Active Clearance of Chest Tubes After Cardiac Surgery: A Prospective Randomized Controlled Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Active Clearance of Chest Tubes After Cardiac Surgery: A Prospective Randomized Controlled Study (NCT02808897), a randomized na study. The primary outcome is Number of Participants With Postoperative Atrial Fibrillation.

2. Clinical Question

The trial’s stated purpose was to assess whether active tube clearance could reduce postoperative atrial fibrillation and to evaluate other complications, including retained blood syndrome. The latter was described as a composite endpoint that includes re-exploration for bleeding or tamponade and interventions for hemothorax, pericardial effusion, or pleural effusion. The record also lists individual secondary outcomes related to invasive fluid removal, re-exploration, chest-tube occlusion, and pericardial or pleural drainage.

The primary comparison is between two drainage strategies used after cardiac surgery. It concerns the recorded incidence of a defined event during the specified follow-up, rather than the duration or severity of atrial fibrillation, or outcomes after hospital discharge. Those other questions are not reported in the registry record.

3. Trial Design

The registry describes a prospective, randomized, parallel-group study of active tube clearance versus standard drainage after cardiac surgery. Enrollment is listed as 520. The study status is completed, with a start date of 2015-11 and a primary completion date of 2018-12. The sponsor is Montreal Heart Institute. The phase is listed as NA.

The control arm received one standard chest tube in the mediastinum, with at most three additional commercially available standard or silastic chest tubes in specified mediastinal or pleural spaces. The active-clearance arm received one mediastinal chest tube using PleuraFlow® active tube clearance, alongside at most three other standard or silastic tubes. Thus, the group contrast concerns the use of active clearance in one tube within the drainage arrangement described in the record.

Masking is listed as single, but the record does not identify who was masked or how masking was maintained. Allocation is listed as randomized. The record does not report the sequence-generation method, allocation concealment, stratification factors, or a detailed protocol for implementing randomization. It also does not report the trial’s original sample-size justification or the assumptions used in its design.

The primary endpoint counts participants with postoperative atrial fibrillation from post index surgery through hospital discharge, an average of 30 days. The registry defines the event as a new-onset episode lasting at least 60 min on telemetry or EKG. Secondary outcomes include intrathoracic fluid-removal procedures for retained blood complications, re-exploration for bleeding or tamponade, chest-tube occlusion, and pericardial or pleural drainage procedures. The posted results include three secondary comparisons; other secondary outcome results are not reported in the registry record.

The record does not describe the analysis population, handling of missing outcome data, or a prespecified statistical analysis plan. Those omissions limit what can be established about how participants were included in each analysis and whether the posted comparisons follow the original planned analysis.

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: 30 patients were excluded after randomization because of the identification of an exclusion criteria Atrial fibrillation history (n = 10) Transcatheter aortic valve replacement (n = 1) Deep hypothermic arrest (n = 1) Active endocarditis (n = 3) Inherited bleeding disorder (n = 1) Minimally invasive procedure (n = 14)

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 Number of Participants With Postoperative Atrial Fibrillation, measured over From post index surgery through hospital discharge, an average of 30 days.

The primary endpoint is the number of participants with postoperative atrial fibrillation (POAF). It is a binary outcome: each participant is classified according to whether a qualifying event was recorded during the specified period. The registry’s definition is any new-onset atrial fibrillation episode lasting at least 60 min on telemetry or EKG, from post index surgery through hospital discharge. The stated average follow-up is 30 days.

Using a defined event threshold makes the outcome more reproducible than a loosely specified clinical label. It also establishes which episodes count for the primary comparison. The measure is the number of participants with an event, not the number of separate episodes, the time spent in atrial fibrillation, or the severity of symptoms. Those measures are not reported in the registry record.

This endpoint matches the study’s stated purpose of assessing whether active tube clearance affects the rate of postoperative atrial fibrillation. The registry also describes a rationale involving retained blood complications and lists procedural outcomes that can reflect the need to remove intrathoracic fluid or address bleeding or tamponade. The primary endpoint and these secondary outcomes therefore address related but distinct questions: the primary measure concerns a rhythm event, while the listed secondary measures concern complications and interventions.

As a general statistical point, a binary endpoint allows a comparison of the proportion of participants with an event in each randomized group. It does not, by itself, explain why an event occurred or establish that a difference is caused by the assigned drainage strategy. Interpretation also depends on the precision of the estimate, the analysis methods, completeness of outcome ascertainment, and the context of the other outcomes.

7. Results Posted in the Registry

• Active Tube Clearance Drainage: 13.7% (33/241) versus 15.7% (39/249) on control; risk difference -2.0 percentage points (95% CI -8.2 to 4.3), risk ratio 0.87 (0.57–1.34); unadjusted two-proportion z-test p = 0.538.

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.

Number of Participants Requiring Invasive Procedure for Intrathoracic Fluid Removal (Retained Blood Complications)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Tube Clearance Drainage: 6.2% (15/241) versus 10.8% (27/249) on control; risk difference -4.6 percentage points (95% CI -9.5 to 0.3), risk ratio 0.57 (0.31–1.05); unadjusted two-proportion z-test p = 0.068.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active Tube Clearance Drainage and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Requiring Re-exploration for Bleeding or Tamponade

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Tube Clearance Drainage: 1.7% (4/241) versus 5.6% (14/249) on control; risk difference -4.0 percentage points (95% CI -7.2 to -0.7), risk ratio 0.30 (0.10–0.88); unadjusted two-proportion z-test p = 0.020.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Active Tube Clearance Drainage than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Patients Requiring Pericardial Drainage Procedure

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Tube Clearance Drainage: 0.8% (2/241) versus 2.0% (5/249) on control; risk difference -1.2 percentage points (95% CI -3.3 to 0.9), risk ratio 0.41 (0.08–2.11); unadjusted two-proportion z-test p = 0.272.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active Tube Clearance Drainage and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address complications and interventions related to retained blood or intrathoracic fluid, rather than the primary rhythm outcome. For the posted secondary comparisons, the event counts are lower in the active-clearance arm than in the standard-drainage arm. That direction is consistent across the secondary comparisons with arm-level results, but the results do not all have the same degree of statistical precision. Other outcomes listed as secondary do not have posted arm-level comparisons in the registry record.

This pattern is relevant to the study’s stated rationale: active tube clearance was intended to be assessed not only in relation to postoperative atrial fibrillation but also in relation to retained blood complications and related procedures. These outcomes are related to the drainage strategy, but they are not interchangeable with the primary endpoint. A pattern in procedural outcomes cannot, on its own, establish an effect on postoperative atrial fibrillation, and the primary result does not settle the secondary questions.

The secondary comparisons are unadjusted. As a general statistical issue, examining multiple outcomes creates multiple opportunities for chance findings. Unless a testing hierarchy or multiplicity adjustment is specified, an individual unadjusted p-value should not be treated as if it were the only test conducted. The registry record does not report a multiplicity plan or identify a prespecified hierarchy for the secondary outcomes. The secondary results therefore provide descriptive context, but carry less weight for confirmatory conclusions than a prespecified, appropriately analyzed primary endpoint.

The record lists five secondary outcome measures, but only three have posted arm-level results and comparisons. The absence of posted results for the others means their findings cannot be assessed from the registry record. The overall secondary pattern should not be treated as a complete account of every listed outcome or as proof of a broad benefit across complications.

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

• Number of Participants Requiring Invasive Procedure for Intrathoracic Fluid Removal (Retained Blood Complications)
• Number of Participants Requiring Re-exploration for Bleeding or Tamponade
• Number of Participants Presenting With a Chest Tube Occlusion
• Number of Patients Requiring Pericardial Drainage Procedure
• Number of Patients Requiring Pleural Drainage Procedure

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, each participant is counted according to whether a qualifying postoperative atrial fibrillation event occurred during the stated follow-up. This is a binary outcome. The registry reports the event count and group size for standard drainage and active tube clearance, then gives a risk difference comparing the groups. The risk difference is expressed as the event proportion in the active-clearance group minus the event proportion in the standard-drainage group. A negative estimate therefore points toward a lower event proportion in the active-clearance group; it does not, by itself, establish that the difference is reliable or attributable to the intervention.

What does the confidence interval describe?

A confidence interval describes the uncertainty around an estimated effect under the statistical method used. For this comparison, the 95% interval for the risk difference runs from -0.082 to 0.043. Because zero lies within that interval, the estimate is compatible with no difference as well as with differences favoring either group. The interval is more informative than the point estimate alone because it communicates a range of values that remain compatible with the data and method. It is not a guarantee that the true effect lies in the interval, and it does not assign probabilities to particular effect values.

How should the p-value be read?

The unadjusted p-value for the primary comparison is 0.538. A p-value describes how unusual data at least as discrepant as those observed would be under a specified no-difference model and the analysis assumptions. It is not the probability that the no-difference model is true, and it is not a measure of clinical importance. The registry does not report an adjusted primary analysis. The value should be considered alongside the estimated risk difference and its confidence interval rather than used as a stand-alone decision rule.

Why use a risk difference?

The risk difference keeps the comparison on the absolute event-proportion scale. Its sign shows the direction of the estimated contrast, while its magnitude describes the estimated absolute separation between groups in the units used by the calculation. The registry also gives relative measures, but the primary comparison highlighted by the record is the risk difference. Relative measures answer a different question and can appear more or less pronounced depending on the underlying event proportions. Neither type of estimate removes uncertainty.

What does randomization contribute?

Random assignment is intended to make the groups comparable, on average, with respect to factors that might influence outcomes. It supports an interpretation of the group contrast as a comparison of assigned drainage strategies, provided trial conduct and analysis preserve that comparison. Randomization does not ensure that every characteristic is balanced in a particular study, nor does it correct for incomplete follow-up or selective exclusions. The registry lists randomized allocation but does not report the sequence-generation process, allocation concealment, analysis population, or missing-data approach. These details are therefore not reported in the registry record.

What does single masking establish?

The registry lists the study as single-masked. That label indicates that masking was used, but the record does not state whether participants, clinicians, outcome assessors, or analysts were masked. It does not explain how the masking was implemented or whether it remained in place. Without those details, the possible role of knowledge of treatment assignment in outcome assessment cannot be evaluated from the registry record.

What do the secondary comparisons add?

The posted secondary comparisons use the same general binary-outcome approach: participants with an event are counted within each arm and contrasted using risk differences, confidence intervals, and unadjusted p-values. The outcomes concern procedures or complications within 30 days post index surgery. Those comparisons may help describe the pattern of recorded outcomes, but each is an additional statistical comparison. No multiplicity adjustment or prespecified hierarchy is reported in the registry record. As a general statistical matter, making multiple comparisons increases the opportunity for at least one result to appear noteworthy by chance, so isolated unadjusted secondary findings warrant caution.

The registry record reports no analysis entries for the primary outcome and no reported analyses for the posted secondary outcomes. The displayed comparisons should consequently be read as the posted numerical results, not as a complete account of a prespecified analysis plan. The original trial’s statistical plan, any interim analyses, and the sample-size justification are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how tightly an effect estimate is determined by the data and statistical method. The primary risk-difference estimate is -0.020, with a 95% confidence interval from -0.082 to 0.043. This interval spans zero and includes estimates on either side of zero. The point estimate favors active clearance in direction, but the range indicates substantial uncertainty about the direction and size of the underlying difference.

A confidence interval is not a range of observed participant outcomes. It is an interval for the estimated group contrast. In general, narrower intervals indicate greater precision, while wider intervals indicate more uncertainty. An interval that includes zero does not prove there is no difference; it means that zero is among the values compatible with the data and method at the stated confidence level. Conversely, an interval excluding zero would not by itself establish clinical importance.

The primary interval should be considered together with the group event counts and the unadjusted p-value of 0.538. Neither the point estimate nor the p-value communicates the full range of uncertainty. The record does not report a clinically important difference threshold, so the interval cannot be judged against a prespecified threshold for importance. It also does not report an equivalence or non-inferiority margin.

The posted secondary intervals vary in their relationship to zero, but they are unadjusted comparisons and should be interpreted in that context. The precision of any estimate does not address risks of missing data, selective reporting, or limitations in outcome ascertainment. Details about those issues are 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 figures are planning illustrations based on the observed effect, not the original trial design calculation. For the primary outcome, they are expressed as participants per arm. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and detection of the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with 80% power under those assumptions; the 90% power column gives the corresponding number per arm for 90% power. In plain terms, power describes the chance that a study using the assumed effect and analysis would detect an effect at the specified significance level. It is a prospective planning concept, not a description of what happened in this completed trial.

For the primary outcome, the figures for planning for 100% of the observed effect are 5,066 participants per arm for 80% power and 6,782 participants per arm for 90% power. For planning for 75% of the observed effect, the figures are 9,132 and 12,225 participants per arm. For planning for 50% of the observed effect, they are 20,827 and 27,880 participants per arm. Smaller effects require more participants to detect under the same planning assumptions.

These are illustrations tied to the observed estimate, which itself is uncertain. They are not evidence that the completed study had a particular probability of detecting an effect. This is not observed power. The original design calculation and its assumptions are not reported in the registry record. The secondary-outcome planning figures should likewise be read as illustrations rather than as information about the trial’s original design.

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 = 0.157; treatment proportion p₁ = 0.137; average p̄ = 0.147.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5005 = 0.9809.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5003 = 0.4210.
4. n = (0.9809 + 0.4210)² / (-0.0197)² = 5,065.9, rounded up to 5,066 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 <- 0.156626506024096                          # control proportion
p1 <- 0.136929460580913                          # 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(2808897)
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 = 5,066 (80% power), 6,782 (90% power)
 75% of observed effect: n per arm = 9,132 (80% power), 12,225 (90% power)
 50% of observed effect: n per arm = 20,827 (80% power), 27,880 (90% power)
power.prop.test: 5065.9 
Simulated power at n = 5,066 per arm: 0.796 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study makes several statistical comparisons. Each comparison can produce a result that looks more pronounced by chance, so a set of unadjusted p-values does not carry the same interpretation as a single prespecified test. This trial has a primary endpoint and multiple listed secondary outcomes. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a plan specifying which secondary outcomes were intended to support confirmatory conclusions. The posted secondary p-values are unadjusted and should be read as exploratory or descriptive evidence rather than as a family of independently definitive tests.

The registry record does not report the original statistical analysis plan, interim analyses, or the trial’s sample-size justification. It also does not identify an analysis population, such as whether the primary comparison was based on all randomized participants or another defined group. Without these details, it is not possible to determine from the registry record how the posted results correspond to the original planned analyses.

Missing outcome data and participant exclusions can affect estimates if availability differs between groups or is related to outcomes. The registry does not describe the extent or handling of missing data, withdrawals, protocol deviations, or exclusions from analysis. These details are not reported in the registry record. Their absence does not demonstrate that missing data occurred; it means the record does not provide enough information to assess the issue.

The record lists a single-masked design but does not state who was masked. It also does not describe the method of outcome ascertainment beyond defining postoperative atrial fibrillation as an episode meeting the duration and recording criteria. The implications of masking for outcome assessment therefore cannot be evaluated fully. These reporting gaps limit assessment of the robustness and reproducibility of the analyses, even though the registry provides numerical estimates for the primary and some secondary outcomes.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports serious adverse events in the two drainage groups, with the numbers at risk varying by adverse-event category. For serious adverse events, 0 of 240 participants are reported in the standard-drainage group and 0 of 230 in the active-clearance group. For other adverse events, 0 of 230 and 0 of 240 are reported, respectively. The record lists 4 deaths in the standard-drainage group and 3 in the active-clearance group.

These figures should be read with their category-specific denominators; the at-risk numbers are not identical across the serious and other adverse-event categories. The registry lists no top serious adverse-event terms. The record does not provide event descriptions, causes of death, timing, relatedness to the drainage strategy, or an analysis comparing safety between groups. The death counts alone do not establish that the deaths were caused by either intervention.

As a general point, adverse-event summaries describe events recorded during the study, but interpretation depends on definitions, ascertainment, follow-up, and attribution. The registry figures do not support a complete safety assessment or a causal conclusion about comparative safety.

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

The primary result estimates the difference in the proportion of participants with postoperative atrial fibrillation between the drainage groups during the period from surgery through hospital discharge. The point estimate is -0.020, with a 95% confidence interval from -0.082 to 0.043 and an unadjusted p-value of 0.538. The estimate points toward fewer recorded events with active clearance, but the interval includes zero and effects in both directions. The result does not establish a clear difference in the primary outcome.

That interpretation is not the same as saying the treatments are equivalent, or that there is no possible effect. The confidence interval remains compatible with a range of effects, and the registry does not report an equivalence or non-inferiority margin. Nor does the result prove that a clinically important difference is absent; the record does not state a threshold for clinical importance against which the estimate could be judged.

The posted secondary results show lower event counts in the active-clearance group for the secondary comparisons that have arm-level results. Those findings are not substitutes for the primary result and are unadjusted. They should be interpreted cautiously because the record does not report a multiplicity plan, and arm-level results for all listed secondary measures are not available in the registry record.

The comparison concerns the drainage strategies as described in this trial and the recorded outcomes during the specified follow-up. It does not establish effects beyond hospital discharge, on outcomes not measured or reported, or in populations not described by the trial. The registry record does not report detailed information about the analysis population, missing data, or the original statistical plan, which limits further assessment.

In general, a randomized trial can provide evidence about differences between assigned groups, but estimates remain subject to uncertainty and to the quality of trial conduct and reporting. These results are statistical findings from the registry record, not medical advice. They do not, on their own, determine which drainage strategy should be used for an individual patient.

17. Why This Trial Matters Statistically

This trial illustrates why an estimated effect, its confidence interval, and the study’s analysis context should be read together. The primary point estimate favors active clearance in direction, but the interval includes zero and extends to values favoring either group. A single point estimate can look conclusive if uncertainty is ignored; the interval shows why the primary comparison remains unresolved in the posted results.

It also illustrates the difference between the primary endpoint and related secondary outcomes. The study’s rationale includes both postoperative atrial fibrillation and retained blood complications, but these outcomes capture different aspects of postoperative care. A consistent direction across some secondary comparisons may be worth noting, yet unadjusted secondary findings do not replace evidence from the primary comparison or establish a broad effect across all outcomes.

The sample-size illustrations show another important distinction: planning calculations based on an observed estimate are not the same as the trial’s original design justification, and they are not observed power. The registry provides assumptions for the illustrations, while the original design assumptions are not reported. Separating these concepts prevents a planning exercise from being mistaken for a retrospective assessment of what the completed trial could detect.

Finally, a registry record can provide useful design and outcome information while leaving important methodological details unreported. Here, the record identifies randomization and single masking but does not explain who was masked, how missing data were handled, or which analysis population was used. Statistical interpretation therefore depends not only on the numerical results, but also on recognizing what the record does and does not document.

18. 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.

The registry record leaves several trial-specific questions unresolved. Although masking is listed as single, it does not identify who was masked or describe how masking was maintained. The method for generating the random sequence and concealing allocation is also not reported. These details would help readers assess how assignment and outcome assessment were protected from bias.

The original sample-size justification and statistical analysis plan are not reported. The registry includes planning illustrations based on observed effects, but those do not establish the original design assumptions. The record also does not describe an interim-analysis plan, multiplicity handling, or a hierarchy for interpreting the secondary outcomes.

The analysis population and the handling of missing outcomes, withdrawals, exclusions, or protocol deviations are not reported. The registry lists five secondary outcomes, while posted arm-level results are available for three. The other listed secondary results are not reported in the registry record, so the secondary outcome pattern is incomplete from the available entries.

The primary endpoint is assessed through hospital discharge, with an average follow-up of 30 days. The record does not report longer-term outcomes or provide details about the timing and completeness of outcome ascertainment. The safety entries include adverse-event counts and deaths but do not describe causes, relatedness, or a comparative safety analysis. These limitations constrain interpretation of the trial-specific results; they do not show that an unreported analysis or event did or did not occur.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Active Clearance of Chest Tubes After Cardiac Surgery: A Prospective Randomized Controlled Study — NCT02808897.
• Registry record last updated 2024-03-06; status last verified 2023-08.
• Results first posted 2024-03-06.
• 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.

22. Record Summary

This completed prospective randomized parallel-group study compared standard drainage with active tube clearance drainage after cardiac surgery. The registry lists enrollment of 520, single masking, and Montreal Heart Institute as sponsor. The primary endpoint was the number of participants with postoperative atrial fibrillation from surgery through hospital discharge, an average of 30 days.

The primary risk-difference estimate was -0.020, with a 95% confidence interval from -0.082 to 0.043 and an unadjusted p-value of 0.538. The interval includes zero, so the posted result does not establish a clear primary-outcome difference. Some secondary outcomes have posted comparisons, but those results are unadjusted, and results for other listed secondary outcomes are not reported in the registry record.

The registry does not report the original sample-size justification, detailed analysis plan, analysis population, or missing-data handling. These omissions limit assessment of how the posted estimates relate to the trial’s original design and analyses.