Pancreas Resection With and Without Drains: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pancreas Resection With and Without Drains (NCT01441492), a randomized na study. The primary outcome is 60-day ≥ Grade II Complication Rate.

2. Clinical Question

In statistical terms, the question is whether the observed frequency of participants experiencing a qualifying complication differed between the randomized groups, and how precisely that difference was estimated. Randomization supports a comparison between assigned strategies, but it does not by itself establish that the groups were comparable in every respect or resolve limitations in outcome reporting. The interpretation therefore rests on the posted counts, the registry’s analysis, and the uncertainty around the estimated difference.

3. Trial Design

The registry describes a randomized prospective multicenter trial of pancreas resection with and without routine intraperitoneal drainage. It used a parallel-group design, with participants assigned to No Drains or Drains, and masking was listed as none. The Drains arm was described as receiving the standard of care treatment. The study status is completed.

The record lists an enrollment of 399. The posted primary outcome counts are 72 participants in the No Drains arm and 76 in the Drains arm. The corresponding arm denominators for that outcome are 170 and 174. The registry record does not explain the difference between the enrollment figure and these outcome denominators, or state whether the outcome denominators reflect exclusions, missing observations, or another analysis-population definition. Those details should not be inferred from the counts alone.

The listed start was 2011-09 and primary completion was 2016-09. The registry includes the conditions Pancreas Tumor and Pancreatitis. It lists one reported analysis for the primary outcome, using a chi-squared method, with p = 0.804. The exact randomization procedure, allocation concealment, eligibility criteria, center-specific enrollment, adherence, crossover, and handling of participants who did not receive their assigned strategy are not reported in the registry record.

The registry lists ten outcome measures and one analysis. It also lists secondary outcomes concerning complication severity and frequency, serious adverse events, mortality, specific complications, length of stay, and crude cost. Results are posted for some secondary outcomes, but not all listed measures have results in the registry record in the registry record. These design and reporting details matter because the credibility and scope of a trial comparison depend not only on randomization but also on how outcomes and analysis populations were defined and reported.

4. Participant Flow and Accounting

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

Overall Study

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 60-day ≥ Grade II Complication Rate, measured over 60 days.

The primary endpoint is the number of participants with at least Grade II complications within 60 days of surgery. It is a binary participant-level outcome: each participant either had a qualifying complication within the specified period or did not. Complications were to be graded using CTCAE v4.0, with severity represented on a Grade 1–5 scale unless otherwise stated. The description says that grading schemes using A, B, C rather than 1–5 would be converted to severity scores from 1–3.

This endpoint is used to capture complications that meet a defined severity threshold during a fixed period after surgery. Counting participants rather than individual events means the outcome describes how many people experienced at least one qualifying complication; it does not describe the total number of complications per participant. The endpoint is clinically interpretable as a participant-level event measure, while its meaning depends on consistent event ascertainment, grading, and follow-up.

The posted values are 72 of 170 participants in the No Drains arm and 76 of 174 in the Drains arm. The registry’s definition calls for meticulous recording with standardized definitions, but does not report further details on adjudication, completeness of follow-up, or how multiple complications in one participant were handled for this primary count. Those procedures are not reported in the registry record.

7. Results Posted in the Registry

• Drains: 43.7% (76/174) versus 42.4% (72/170) on control; risk difference 1.3 percentage points (95% CI -9.1 to 11.8), risk ratio 1.03 (0.81–1.32); unadjusted two-proportion z-test p = 0.804.

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.

60-day ≥ Grade III Complication Rate

• 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:
  • Drains: 29.3% (51/174) versus 25.9% (44/170) on control; risk difference 3.4 percentage points (95% CI -6.0 to 12.9), risk ratio 1.13 (0.80–1.60); unadjusted two-proportion z-test p = 0.477.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Drains and the control. The interval gives the range of effects that remain compatible with the data.

90-day Mortality Rate

• 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:
  • Drains: 0.0% (0/174) versus 1.2% (2/170) on control; risk difference -1.2 percentage points (95% CI -2.8 to 0.4); unadjusted two-proportion z-test p = 0.151.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Drains and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes broaden the focus beyond the primary Grade II or higher complication endpoint. They include a more severe complication threshold and mortality, as well as measures of serious adverse events, complication frequency and severity, specific complications, hospital stay, and cost. Results are available for some of these outcomes, while the registry record does not report results for every listed measure.

The recalculated Grade III or higher complication comparison has a risk difference of 0.034, with a 95% confidence interval from -0.060 to 0.129 and p = 0.477. The 90-day mortality comparison has a risk difference of -0.012, with a 95% confidence interval from -0.028 to 0.004 and p = 0.151. Both intervals include zero, so these posted comparisons also leave uncertainty about the direction and size of a difference. They do not overturn or independently confirm the primary result.

Secondary endpoints can help describe whether the overall clinical pattern is consistent across different aspects of outcome, but they should be interpreted in the context of the primary endpoint and the number of outcomes examined. When many outcomes are tested, the chance of finding at least one apparently unusual result can increase. The record does not report a multiplicity adjustment or a hierarchy for testing secondary outcomes. Unadjusted secondary results therefore carry less evidential weight than a prespecified primary analysis and should be treated as exploratory unless the registry record establishes otherwise.

The outcomes also measure different constructs and may differ in event frequency, follow-up window, and precision. Counts for complications, mortality, and adverse events are not interchangeable, and a result for one does not answer all questions about another. Missing results for listed outcomes limit the ability to assess the complete pattern. These secondary data are best read as additional descriptive evidence, not as a substitute for the primary comparison or as proof of a broad effect across all outcomes.

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

• 60-day ≥ Grade III Complication Rate
• Serious Adverse Event (SAE) Rate
• Median Complication Severity Grade
• 60-day Frequency of Complications
• 90-day Mortality Rate
• Rate of Specific Complications
• Length of Stay for the Index Admission
• Crude Cost

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary at the participant level: whether a participant experienced at least one Grade II or higher complication within 60 days. A comparison of binary outcomes can be expressed as a difference in risks, a risk ratio, or an odds ratio. These are different scales for describing the same group comparison and should not be treated as interchangeable numerical quantities.

What does the risk difference describe?

The risk difference is the risk in the Drains group minus the risk in the No Drains group. For the primary outcome, the recalculated estimate is 0.013. A value above zero indicates a higher observed risk in the Drains group on this scale; a value below zero indicates a lower observed risk in that group. The estimate is not a statement about the cause of an individual participant’s complication. It summarizes the contrast between the posted group results.

The confidence interval for this difference runs from -0.091 to 0.118. It represents the range of values compatible with the data under the method used to calculate the interval. Since it crosses zero, the data do not clearly distinguish a positive difference from a negative one. The width also signals that the estimate is not highly precise. The interval is not a guarantee that the true difference lies within it, and it does not account for possible problems that are not reflected in the calculation, such as unreported missingness or outcome misclassification.

What do the risk ratio and odds ratio add?

The posted recalculation gives a risk ratio of 1.031, with an interval from 0.808 to 1.315, and an odds ratio of 1.056, with an interval from 0.689 to 1.618. A risk ratio compares the risks directly, while an odds ratio compares odds. Values of 1 correspond to no relative difference on the relevant scale. Both intervals include 1, consistent with the risk-difference interval including zero: these posted estimates do not clearly establish a difference between arms.

Risk differences are often easier to relate to absolute changes in event frequency. Relative measures can make the scale of a comparison clearer in some settings, but may appear more or less dramatic depending on the baseline risk. No one measure should be read in isolation. All are based on the same posted group outcomes and do not provide independent confirmations of an effect.

How should the p-value be read?

The registry reports a chi-squared analysis and p = 0.804. The unadjusted recalculation also gives p = 0.804. A p-value describes how unusual a test statistic at least as extreme as the observed one would be under the null model used by the test. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of a difference. A relatively large p-value does not prove that the groups are equivalent; the confidence interval is important for judging which differences remain compatible with the data.

The registry’s chi-squared result is the sponsor’s reported analysis. The additional risk difference, risk ratio, odds ratio, confidence intervals, and unadjusted p-value are simple unadjusted recalculations from the posted summary statistics. They do not adjust for covariates, centers, or other factors. The registry record does not report whether the sponsor used any additional adjustment for the primary outcome.

Why do confidence intervals matter alongside testing?

A significance test reduces a comparison to a measure of compatibility with a null model. A confidence interval shows a range of effect sizes compatible with the observed data under the calculation method. It therefore helps distinguish a tightly estimated near-zero result from an uncertain result that happens to have a nonsignificant test. In this trial, the primary interval includes zero and extends in both directions, so the uncertainty is central to interpretation.

The recalculated intervals are based on posted summary counts and are unadjusted. They do not incorporate any unreported features of the trial analysis, and they should not be mistaken for a reconstruction of a more complex sponsor model. The record does not report a prespecified statistical analysis plan, any covariate adjustment, or an approach for multiple comparisons. Those matters are relevant when assessing how much emphasis to place on a single unadjusted estimate among numerous outcomes.

What is the role of outcome grading?

The primary outcome groups complications by a severity threshold and a follow-up window. Grade II or higher includes the grades at or above the stated threshold; the secondary Grade III or higher endpoint applies a more severe threshold. Grading makes severity part of the endpoint definition, but consistent application depends on standardized assessment. The registry describes the grading framework but does not report further details about adjudication or assessor procedures. Since masking was listed as none, the record indicates that masking was not used, but does not give enough information to assess how this might have affected outcome assessment.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the group difference. For the primary outcome, the recalculated risk difference is 0.013 and its 95% confidence interval runs from -0.091 to 0.118. That interval crosses zero and spans values on either side of it. The data therefore do not pin down the direction of the difference with precision, and they remain compatible with a range of differences. The estimate near zero should not be separated from this uncertainty.

The relative-scale estimates tell a similar uncertainty story. The risk ratio is 1.031, with an interval from 0.808 to 1.315; the odds ratio is 1.056, with an interval from 0.689 to 1.618. Each interval includes the no-difference value for its scale. These intervals do not prove that there is no effect; they indicate that the posted data are compatible with values on both sides of no difference.

A confidence interval is a statistical range produced by a method with a stated long-run coverage property under its assumptions. It is not a range containing a known fixed proportion of individual participant outcomes, nor does it account for every potential source of uncertainty. In particular, the recalculated intervals are based on the posted summary counts and are unadjusted. The registry record does not report enough about missing outcome data, population definitions, or any adjusted sponsor model to quantify how those features might affect precision.

The secondary Grade III or higher complication result and the mortality result also have intervals that include no difference. The mortality estimate is based on sparse posted event counts, so its numerical difference is especially sensitive to the few events observed. Across outcomes, nonsignificant tests should not be treated as evidence of exact equality. Precision is best judged from the estimate and interval together, with attention to the endpoint, analysis population, and limitations of the registry reporting.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. For the primary outcome, the figures are participants per arm. Using 100% of the observed effect, the illustration gives 21,909 participants per arm for 80% power and 29,330 participants per arm for 90% power. Planning for 75% of the observed effect gives 38,913 participants per arm for 80% power and 52,093 participants per arm for 90% power. Planning for 50% of the observed effect gives 87,470 participants per arm for 80% power and 117,097 participants per arm for 90% power.

The calculations use a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. For the binary outcomes, the figures refer to participants per arm; time-to-event planning figures, if present, would instead refer to total events. The planning assumptions for the trial’s own design, including any original target or rationale, are not reported in the registry record.

The 80% power column represents the planning size associated with an 80% chance of detecting the specified effect under the stated assumptions if that effect were present. The 90% column represents the corresponding planning size for 90% power. These are design concepts, not probabilities that the posted trial result is correct. Smaller effects require more participants to detect under the same assumptions, which is why the illustrations increase as the assumed effect fraction decreases. This is not observed power.

The curve should be read as a planning relationship between the effect size targeted and the participant requirement under the stated assumptions. It is not a projection of what the completed trial would have found at other sample sizes, nor evidence about the original protocol’s calculations.

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 = 0.424; treatment proportion p₁ = 0.437; average p̄ = 0.430.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7002 = 1.3723.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7001 = 0.5892.
4. n = (1.3723 + 0.5892)² / (0.0133)² = 21,908.9, rounded up to 21,909 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 <- 0.423529411764706                          # control proportion
p1 <- 0.436781609195402                          # 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(1441492)
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 = 21,909 (80% power), 29,330 (90% power)
 75% of observed effect: n per arm = 38,913 (80% power), 52,093 (90% power)
 50% of observed effect: n per arm = 87,470 (80% power), 117,097 (90% power)
power.prop.test: 21908.9 
Simulated power at n = 21,909 per arm: 0.797 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a chi-squared analysis for the primary comparison with p = 0.804. A simple unadjusted recalculation from the posted counts also gives p = 0.804. The sponsor’s reported analysis therefore agrees with the recalculated test result at the precision recorded.

The recalculation additionally expresses the group comparison as a risk difference of 0.013, with a 95% confidence interval from -0.091 to 0.118, alongside relative measures. These are unadjusted calculations from the posted summary statistics. They are useful for describing the magnitude and uncertainty of the observed contrast, but they are not a replacement for the sponsor’s own analysis or an attempt to reconstruct any unreported adjustment or modeling choices. The sponsor’s own analysis takes precedence if a discrepancy exists; the discrepancy flag is false for this comparison.

The registry record does not report a detailed statistical analysis plan, covariate adjustments, or an explanation of analysis-population decisions. Agreement in the p-value does not resolve those reporting gaps. Nor does the reported p-value establish equivalence or noninferiority; those conclusions require an appropriate prespecified framework, and the registry record does not report such a margin or criterion.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures, while the primary endpoint is the 60-day Grade II or higher complication rate. Testing several outcomes can increase the possibility that at least one result appears statistically notable by chance. A multiplicity strategy can address this through prespecified ordering, adjusted significance thresholds, or other methods. The registry record does not report whether such a strategy was planned or used, and no adjustment should be assumed for the posted secondary comparisons.

The record lists one reported analysis, a chi-squared test for the primary outcome. It does not report a full statistical analysis plan, the intended analysis population, or whether the primary analysis was by randomized assignment. It also does not describe how outcome data were handled when unavailable, how protocol deviations were treated, or whether any sensitivity analyses were conducted. These details are important because choices about analysis populations and missing observations can affect the estimated comparison.

The enrollment field is 399, whereas the posted primary outcome denominators are 170 and 174. The registry record does not explain the relationship between these figures. The observed counts should therefore be described using their posted denominators without assuming a reason for the difference or inferring how many participants were excluded, lost to follow-up, or otherwise absent from an analysis.

Missing data can create bias if the likelihood of an outcome being unobserved is related to the outcome itself or differs between randomized groups. General statistical approaches include describing missingness, using justified imputation or weighting methods, and conducting sensitivity analyses under alternative assumptions. Those are general methodological options; the registry record does not say whether any were applied in this trial. Without the relevant reporting, the impact of missingness cannot be quantified from the posted summary counts.

The record also does not report allocation concealment, a noninferiority margin, interim analyses, or the protocol’s original sample-size justification. These omissions do not establish that such procedures were absent; they mean they are not reported in the registry record. The distinction is important when interpreting the scope and strength of the evidence.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: grade 3 intra-abdominal infection and pancreatic leak/fistula (1.2%).

The adverse-event figures list serious adverse events affecting 2 participants in the No Drains arm and 0 in the Drains arm. The corresponding numbers at risk are 170 and 174. The record also lists other adverse events affecting 99 participants in the No Drains arm and 130 in the Drains arm, with the same arm-specific numbers at risk. These are posted counts, not adjusted comparisons, and the registry record does not provide a statistical analysis for these adverse-event figures.

The record lists “Grade 3 intra-abdominal infection and pancreatic leak/fistula” among the top serious terms at 1.2%. It does not provide enough context to attribute that term to a specific arm from the posted fact alone. The deaths fields in the adverse-event record are null; the separate 90-day mortality outcome reports 2 in the No Drains arm and 0 in the Drains arm.

Adverse-event counts describe events recorded in the trial, but they do not establish that the assigned strategy caused them. The record does not report the serious adverse event definition, event-level details, relatedness assessments, or a comparative safety analysis for these figures. The counts should therefore be read descriptively and alongside the stated denominators, without treating the difference in counts as a causal estimate.

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

The primary comparison shows similar observed counts of participants with Grade II or higher complications across the randomized arms, with a recalculated risk difference of 0.013. However, the 95% confidence interval from -0.091 to 0.118 includes zero and spans potentially meaningful differences in either direction. The result is therefore not a precise demonstration that the groups are the same.

The registry’s stated hypothesis concerned whether omitting routine drainage would not increase complication severity or frequency within 60 days. A formal noninferiority conclusion requires a prespecified margin defining how much increase would still be considered acceptable, along with a suitable analysis and interpretation against that margin. The registry record does not report a margin or establish that the analysis was a formal noninferiority test. The posted nonsignificant p-value cannot, on its own, establish noninferiority or equivalence.

Likewise, the result does not show that one approach is superior. The primary p-value is 0.804, and the confidence interval crosses zero. A nonsignificant result is not proof of no effect; it indicates that the observed data did not provide clear evidence against the no-difference model used for the test. The uncertainty interval conveys the range of contrasts that remains compatible with the data under the recalculation method.

The trial’s randomized design is relevant to interpreting the comparison, but important implementation and analysis details are not reported in the registry record. These include the relationship between enrollment and outcome denominators, the handling of missing outcomes, and the definition of the analysis population. The posted results also do not cover all listed secondary outcomes. Consequently, conclusions should be limited to the reported comparisons and their stated follow-up periods.

These findings are statistical descriptions of the registry results, not medical advice. They do not settle individual treatment choices, establish that complications are prevented, or resolve outcomes and populations not represented in the posted data. The appropriate conclusion is that the primary estimate is close to zero but uncertain, and that the registry record does not support a definitive claim of equivalence, noninferiority, or superiority.

18. Why This Trial Matters Statistically

This trial addresses a design question that is especially important in surgical research: how to compare two perioperative strategies when the outcome is a complication occurring after an operation. Random assignment provides a structured basis for comparing the groups, and a participant-level complication endpoint gives the result a direct clinical interpretation. The defined follow-up window and grading threshold make the primary outcome more specific than an unrestricted count of postoperative events.

Statistically, the trial also illustrates why a nonsignificant test should not be mistaken for proof that two strategies are equivalent. The primary p-value is 0.804, but the confidence interval for the recalculated risk difference extends in both directions. The estimate and its precision answer different questions: the estimate describes the observed contrast, while the interval shows how uncertain that contrast remains.

The registry hypothesis is framed around not increasing complication severity or frequency, but the record does not report a noninferiority margin. This matters because a formal noninferiority question cannot be answered merely by observing that a conventional test is nonsignificant. Prespecification and the margin determine what degree of difference would count as acceptable under such a design.

The outcome denominators also deserve attention. The enrollment field and posted primary denominators do not match, and the registry record does not explain why. This is a reminder that an analysis needs more than outcome counts: readers need to know who was analyzed, how missing outcomes were handled, and whether assignment was preserved in the analysis. The trial’s results are useful for understanding the posted comparison, while the unreported details constrain stronger conclusions.

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.

Several limitations specific to the registry record affect interpretation. Although the study is described as randomized, the randomization method and allocation concealment are not reported. Masking is listed as none, and the record does not provide details about outcome assessor procedures or adjudication. The primary endpoint uses complication severity grading, so information about consistent assessment would help readers judge the possibility of measurement differences.

The enrollment field records 399, while the primary outcome results use denominators of 170 and 174. The registry record does not explain this difference or specify the analysis population. It also does not report the extent or handling of missing outcomes, protocol deviations, crossovers, or adherence to assigned strategies. No conclusion about the reason for the denominator difference should be drawn from the counts alone.

The primary result is accompanied by a chi-squared p-value, but a full statistical analysis plan is not reported. The record does not report covariate or center adjustment, a noninferiority margin, multiplicity handling, interim analyses, or the trial’s original sample-size justification. These omissions limit assessment of whether the reported analysis matches a prespecified plan and whether secondary comparisons were exploratory.

Not every listed secondary outcome has posted results in the registry record in the registry record. The available secondary estimates also have uncertainty and should not be used to fill gaps in outcomes that are not reported. The adverse-event counts are descriptive, and further information about event definitions and relatedness is not reported. These limitations do not establish that a procedure was not performed or that data were unavailable to investigators; they identify what the registry record does not report.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Pancreas Resection With and Without Drains — NCT01441492.
• Registry record last updated 2020-08-31; status last verified 2020-08.
• Results first posted 2020-08-31.
• 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

NCT01441492 is a completed, randomized, prospective multicenter, parallel-group trial of pancreas resection with and without routine intraperitoneal drainage. The study lists no masking and an enrollment of 399. Its primary outcome is participants with Grade II or higher complications within 60 days of surgery.

The posted primary counts are 72 of 170 in the No Drains arm and 76 of 174 in the Drains arm. The registry reports a chi-squared p-value of 0.804. The unadjusted recalculation gives a risk difference of 0.013, with a 95% confidence interval from -0.091 to 0.118. This estimate is uncertain and does not establish equivalence, noninferiority, or superiority.

The registry record does not report a noninferiority margin, the original sample-size justification, or important details about missing data and analysis populations. Secondary results are posted for some outcomes, while results for every listed measure are not reported in the registry record.