Comparison Study of Surgical Staplers for the Treatment of Hemorrhoids: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison Study of Surgical Staplers for the Treatment of Hemorrhoids (NCT01306877), a randomized na study. The primary outcome is Intraoperative Bleeding.

2. Clinical Question

3. Trial Design

This was a prospective, randomized, single-blind, parallel-group controlled trial comparing two stapling devices in hemorrhoidopexy. The devices were the EEA Hemorrhoid and Prolapse Stapling Set and the Endosurgery Proximate PPH03 Stapling Set. The registry lists the condition as hemorrhoids and enrollment as 149. The recorded start was 2011-01, primary completion was 2012-08, and status is completed. The registry identifies the sponsor as Medtronic - MITG.

Randomized allocation supports a design in which assignment to the device groups is intended to reduce systematic differences between groups. Randomization does not guarantee that groups will be identical in every feature, and the registry record does not provide the allocation sequence or details of how assignments were concealed. Single masking is recorded, but the identity of the masked people is not reported in the registry record. The record describes a parallel design, meaning the two device groups are compared as separate arms rather than as a crossover comparison.

The primary outcome was intraoperative bleeding, defined as the number of subjects requiring intervention to stop bleeding during surgery. Its timeframe is Day 0, at the time of surgery. The registry says the primary analysis used a per-protocol population, with misrandomized subjects excluded, and notes that this population differs from participant flow. The number randomized to each arm and the reasons for exclusions from the primary analysis are not detailed in the record excerpt.

Secondary outcomes named in the record include postoperative pain measured by PI-NIRS and analgesic intake, general health score, staple-line location, length of stay, and operating-room time. Numerical secondary results are posted for staple-line location, length of stay, and operating-room time. Numerical results for the other named secondary outcomes are not reported in the registry record. The original sample-size assumptions, analysis plan, and any interim analyses are not reported in the registry record.

4. Participant Flow and Accounting

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

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 Intraoperative Bleeding, measured over Day 0 - time of surgery.

The primary endpoint counts participants who required an intervention to stop bleeding during the operation. It is a binary participant-level outcome: each participant either met the endpoint definition or did not. The registry gives the assessment timeframe as Day 0, at the time of surgery, and describes the outcome as a number of subjects rather than a measure of blood loss, bleeding duration, or severity. Those other features are not reported in the registry record.

This endpoint is relevant to the stated trial question because the registry summary says the study sought to demonstrate non-inferiority of the EEA device to the competitor based on the primary endpoint. A comparison of the proportions of participants meeting the endpoint can describe how frequently intervention for intraoperative bleeding occurred in the two groups. The posted endpoint counts are 32 of 76 in the EEA group and 50 of 68 in the PPH03 group. They should be read with attention to the analysis population: the registry specifies a per-protocol analysis and says misrandomized subjects were excluded, so these denominators need not match participant-flow counts.

For a non-inferiority question, the observed difference is not interpreted in isolation. The prespecified margin and decision rule determine how much difference would be acceptable for the non-inferiority claim. Neither the margin nor the full rule is reported in the registry record. The endpoint therefore describes the recorded event counts, while the registry’s reported analysis and its stated inferential framework need to be considered separately.

7. Results Posted in the Registry

• Endosurgery Proximate PPH03 Stapling Set: 73.5% (50/68) versus 42.1% (32/76) on control; risk difference 31.4 percentage points (95% CI 16.2 to 46.7), risk ratio 1.75 (1.29–2.36); unadjusted two-proportion z-test p = <0.001.

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.

Location of the Staple Line

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Endosurgery Proximate PPH03 Stapling Set: mean 24.00 versus 25.94 on control; difference -1.94 (95% CI -4.61 to 0.73), standardized effect d = -0.23; z-test p = 0.155.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Endosurgery Proximate PPH03 Stapling Set and the control. The interval gives the range of effects that remain compatible with the data.

Length of Stay

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Endosurgery Proximate PPH03 Stapling Set: mean 4.37 versus 4.16 on control; difference 0.21 (95% CI -1.85 to 2.27), standardized effect d = 0.03; z-test p = 0.842.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Endosurgery Proximate PPH03 Stapling Set and the control. The interval gives the range of effects that remain compatible with the data.

Operative Room (OR) Time

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Endosurgery Proximate PPH03 Stapling Set: mean 25.60 versus 25.40 on control; difference 0.20 (95% CI -4.25 to 4.65), standardized effect d = 0.01; z-test p = 0.930.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Endosurgery Proximate PPH03 Stapling Set and the control. The interval gives the range of effects that remain compatible with the data.

The posted numerical secondary findings cover staple-line location, length of stay, and operating-room time. Their recalculated mean differences are small relative to the ranges of values compatible with the data, and each interval includes zero. The registry’s own rank-based analyses also report p-values that do not indicate a clear separation under those tests. The two approaches are not identical: the recalculations compare means, while the reported tests use ranks. Accordingly, the overall secondary pattern is one of uncertain differences rather than a consistent, precisely estimated shift across these measures.

The registry also names postoperative pain measured by PI-NIRS, postoperative analgesic intake, and overall quality of life measured by general health score. Numerical results for these named outcomes are not reported in the registry record. Their absence means the overall secondary-outcome picture is incomplete; it does not establish that the outcomes were not measured. The registry lists six secondary outcomes, while numerical results are posted for three of them.

These outcomes address different aspects of the procedure and do not directly substitute for the primary intraoperative bleeding endpoint. The primary comparison concerns whether participants required an intervention to stop bleeding during surgery. Secondary measures address pain, quality of life, staple-line location, time in hospital, and operating-room duration. They can add context, but they do not alter the definition of the primary endpoint or fill in the unreported non-inferiority margin.

Secondary findings generally carry less inferential weight when many outcomes are examined without a reported adjustment for multiple comparisons. Repeated testing can increase the chance of at least one apparently notable result arising by chance. The multiplicity plan is not reported in the registry record. The unadjusted recalculations should therefore be treated as exploratory descriptions, not as a set of independent confirmatory conclusions. Because several named outcomes lack posted numerical results, claims about a broad pattern across pain, quality of life, and procedural outcomes would go beyond the registry record.

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

• Post Operative Pain - (PI-NIRS)
• Post-Operative Pain (Analgesic Intake)
• Overall Quality of Life - General Health Score
• Location of the Staple Line
• Length of Stay
• Operative Room (OR) Time

9. Statistical Interpretation

10. Statistical Methods Explained

A randomized parallel-group trial compares outcomes between groups assigned to different interventions. Random allocation is intended to make the groups comparable on average with respect to measured and unmeasured characteristics, although it does not ensure identical groups in any particular trial. The registry records randomized allocation and a single-blind, parallel design. It does not report the allocation-generation or concealment procedures, or who was masked. Those omissions limit what can be assessed about implementation from the registry record alone.

What does a binary endpoint comparison describe?

Intraoperative bleeding is recorded as the number of participants who required an intervention to stop bleeding. A risk is the proportion of participants in an arm who experienced the defined event. A risk difference subtracts one arm’s risk from the other arm’s risk. Its sign depends on the subtraction order, so comparisons must be read with the group order stated. The recalculation uses PPH03 minus EEA and gives a positive risk difference of 0.314. The registry’s reported estimate is -0.314, which follows the reverse direction, EEA minus PPH03. Opposite signs can therefore describe the same contrast when group order is reversed.

The registry reports a Chi-squared analysis for the primary outcome and classifies the analysis as non-inferiority or equivalence. A Chi-squared test is a general method for testing an association between categorical group and outcome information. The reported p-value describes compatibility of the observed data with the test’s null hypothesis under the method used; it is not itself an estimate of the size or practical importance of the difference. The registry does not report the full test specification or its non-inferiority margin. A non-inferiority assessment generally depends on comparing an interval estimate with a prespecified margin, so knowing the margin and decision rule matters for interpreting the stated aim.

Why are the continuous outcomes assessed differently?

Staple-line location, length of stay, and operating-room time are continuous measures. The posted arm summaries give means and standard deviations. A mean difference compares the average values between groups, with the direction again depending on the subtraction order. The recalculated comparisons use PPH03 minus EEA. Their confidence intervals describe a range of effect values compatible with the data and the calculation’s assumptions. The registry’s own analyses for these outcomes use Wilcoxon (Mann-Whitney) tests, a rank-based approach that compares the distributions of observations rather than directly testing the difference between the reported means. A rank-based p-value is not an estimate of the mean difference and does not provide a confidence interval for that difference.

The recalculated continuous comparisons are simple, unadjusted calculations from the posted summary statistics. They do not replace the registry-reported tests. A test based on individual observations can use information that is not recoverable from means, standard deviations, and sample counts alone, including the detailed shape and ordering of the observed data. The registry does not post the individual observations or enough detail to reproduce its rank-based tests. Thus the recalculated mean differences and the reported rank-test p-values answer related but not identical statistical questions.

What does a confidence interval add?

A confidence interval presents an estimate together with a range that reflects sampling uncertainty under the method used. A narrow interval indicates greater precision for that particular estimate; a wide interval indicates less precision. If a difference interval includes zero, the data are compatible with both directions of difference as well as little or no difference under the calculation. That does not prove the groups are identical. For a non-inferiority question, the interval must be assessed against the prespecified margin, which is not reported in the registry record. A p-value and a confidence interval are related summaries, but they are not interchangeable: the interval also displays the range of effect sizes compatible with the analysis.

Why can over-dispersion matter?

Over-dispersion is a general statistical concern when observed variability is greater than a model expects. If a model assumes less variability than the data contain, its uncertainty estimates can be too small and its tests can appear more decisive than warranted. This trial’s posted primary outcome is a binary participant count, and the continuous secondary summaries include standard deviations. The record does not identify an over-dispersion model or report that over-dispersion was assessed. It would therefore be inappropriate to claim that it affected these results. The concept is relevant generally when choosing or checking a model, but the registry record does not provide the information needed to assess it for this analysis.

What is the role of the analysis population?

The primary endpoint description states that the analysis used the per-protocol analysis set and excluded subjects who were misrandomized. Per-protocol analyses include participants according to adherence or protocol-defined eligibility rules; the exact rules beyond the misrandomized exclusion are not reported in the registry record. The record explicitly says the primary analysis population differs from participant flow. This distinction matters because a randomized comparison and a per-protocol comparison can involve different participants and different denominators. The record does not describe the handling of missing endpoint values or the secondary-outcome analysis populations.

Why distinguish recalculation from reported analysis?

A recalculation from posted summary statistics can help readers understand direction, scale, and approximate precision. It remains an unadjusted calculation and may use a different estimand or method from the registered analysis. Here, the primary recalculation uses the displayed counts and reverses the subtraction order relative to the registry’s reported risk difference. For secondary outcomes, the recalculated mean comparisons differ in method from the reported Wilcoxon (Mann-Whitney) tests. The estimates should therefore be labeled by their method and not merged into a single purported analysis. The record does not report enough information to reconstruct all prespecified analyses or determine whether any additional adjustments were made.

11. Confidence Intervals and Precision

The recalculated primary risk difference is 0.314 for PPH03 minus EEA, with a 95% confidence interval from 0.162 to 0.467. This interval is entirely positive for that comparison direction. The registry’s analysis reports EEA minus PPH03 as -0.314 and gives an upper 95% confidence limit of -0.18; its lower confidence limit is not reported in the registry record. The registry estimate and recalculation use reverse group order, so their signs should not be compared without accounting for that orientation.

The continuous-outcome confidence intervals are broader in relation to their estimates and include zero: -4.613 to 0.733 mm for the mean difference in staple-line location, -1.854 to 2.274 hours for length of stay, and -4.248 to 4.648 minutes for operating-room time. These intervals indicate that the recalculated mean differences are not estimated with enough precision to rule out effects on either side of zero. They do not demonstrate equivalence, and they do not supply confidence intervals for the registry’s rank-based tests.

A confidence interval is a measure of precision under the analysis used, not a guarantee that the true effect lies within the displayed range. Its interpretation also depends on the outcome definition, group order, population, and statistical method. The primary analysis population is per protocol, and its denominators differ from participant flow according to the registry. The non-inferiority margin is not reported in the registry record, so the primary interval cannot be assessed against that margin from the posted details. Secondary confidence intervals are recalculated and unadjusted; multiplicity handling 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 planning illustrations give participants per arm for 80% power and participants per arm for 90% power for the continuous outcomes, as well as the binary primary outcome. They are not totals across both arms. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect. The trial’s original design assumptions are not reported in the registry record. These calculations are planning illustrations based on observed effects, not observed power.

The 80% power column represents the number of participants per arm a hypothetical study would plan for to have an 80% chance of detecting the specified effect under the stated assumptions. The 90% column expresses the corresponding planning target for a 90% chance. Power is a design property under assumed conditions, not a measure of how likely the observed finding is to be true. The values are conditional on the chosen effect size and assumptions, and do not establish what the original trial was designed to detect.

Scenarios labeled 100% of the observed effect use the full observed effect as the planning target; scenarios labeled 75% or 50% use smaller fractions. A smaller effect is harder to distinguish from random variation and therefore requires more participants for the same target power under otherwise unchanged assumptions. The planning figures can be very large when the observed effect is small relative to variability, as in some continuous outcomes. For the binary endpoint, the illustrations use participants per arm rather than total events. No time-to-event outcome is included in these posted secondary results; if a time-to-event planning illustration were presented, its figures would refer to total events, but that distinction does not change the meaning of the participant-per-arm figures for these outcomes.

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 = 0.421; treatment proportion p₁ = 0.735; average p̄ = 0.578.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6984 = 1.3689.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6621 = 0.5573.
4. n = (1.3689 + 0.5573)² / (0.3142)² = 37.6, rounded up to 38 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 <- 0.421052631578947                          # control proportion
p1 <- 0.735294117647059                          # 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(1306877)
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 = 38 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 70 (80% power), 92 (90% power)
 50% of observed effect: n per arm = 158 (80% power), 211 (90% power)
power.prop.test: 37.6 
Simulated power at n = 38 per arm: 0.807 (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-reported primary analysis is a Chi-squared analysis labeled as non-inferiority or equivalence. It reports an EEA-minus-PPH03 risk difference of -0.314, an upper 95% confidence limit of -0.18, and p < 0.001. The lower confidence limit is not reported in the registry record. The simple recalculation from the posted counts uses PPH03 minus EEA and gives a risk difference of 0.314, a 95% confidence interval from 0.162 to 0.467, and p <0.001. The reversed sign reflects the reversed order of subtraction, rather than a different direction of the underlying group contrast.

The recalculation is unadjusted and derived from posted summary counts. It is useful for making the comparison’s direction and scale explicit, but it does not replace the registry-reported analysis. The registry’s reported estimate is rounded differently and is associated with the stated Chi-squared method and non-inferiority/equivalence analysis type. The record does not report the margin or the complete decision rule, so the numerical agreement in direction cannot independently establish how the formal non-inferiority criterion was applied.

For the secondary outcomes, the registry reports Wilcoxon (Mann-Whitney) p-values, while the recalculated comparisons are mean differences with intervals from summary statistics. These are methodologically distinct summaries. The registry does not provide effect estimates or confidence intervals for its rank-based analyses. The recalculations should be read as supplementary descriptive analyses, not as corrections to the registry’s reported tests.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the statistical plan adjusted for testing multiple outcomes, how any adjustment was performed, or whether a hierarchy of outcomes was prespecified. This is important because the trial includes a primary endpoint and several secondary outcomes. When multiple comparisons are made, the chance of obtaining at least one apparently unusual result by chance can increase. An adjustment or prespecified testing hierarchy can address that concern, but neither is described in the registry record. The posted recalculated p-values are unadjusted and should be interpreted accordingly.

Missing-data handling is also not reported in the registry record. The record does not say how participants with missing primary or secondary endpoint values were treated, whether missingness was assessed, or whether any sensitivity analysis was conducted. The listed arm denominators for the primary analysis are 76 and 68, while the secondary summaries use different denominators. These are outcome-specific posted analysis counts; the record does not explain all reasons for differences between them. No totals should be inferred from those separate outcome records.

The primary endpoint description identifies a per-protocol analysis set and says misrandomized subjects were excluded. It also states that the population analyzed differs from participant flow. The details of any other per-protocol criteria are not reported in the registry record. The record does not say whether an intention-to-treat analysis was conducted, whether the primary conclusion was assessed in more than one population, or what analysis populations were used for each secondary endpoint.

These omissions do not establish that the trial lacked a multiplicity strategy, missing-data procedures, or additional analyses; they mean those details are not reported in the registry record. They limit the ability to evaluate whether the displayed results follow a prespecified analysis plan and whether exclusions or missing observations could affect interpretation. This matters particularly for a non-inferiority objective, for which analysis populations and sensitivity to exclusions can be relevant to the 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: proctalgia (1.5%), tooth abscess (1.5%), procedural pain (1.5%), faecoloma (1.2%), urinary retention (1.2%).

The adverse-event record lists serious events for the EEA group as 2 affected among 81 at risk, and for the PPH03 group as 3 affected among 68 at risk. These figures describe the registry’s serious-event counts and the corresponding at-risk denominators; they are not the primary efficacy endpoint. The record does not provide a definition of serious adverse events or detailed information about event timing, relatedness to the device, or how events were adjudicated. Death counts are not reported in the registry record.

The registry also gives other-event counts of 65 among 81 at risk for EEA and 40 among 68 at risk for PPH03. Those counts should not be combined with the serious-event counts: the categories are recorded separately, and the record does not explain whether participants could contribute to more than one event category. The listed serious-event terms include Proctalgia, Tooth Abscess, Procedural Pain, Faecoloma, and Urinary Retention, each with a percentage shown in the adverse-event record. The registry information presented does not attribute each listed term to a particular device group.

These counts are descriptive safety information. They do not by themselves establish whether a device caused an event or whether the groups differ reliably in safety. The record does not report a comparative safety analysis, uncertainty intervals, or detailed event-level data. A cautious reading is therefore limited to the reported affected counts, denominators, and listed terms.

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

The posted primary outcome shows more participants meeting the intraoperative bleeding endpoint in the PPH03 group than in the EEA group, using the recorded analysis counts. The simple unadjusted risk-difference recalculation makes that direction explicit as PPH03 minus EEA. The registry’s reported analysis presents the same contrast in reverse order. This describes the posted endpoint data; it is not, by itself, a complete assessment of the study’s non-inferiority claim.

The registry states that the study aimed to demonstrate non-inferiority of the EEA device based on the primary endpoint and classifies its analysis as non-inferiority or equivalence. The non-inferiority margin and full decision rule are not reported in the registry record. Without those elements, readers cannot independently determine from the registry information whether the prespecified criterion was met. The reported p-value should not be treated as a stand-alone measure of clinical importance or as a replacement for the margin-based assessment.

The secondary results do not establish that the devices are equivalent on staple-line location, length of stay, or operating-room time. Their recalculated confidence intervals include zero, which leaves uncertainty about the direction and size of the mean differences. The registry’s rank-based p-values are not confidence intervals for those mean differences. Numerical results for the named pain, analgesic intake, and general health outcomes are not reported in the registry record, so no conclusion about those outcomes follows from the numerical secondary results that are posted.

The findings also do not establish that either device is safer overall. The serious-event counts are descriptive, and the registry record does not supply the detail needed to assess causation or a comparative safety effect. More generally, a result in one trial applies to its studied setting and analysis population; information about eligibility, clinical setting, and longer-term follow-up is not reported in the registry record. The appropriate interpretation is therefore specific: the registry records a primary event-count contrast and selected secondary summaries, alongside important unreported design and analysis details.

18. Why This Trial Matters Statistically

This trial illustrates why direction of comparison must be made explicit. The registry-reported primary risk difference is EEA minus PPH03, whereas the simple recalculation is PPH03 minus EEA. The opposite signs do not imply contradictory patterns; they reflect a reversed subtraction order. Clear orientation is essential when interpreting an effect estimate, confidence interval, or statement about which group had the higher recorded event proportion.

It also illustrates the distinction between an outcome count and the analysis population behind that count. The primary endpoint is reported for a per-protocol set, with misrandomized subjects excluded, and the registry says this population differs from participant flow. A reader who assumes that every denominator refers to all randomized participants could misunderstand the scope of the estimate. Outcome-specific counts and denominators need to be interpreted with the stated population.

The non-inferiority objective makes the prespecified margin particularly important. A non-inferiority claim is not established merely by observing a difference or reading a p-value; the comparison depends on a margin and a decision rule. Those details are not reported in the registry record. This is a useful statistical distinction between the trial’s stated question and the information available to independently evaluate that question.

Finally, the secondary outcomes show why different methods and multiplicity matter. The registry reports rank-based tests, while recalculated mean differences use summary statistics. Those summaries answer related but distinct questions. Multiple secondary outcomes also raise the question of adjustment, which is not reported. The record is therefore a practical example of reading estimates, analysis labels, populations, and missing methodological details together rather than relying on one number.

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 trial-specific limitations arise from the registry information available. First, the primary endpoint analysis is per protocol and excludes misrandomized subjects. The registry explicitly says that its analysis population differs from participant flow, but does not provide the full exclusion accounting or all per-protocol criteria. This makes it difficult to reconcile the primary analysis denominator with the overall trial flow from the record alone.

Second, the trial is described as non-inferiority, but the margin and complete decision rule are not reported in the registry record. The reported primary analysis includes an upper confidence limit but not a lower limit. These omissions make independent review of the non-inferiority criterion incomplete. The registry’s reported analysis remains the relevant reported result; the recalculation from counts does not reconstruct the full protocol analysis.

Third, the registry’s numerical secondary findings cover only some of the named secondary outcomes. Results for postoperative pain, analgesic intake, and general health score are not reported in the registry record. For the outcomes with numerical values, the registry uses Wilcoxon (Mann-Whitney) tests, while the recalculated summaries compare means. No individual-level data are posted to assess the distributions or reproduce the registry tests.

Fourth, allocation concealment, the identity of the masked participants, missing-data methods, multiplicity handling, and the original sample-size rationale are not reported in the registry record. These gaps do not prove that the procedures were absent, but they constrain assessment of trial conduct and analysis. The adverse-event information is also limited: event definitions, attribution, detailed event-level context, and death counts are not reported. Together, these limitations call for a restrained interpretation of the posted comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparison Study of Surgical Staplers for the Treatment of Hemorrhoids — NCT01306877.
• Registry record last updated 2014-10-29; status last verified 2014-10.
• Results first posted 2014-10-29.
• 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 prospective, randomized, single-blind, parallel-group comparison of the EEA Hemorrhoid and Prolapse Stapling Set and the Endosurgery Proximate PPH03 Stapling Set for hemorrhoidopexy. Enrollment is recorded as 149, with a start of 2011-01 and primary completion in 2012-08.

The primary endpoint was the number of participants requiring intervention to stop intraoperative bleeding. The registry reports a per-protocol analysis that excluded misrandomized subjects and notes that its population differs from participant flow. The registry’s primary analysis is labeled non-inferiority or equivalence; the non-inferiority margin is not reported in the registry record.

Numerical secondary results are posted for staple-line location, length of stay, and operating-room time. Numerical results for the other named secondary outcomes, along with the original design assumptions, missing-data approach, and multiplicity plan, are not reported in the registry record. Interpretation should keep the reported analyses distinct from unadjusted recalculations and should account for their group-order conventions and analysis populations.