based comparison straightforward to communicate: the result describes how often the defined outcome occurred in each arm. Here, the endpoint reflects whether air-leak freedom persisted through a clinically relevant part of the post-operative course. It complements the intra-operative sealing outcome, which addresses sealing success during the procedure rather than persistence through discharge.

The registry wording links the endpoint to hospital discharge, while the stated timeframe is 30 days. The record does not explain how discharge before or after that point was handled, how an air leak was assessed, or how missing outcome information was classified. Those details are important for understanding the exact measurement process but are not reported in the registry record. The percentages should therefore be read as the posted outcome summaries, not as a complete description of endpoint ascertainment.

The endpoint is useful for comparing the proportions meeting the same stated criterion across randomized groups. It does not, on its own, show the duration of any leak, the clinical importance of a leak, or the effect on other outcomes such as chest drainage or hospitalization. Those are separate questions reflected in other outcomes listed by the registry.

7. Results Posted in the Registry

• PleuraSeal: 41.9% (26/62) versus 30.5% (18/59) on control; risk difference 11.4 percentage points (95% CI -5.6 to 28.4), risk ratio 1.37 (0.85–2.23); unadjusted two-proportion z-test p = 0.192.

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.

Percentage of Subjects for Whom Intra-operative Air Leak Sealing Success is Achieved.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • PleuraSeal: 71.0% (44/62) versus 23.7% (14/59) on control; risk difference 47.2 percentage points (95% CI 31.6 to 62.9), risk ratio 2.99 (1.84–4.85); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for PleuraSeal than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary-outcome pattern is not uniform in what it measures. The intra-operative endpoint concerns immediate sealing success during the procedure and shows a clearer arm contrast than the primary outcome. Other listed measures address the later course: time from skin closure to the last observable air leak, duration of chest drainage, and duration of hospitalization. Their numerical results are not included in the available posted details. It is therefore not possible to summarize the direction or size of every secondary outcome from this record.

The intra-operative result relates to the primary question but is not a substitute for it. Sealing success at the time of surgery may be relevant to the intended purpose of the device, while the primary endpoint asks whether air-leak freedom persisted from skin closure through hospital discharge. Success at one time point does not establish the later outcome, and a later outcome can be affected by factors not captured by an intra-operative measure. The registry does not report analyses linking these endpoints at the participant level.

Secondary results generally carry less weight than a prespecified primary result when the study has multiple outcomes, particularly if no multiplicity plan is available. In general, testing many outcomes creates more opportunities for apparently noteworthy results by chance. The registry record does not report how multiple comparisons were handled or whether any secondary endpoint was designated for confirmatory interpretation. The intra-operative p-value should accordingly be understood as a posted secondary result, not as a replacement primary conclusion.

The registry lists six outcome measures but reports four secondary outcomes in the information. The detailed results available for this review do not include numerical findings for all of those measures. An absence of results in the record is not evidence of no effect, nor can it be used to infer that an outcome was unfavorable. The direction, uncertainty, and analysis method for those unreported results are not reported in the registry record. This limits the assessment of whether the procedural result was accompanied by differences in later recovery measures.

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

• Percentage of Subjects for Whom Intra-operative Air Leak Sealing Success is Achieved.
• Time From Skin Closure to Last Observable Air Leak.
• Duration of Chest Drainage
• Duration of Hospitalization

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary percentage: the percentage of participants who remained air-leak free. The primary comparison is consequently a comparison of two proportions. The table presents the proportion in each randomized arm, and the plotted or tabulated comparison summarizes the difference between those proportions. The simple recalculation is unadjusted, meaning it uses the posted group summaries rather than adjusting for other participant characteristics.

What does the risk difference describe?

The risk difference expresses the difference between the event proportions in the two arms. A value of zero represents equal proportions; values on either side represent differences in opposite directions, depending on which arm is subtracted from which. In this record, the comparison is framed as PleuraSeal relative to standard of care. The interval for the primary risk difference includes zero, so the data do not pin down a direction with the precision that an interval excluding zero would indicate. The risk difference is an absolute contrast in proportions and is not the same as a relative measure.

How do relative measures differ?

A risk ratio compares proportions by division, while an odds ratio compares the odds of the event between groups. These relative measures can be useful when the question concerns proportional rather than absolute contrast, but they answer different descriptions of the same binary data. Their interpretation depends on which event is coded as the outcome. The registry's posted analysis includes relative measures for the primary outcome, but this page does not treat them as substitutes for the absolute arm percentages or risk difference. The registry record does not describe a planned hierarchy among these measures.

What does the confidence interval add?

General explanation: a confidence interval is a range produced by a statistical method that conveys uncertainty around an estimate. It is not a range containing a known fixed proportion of individual outcomes, nor does it assign a probability to the true effect after the data are observed. For a risk difference, zero is the no-difference reference point. The primary interval extends across that point, showing that the estimate is not highly precise about the direction of the difference. For the intra-operative endpoint, the posted recalculated interval lies above zero. The separate endpoints should not be conflated simply because both are percentages.

Why are two p-values visible?

The registry reports a Fisher Exact test for the primary comparison, with p = 0.257. The simple unadjusted recalculation reports p = 0.192. Fisher's Exact test evaluates an association in a two-by-two table using an exact probability calculation. The recalculation is a separate unadjusted analysis based on the posted summary counts. The registry record does not explain the difference between the results, and no explanation should be assumed. The posted sponsor analysis and the recalculation are therefore identified separately rather than blended into one result.

In general, the p-value is conditional on a null hypothesis and a statistical model. A smaller p-value indicates that data at least as incompatible with that null model would be less frequently expected under the model; it is not a measure of effect size or clinical importance. The primary p-values are not small, but the registry record does not state the planned significance threshold or multiplicity strategy for the primary analysis. That missing context limits what can be concluded from a threshold-based interpretation.

What does randomization contribute?

Randomized allocation is intended to make the assigned groups comparable in expectation, reducing selection as a source of systematic difference. It does not guarantee that every measured or unmeasured feature will be balanced in a particular study. The registry records randomization and a parallel model, but the sequence-generation approach, concealment, and baseline comparisons are not reported in the registry record. The single-masked designation is also not accompanied by details of who was masked or how masking was maintained.

The primary outcome denominators are 62 and 59. The registry enrollment is 121. Those values are consistent with the posted arm totals, but the record does not describe exclusions, withdrawals, or whether every randomized participant was included in each analysis. It would therefore be inappropriate to label the results as an intention-to-treat analysis or to infer a particular missing-data method. Analysis populations and handling of missing outcomes are not reported in the registry record.

What does the secondary endpoint test?

The intra-operative outcome is also binary and is reported as the percentage achieving sealing success during the study procedure. Its recalculated risk difference interval excludes zero, and both the recalculated and sponsor-reported p-values are shown as p < 0.001. In general, a large contrast on a procedural endpoint does not determine the result on a later endpoint: the timing and definition differ. The primary outcome asks whether participants remained leak free through discharge, whereas the secondary procedural measure concerns sealing at the time of the operation.

The study lists other secondary measures that are not binary percentages, including time from skin closure to the last observable air leak, duration of chest drainage, and duration of hospitalization. Their analysis details and results are not reported in the registry record. The posted registry information also does not describe adjustments for multiple endpoint testing, interim analyses, or a statistical analysis plan. These absences should be treated as limits on what can be reconstructed from the record, not as evidence that a particular method was or was not used.

11. Confidence Intervals and Precision

The arm percentages are the most direct description of the posted primary outcome: 41.9% for PleuraSeal and 30.5% for standard of care. The recalculated risk-difference interval is the main guide to how precisely the contrast is estimated. Its lower bound is below zero and its upper bound above zero. Thus the interval includes no difference and also allows for effects in either direction. The point estimate alone cannot express that uncertainty.

General explanation: a confidence interval depends on the observed data and the calculation method. A wider interval indicates less precision than a narrower interval, while an interval's position relative to the no-difference value indicates which effect values are compatible with the interval. Neither feature answers whether a difference is important to patients or clinicians. The registry does not report a prespecified clinically important threshold for this endpoint, so the clinical meaning of particular effect magnitudes cannot be established from the record.

The primary comparison is based on 62 participants in one arm and 59 in the other. The limited group sizes help explain why a range of possible effect values remains compatible with the data, although the precise impact of group size cannot be separated from event frequency and analysis method using the summary alone. The registry's Fisher Exact p-value and the simple recalculated p-value are not identical; the record does not explain the difference. The interval and p-value should therefore be read as separate summaries rather than treated as interchangeable.

The intra-operative endpoint has a distinct interval that excludes zero, providing a more directionally clear comparison under the recalculated method. That greater clarity for the procedural endpoint does not transfer automatically to the primary endpoint. Its definition and timing are different. Also, the registry does not report interval estimates for all listed secondary outcomes in the available details, so precision cannot be assessed consistently across every outcome.

Overall, the primary result is not precise enough to settle the direction of the underlying difference. It is appropriate to describe the observed arm percentages and the interval's inclusion of zero, while avoiding claims that the interval proves equivalence or rules out meaningful effects. Equivalence would require a defined margin and an analysis designed for that question; such a margin is not reported in the registry record.

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 sample-size display is a planning illustration based on the observed effect, not a reconstruction of the study's original design. For this binary endpoint, the listed figures are participants per arm, not total events. The table considers planning for 100%, 75%, and 50% of the observed effect. Each row gives the number of participants per arm for 80% power and for 90% power under its stated assumptions.

The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The sample-size assumptions used for the study's own original design are not reported in the registry record. These display assumptions therefore describe the illustration only and should not be attributed to the investigators' original planning.

In plain language, 80% power means that, under the planning model and for the specified effect, a study of that size would have an 80% chance of producing a result that meets the chosen statistical criterion if that effect were the true one. The 90% column represents a higher chance under the same model and effect, and consequently requires more participants per arm. These are design calculations, not statements about the probability that the trial's conclusion is correct.

The rows show the general pattern that planning to detect a smaller effect requires more participants. The observed effect is only one estimate from this study and may not equal the effect in a future study. For that reason, the reduced-effect rows can be useful as sensitivity illustrations, while none should be mistaken for a definitive forecast. The registry's sample-size section is not observed power: it does not calculate the probability that the completed trial detected its actual effect after the results were known.

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 = 0.305; treatment proportion p₁ = 0.419; average p̄ = 0.362.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6797 = 1.3322.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6749 = 0.5680.
4. n = (1.3322 + 0.5680)² / (0.1143)² = 276.5, rounded up to 277 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 <- 0.305084745762712                          # control proportion
p1 <- 0.419354838709677                          # 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(704171)
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 = 277 (80% power), 370 (90% power)
 75% of observed effect: n per arm = 484 (80% power), 648 (90% power)
 50% of observed effect: n per arm = 1,068 (80% power), 1,430 (90% power)
power.prop.test: 276.5 
Simulated power at n = 277 per arm: 0.799 (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

For the primary endpoint, the registry reports the sponsor's Fisher Exact analysis as p = 0.257. The simple unadjusted recalculation based on the posted group summaries gives p = 0.192. These are distinct results, and the registry record does not explain why they differ. The record does not provide enough detail to attribute the difference to a specific analysis choice, adjustment, or data-handling decision.

The sponsor result should be read as the analysis reported in the registry, while the recalculation is a transparent unadjusted comparison derived from the posted summaries. Neither p-value replaces the arm percentages or the interval, and neither should be interpreted alone. The interval for the recalculated primary risk difference includes zero, consistent with uncertainty about the direction of the comparison. No discrepancy between the sponsor analysis and the recalculation is flagged in the record; nevertheless, the reason for the different p-values is not reported in the registry record.

For the intra-operative endpoint, the sponsor-reported Fisher Exact result and the recalculated result are both reported as p < 0.001. The close agreement in the displayed p-value does not mean the analyses are identical in every respect; the record identifies the test used for the sponsor analysis but does not provide a full statistical analysis plan. This distinction between sponsor-reported analysis and recalculation is maintained so readers can see which result comes from the registry and which is an unadjusted re-analysis of posted summaries.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity strategy for the primary and secondary outcomes. This matters because the study lists several outcomes, and separate statistical tests across several endpoints can increase the chance of at least one apparently strong result when all null hypotheses are true. General explanation: multiplicity methods can control that chance or define a hierarchy among hypotheses, but the appropriate approach depends on the study's objectives and prespecified plan. No such plan is available, so this page does not infer that the reported secondary p-value was or was not adjusted.

The record also does not report interim analyses, stopping rules, or whether any analyses were specified before enrollment began. It would be speculative to assume either that interim looks occurred or that they did not. The original statistical analysis plan, sample-size justification, and analysis thresholds are not reported in the registry record. The listed illustration assumptions belong to the planning display and do not fill that gap.

Missing-data handling is another important unknown. The primary outcome is framed through hospital discharge and has a 30-day timeframe, but the registry information does not state how missing or unevaluable outcomes were treated. It does not describe whether participants were analyzed according to assigned group, whether any participants were excluded, or whether imputation or other methods were used. The outcome denominators alone do not establish the analysis population or the handling of missingness.

Analysis populations are not reported in the registry record. In particular, the information does not say whether the reported analyses used all randomized participants, only participants with available outcome data, or a different defined group. The registry marks the study as randomized, but that fact does not establish which analysis set was used. Baseline characteristics and the protocol details needed to evaluate the consequences of exclusions are also not included.

These omissions do not invalidate the posted results, but they limit how completely a reader can audit the analysis. The strongest grounded description is to report the arm summaries and the named sponsor test, distinguish those from the simple recalculation, and avoid inferring an unreported plan. The record does not support a claim that results were corrected for multiple testing or that missing outcomes had no influence.

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: pneumothorax (8.1%), fatigue (3.4%), hydropneumothorax (3.4%), pain (3.2%), empyema (3.2%).

The adverse-event summary lists serious adverse events affecting 16 of 62 participants in the PleuraSeal arm and 11 of 59 in the standard-of-care arm. Other adverse events are listed for 2 of 62 and 4 of 59 participants, respectively. These are participant counts in the posted safety groups; they are not a comparison adjusted for follow-up time, event recurrence, or participant characteristics. The registry record does not provide such details.

The listed top serious-event terms include Pneumothorax at 8.1%, Fatigue at 3.4%, Hydropneumothorax at 3.4%, Pain at 3.2%, Empyema at 3.2%, and Pneumonia at 3.2%. These terms describe events recorded in the registry and do not, by themselves, establish that an event was caused by the device or the procedure. The record does not provide event-level timing or attribution in the information.

Death counts are not reported in the registry record. Serious adverse event totals should be interpreted descriptively and in the context of the specific trial groups, not as proof that one arm is safer or less safe. No statistical safety comparison or causal analysis is reported.

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

The primary result shows that the posted percentage remaining air-leak free was 41.9% in the PleuraSeal arm and 30.5% in the standard-of-care arm. The observed proportions therefore favor PleuraSeal descriptively. However, the recalculated confidence interval for the risk difference extends across zero, and the sponsor-reported Fisher Exact p-value is p = 0.257. The result does not precisely establish the direction or size of the underlying primary-outcome difference.

That uncertainty is not the same as evidence that the groups are equivalent. Equivalence requires a prespecified margin and a design and analysis intended to determine whether plausible effects fall within that margin. No equivalence margin is reported in the registry record. The record also does not give enough information to reconstruct missing-data handling, analysis populations, or the original statistical plan. Conclusions should stay within the posted comparison.

The secondary intra-operative endpoint has a different result pattern, with the registry reporting higher sealing-success percentage in the PleuraSeal arm and a Fisher Exact p-value of p < 0.001. This is evidence about sealing success during the procedure, not direct proof of the primary endpoint through hospital discharge. Other secondary outcome results are not included in the detailed information, preventing a complete assessment of the trial's listed outcomes.

The findings apply most directly to the study population described in the registry: subjects undergoing elective pulmonary lobectomy or segmentectomy via open thoracotomy. The record does not establish how results would extend to other operations, populations, or clinical settings. It also does not provide detailed participant characteristics or baseline comparisons to support assessment of representativeness.

This page describes a statistical reading of a registry record, not a recommendation about care. The posted data can be used to understand what was observed and how uncertain the primary comparison remains. They cannot, on their own, settle broader questions about clinical benefit, harms, or applicability. Those judgments require evidence and context beyond the summaries available in this record.

18. Why This Trial Matters Statistically

This study illustrates why statistical interpretation should keep the endpoint, estimate, interval, and test result in view at the same time. A visible difference between arm percentages is a descriptive observation. The interval shows that the primary contrast remains uncertain about direction, and the sponsor's Fisher Exact result is not the same as the simple recalculation. Reporting these elements separately avoids reducing a randomized trial to one number or one threshold-based label.

It also highlights the importance of distinguishing an immediate procedural outcome from a later patient-level outcome. Intra-operative sealing success is closely related to the device's stated purpose, but the primary question extends through hospital discharge. The distinct timing and definitions mean that a strong secondary result cannot automatically settle the primary comparison. This is a general lesson in endpoint interpretation: outcomes can be related while still answering different questions.

The post-market setting and randomized design make the record informative about an evaluation of the device in the described surgical context. At the same time, important design and analysis details are absent, including the original sample-size rationale, analysis populations, missing-data approach, and multiplicity plan. Recognizing these absences is part of statistical interpretation, not an attempt to fill them with assumptions.

Finally, the planning illustration makes clear how sample size depends on the effect a future study is intended to detect. Smaller target effects call for more participants under the stated assumptions. Those calculations are distinct from the completed trial's observed results and do not tell us whether that trial had adequate power. Keeping design planning separate from retrospective interpretation helps prevent misleading claims about what the study could or could not detect.

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 registry summary does not report the original sample-size justification, protocol assumptions, or planned significance threshold. The displayed planning calculations use a separate illustration based on the observed effect and cannot be taken as the trial's design rationale. The record also does not describe random sequence generation, allocation concealment, or the individuals masked under the single-masked designation.

Endpoint ascertainment details are limited. The primary measure refers to remaining air-leak free from skin closure to hospital discharge, with a 30-day timeframe, but the registry does not explain how the outcome was assessed, how discharge timing was handled, or how missing observations were classified. The analysis populations and participant flow through each outcome are not reported in the registry record.

The primary sponsor-reported Fisher Exact p-value differs from the simple unadjusted recalculation, and the registry does not explain why. The record does not contain a full statistical analysis plan that would clarify the intended analysis or reconcile the results. The primary interval itself includes zero, so precision about the direction of the comparison is limited. The available data also do not establish an equivalence margin or a clinically important threshold.

Although the record lists several secondary outcomes, full numerical results are not available for all of them in the information. The registry does not report a strategy for accounting for multiple comparisons. Safety summaries are aggregate counts; event attribution, timing, and detailed comparative analyses are not reported in the registry record. Death counts are also not reported.

Finally, the described population is specific to elective pulmonary resection via open thoracotomy, and the registry summary does not provide detailed baseline characteristics. These limitations constrain both auditability and generalization. They do not prove that omitted methods were inadequate; they mean that the methods cannot be assessed from the available registry information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: PleuraSeal Post Market Study (Europe) — NCT00704171.
• Registry record last updated 2016-10-27; status last verified 2016-09.
• Results first posted 2010-03-15.
• 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, single-masked, parallel Phase 4 post-market study of the PleuraSeal Lung Sealant System as an adjunct to standard tissue closure after elective pulmonary resection via open thoracotomy. Enrollment was 121. The primary endpoint was the percentage remaining air-leak free from skin closure to hospital discharge, with a 30-day timeframe.

The posted primary percentages were 41.9% for PleuraSeal and 30.5% for standard of care. The recalculated interval includes zero; the sponsor-reported Fisher Exact result was p = 0.257. The secondary intra-operative sealing-success result showed a different pattern, with a sponsor-reported p-value of p < 0.001. Several design, analysis, and outcome details are not reported in the registry record, so interpretation should remain focused on these posted results and their uncertainty.