The Use of a High-frequency Ultrasonic Knife in Breast Cancer Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Use of a High-frequency Ultrasonic Knife in Breast Cancer Surgery (NCT00996632), a randomized na study. The primary outcome is Drainage Volume.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with single masking. It lists 94 participants in total and two procedure groups: 38 participants in the ultrasonic-knife group and 56 in the conventional-diathermy group. The trial record is marked completed. The recorded start was 2000-09 and primary completion was 2004-09. A study phase is listed as not applicable.

The trial enrolled people with operable breast carcinoma. The brief summary reports 1 male and 93 females and a mean age of 64.7 years. The study concerned axillary dissection during breast cancer surgery, with the two groups differentiated by the knife used. The registry identifies the ultrasonic procedure as Ultracision®, Ethicon Endo Surgery, and the comparator as a conventional diathermy knife.

Drainage volume at discharge was designated the primary outcome. Time of discharge was the posted secondary outcome. The primary description says the number of participants for analysis was determined by means of a power sample-size calculation, but the details of that calculation, including its target effect and assumptions, are not reported in the registry record. The actual group sizes are unequal; the equal-allocation assumption used for the separate planning illustrations should not be mistaken for the trial’s observed allocation.

The registry identifies single masking but does not state who was masked or how masking was implemented. Details of sequence generation, allocation concealment, recruitment procedures, or protocol deviations are not reported in the registry record. These omissions limit how fully the randomization process and conduct can be assessed from the record alone.

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:

Analysis population for the primary outcome, as defined in the registry: the number of participants for analysis was determined by mean of power sample size calculation

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 Drainage Volume, measured over discharge day.

The primary endpoint was the volume of axillary drainage in milliliters, measured on the day of discharge. The group results are reported as means and standard deviations. This endpoint quantifies the amount of drainage recorded at a clinically relevant point in the postoperative course. The investigators’ stated rationale was that lymphatic stasis and seroma formation are common complications of axillary lymphadenectomy, and that using an ultrasonic knife might reduce drainage amount and duration as well as hospital stay.

Drainage volume at discharge is one part of that stated hypothesis. A single measurement on discharge day does not, by itself, describe the total drainage accumulated over the full postoperative period or the duration of persistent drainage. The registry’s separate secondary outcome, time of discharge, relates to hospital stay, but the posted primary endpoint remains the drainage volume measure.

Means describe the average recorded volume within each group. Standard deviations describe the spread of individual observations around those group means. The reported standard deviations are large, indicating substantial variability in drainage volume within both groups. Because the mean is sensitive to unusually high observations, the group summaries alone do not reveal the shape of the individual-level distributions. The registry also reports a Wilcoxon (Mann-Whitney) analysis, a rank-based comparison that does not directly test the difference between arithmetic means.

7. Results Posted in the Registry

• Conventional: mean 525.20 versus 182.60 on control; difference 342.60 (95% CI 157.26 to 527.94), standardized effect d = 0.67; 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.

Time of Discharge

• 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:
  • Conventional: mean 8.10 versus 4.50 on control; difference 3.60 (95% CI 2.11 to 5.09), standardized effect d = 0.86; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Conventional than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time of discharge is the one posted secondary outcome. Its group pattern is directionally consistent with the primary result: the conventional group has a longer mean time to discharge than the ultrasonic group. This concordance gives the primary drainage finding a related clinical context, because the investigators’ stated hypothesis included hospital stay. It does not make the secondary measure equivalent to drainage volume, nor does it independently establish the primary result.

The secondary endpoint is a distinct outcome, with its own measurement and analysis. Its registry-reported Wilcoxon result and the unadjusted recalculation address different statistical quantities, just as for the primary endpoint. Interpretations should keep that distinction in view rather than treating all reported p-values or mean differences as outputs of one common analysis.

Unadjusted secondary results generally carry less weight than a prespecified primary result because multiple outcomes and comparisons create more opportunities for chance findings. This is a general statistical concern. The registry lists one secondary outcome and does not report a multiplicity adjustment, a hierarchy of tests, or a plan for interpreting secondary findings alongside the primary endpoint. It is therefore not possible to determine from the record whether the secondary analysis was confirmatory or exploratory.

The overall pattern is consistent across the two posted outcomes, but the registry’s reporting limitations remain relevant to both. The secondary result can inform the interpretation of the trial’s stated aims, while it should not be used as a substitute for the primary analysis or as independent proof that the primary endpoint reflects the full clinical course.

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

• Time of Discharge

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a Wilcoxon (Mann-Whitney) method for both the primary drainage outcome and the secondary discharge outcome. It does not give the test statistic, an effect estimate from that analysis, or a confidence interval. For each outcome, the posted p-value is the registry’s reported inferential result. Separate unadjusted calculations use the reported group means, standard deviations, and sample sizes to estimate a difference between means and its confidence interval. These answer related but not identical statistical questions.

What does a mean difference describe?

A mean is the arithmetic average of the recorded values within a group. A mean difference compares the two group averages, with its direction depending on which group is subtracted from which. The posted recalculations express the conventional-group mean relative to the ultrasonic-group mean. They are unadjusted: they do not account for covariates or other features of individual participants. The registry does not report an adjusted estimate for these outcomes.

A mean difference is easy to express in the measurement’s original units, which makes it useful for describing the scale of an average contrast. But it does not capture every feature of the outcome distribution. In particular, an average may be influenced by unusually large values. The registry gives means and standard deviations but not medians, ranges, or individual observations, so the distributional shape cannot be evaluated from the posted summaries.

Why is a rank-based test also reported?

The Wilcoxon (Mann-Whitney) test ranks observations across the two groups and assesses whether the distributions tend to differ in their ordering. It does not directly estimate the arithmetic mean difference shown by the unadjusted recalculation. Depending on the distributions, a rank-based comparison and a mean-based comparison can tell different parts of the story. A p-value from the rank test should therefore not be read as a test specifically of the posted difference between means.

Rank methods can be useful when observations are skewed or when extreme values make a mean-based model less suitable. That is a general statistical rationale, not evidence that this trial’s investigators selected the method for a particular distributional reason. The record does not describe diagnostic checks or explain why the Wilcoxon method was chosen.

What does the p-value say?

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test. It does not measure the probability that the null hypothesis is true, nor does it describe the size or practical importance of a difference. The primary registry-reported p-value is <0.05; the secondary registry-reported p-value is 0.05. The registry does not give additional detail about whether these were one-sided or two-sided tests, beyond the separate two-sided assumption used for the planning illustrations.

The recalculated unadjusted p-values are based on summary statistics and a mean-comparison framework. The registry’s own analysis uses a rank-based method. As a result, the reported and recalculated p-values should not be treated as duplicate estimates of the same analysis. Where the record marks a discrepancy, the sponsor’s own analysis takes precedence.

Why does over-dispersion matter?

In general, over-dispersion means that observations vary more than a statistical model expects. Greater variability can make an estimated group contrast less precise, because the group averages are less stable from sample to sample. The posted standard deviations show broad spread in drainage volumes and discharge times, so readers should consider the uncertainty around the averages rather than focus on the point estimates alone. This is a general explanation of variability; the registry does not report a formal over-dispersion assessment.

The group standard deviations also differ in magnitude, especially for the primary outcome. A single pooled spread is used in the effect-size and planning calculations, but this simplifying calculation is not the same as an adjusted trial analysis. No variance-model diagnostics or alternative variance estimates are reported in the registry record.

How should the confidence interval be read?

A confidence interval describes a range of effect values compatible with the data and the calculation’s assumptions. A narrower interval indicates greater statistical precision, while a wider one indicates less precision. It is not a range containing every participant’s result, and it does not account for uncertainties that the calculation leaves out, such as missing-data mechanisms or unreported analytical choices. The registry’s own Wilcoxon analyses do not have posted confidence intervals; intervals shown for the mean differences are recalculated from summary statistics.

For the primary mean difference, the recalculated 95% confidence interval is 157.3 to 527.9 milliliters. For time to discharge, the recalculated interval is 2.107 to 5.093 days. These are unadjusted estimates and should be distinguished from the registry-reported rank tests. They describe uncertainty under the recalculation’s method, not a sponsor-reported interval.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 342.6 milliliters, with a 95% confidence interval from 157.3 to 527.9 milliliters. The interval expresses uncertainty around the estimated contrast in group means under the unadjusted calculation. Its endpoints are both on the conventional-higher side of the difference as defined by the recalculation. The interval does not describe the spread of individual drainage volumes; the group standard deviations do that in a different way.

The observed standard deviations are 267.1 milliliters for the ultrasonic group and 629.0 milliliters for the conventional group. Those values indicate considerable within-group variability, particularly in the conventional group. The confidence interval reflects sampling uncertainty as modeled by the recalculation, but it does not resolve the uncertainty about distributional form, analysis populations, or missing outcomes because the registry does not report those details.

For the registry’s Wilcoxon analysis, no confidence interval or effect estimate is reported. Therefore, the rank-based result cannot be assessed from a posted interval in terms of the magnitude and precision of its own effect measure. The mean-difference interval is useful for understanding the scale of the average contrast, but it is not an interval for the rank test’s estimand and does not supersede the sponsor’s analysis.

A confidence interval is not a guarantee that the true effect lies within its limits, and it is not a range for individual participant outcomes. It is a measure of statistical uncertainty conditional on the data and method. The interval also does not address possible bias from missing observations, allocation procedures, or selective reporting. Those features are not described adequately 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 figures are participants per arm, not total participants or total events. Both outcomes are continuous measures, and the planning assumptions specify equal allocation between the two arms. The calculation uses a two-sided significance level of 0.05 and a normal approximation. It considers effects equal to the observed effect, 75% of the observed effect, and 50% of the observed effect. These are planning illustrations based on the observed effect, not the assumptions documented for the trial’s original design.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to detect the chosen effect under those assumptions with 80% power. In plain terms, power is the chance that a study would meet its statistical detection criterion if the assumed effect were the true effect and the model assumptions held. The 90% column gives the corresponding per-arm planning figure for a higher chance of detecting that assumed effect. Neither column reports the power achieved by the completed trial.

The figures increase as the assumed effect becomes smaller: a less pronounced difference is harder to distinguish from random variation, so the planning calculation requires more participants. The observed trial groups contained 38 and 56 participants, but those actual group sizes should not be confused with the equal-allocation planning assumption. The registry says a power sample-size calculation informed the number analyzed, yet the original target effect, allocation plan, and other design assumptions are not reported in the registry record. These planning calculations are not observed power.

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

Worked calculation for this trial

1. Observed difference Δ = 342.600; pooled standard deviation σ = 514.992.
2. n = 2 × (1.96 + 0.842)² × 514.992² / 342.600² = 35.5, rounded up to 36 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 342.6                      # observed difference in means
sigma <- 514.991812619596                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(996632)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 36 (80% power), 48 (90% power)
 75% of observed effect: n per arm = 64 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 142 (80% power), 190 (90% power)
power.t.test: 36.5 
Simulated power at n = 36 per arm: 0.796 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s reported primary analysis is a Wilcoxon (Mann-Whitney) comparison, with p <0.05. It does not report an effect estimate or confidence interval for that analysis. The unadjusted recalculation instead uses the posted means, standard deviations, and sample sizes to estimate a difference between group means, producing a mean difference of 342.6 milliliters and a 95% confidence interval from 157.3 to 527.9 milliliters. Its p-value is <0.001.

These results are not interchangeable. A rank-based test assesses group ordering or distributional differences, whereas the recalculated estimate targets an arithmetic mean contrast. Because the record flags a discrepancy between the sponsor-reported result and the recalculation, the sponsor’s own analysis takes precedence. The recalculation is a supplementary, unadjusted description of the posted summaries, not a correction to the reported test and not a substitute for an analysis using participant-level data.

The same distinction applies to the secondary outcome. The registry reports a Wilcoxon p-value of 0.05, while the separate unadjusted mean comparison is based on summary values. Without participant-level data and more complete analysis documentation, the recalculation cannot reproduce the sponsor’s method or establish why the outputs differ. The record does not report further explanation of that discrepancy.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies drainage volume as the primary outcome and time of discharge as a secondary outcome. It does not report a multiplicity strategy, such as an adjustment for testing more than one outcome or a prespecified hierarchy determining how results would be interpreted. Without that information, the family of analyses intended to support confirmatory conclusions is unclear. This matters because multiple tests can increase the chance of obtaining at least one apparently notable result by chance.

Missing-data handling is not reported in the registry record. The posted group summaries give sample sizes for each outcome, but do not explain whether those counts represent all randomized participants, whether any outcome observations were unavailable, or how missing values were handled. No imputation method, sensitivity analysis, or comparison of participants with and without outcome data is described. It is not possible to assess the effect of missing observations from the posted summaries alone.

The analysis population is also not clearly defined. The primary outcome description refers to the number of participants for analysis being determined by a power sample-size calculation, but it does not specify whether the analysis followed intention-to-treat, per-protocol, or another approach. The registry does not report exclusions after randomization or the reasons for any exclusions. These omissions prevent a full assessment of whether the analysis retained the benefits of random allocation.

Further analysis-plan details are not reported, including covariate adjustment, handling of protocol deviations, distributional checks, and the rationale for selecting the Wilcoxon method. The registry reports single masking but does not identify who was masked. These are reporting gaps, not evidence that any particular procedure was or was not followed. They limit how much can be concluded about the robustness of the results from the registry record alone.

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

The posted results describe differences in the two randomized groups’ average outcomes. For the primary endpoint, the conventional group’s mean drainage volume at discharge is higher than the ultrasonic group’s mean, and the unadjusted recalculation estimates the size and uncertainty of that mean contrast. The registry separately reports a rank-based primary comparison with p <0.05. The distinction between these analyses is important: the recalculated mean difference is not the effect estimate from the sponsor-reported test.

The results do not establish that every participant in one group had more drainage than every participant in the other. Group averages and rank-based tests summarize patterns across participants, while the posted standard deviations indicate substantial variability. Nor does drainage volume at discharge capture all aspects of drainage over time. The registry’s stated hypothesis includes drainage amount, duration, and hospital stay, but a single discharge-day volume does not measure all of those concepts.

The secondary discharge outcome follows a direction consistent with the primary group pattern. It offers related evidence about the trial’s stated interest in hospital stay, but it is a separate outcome and its registry analysis is not accompanied by a detailed multiplicity plan. It should therefore be read as context rather than as a second, fully independent confirmation.

The record does not provide enough information to evaluate missing outcomes, the precise analysis population, allocation concealment, or the original statistical plan. The reported group summaries also do not reveal the individual observations or outcome distributions. These limits mean that the registry results should be interpreted as reported statistical evidence from this trial, with uncertainty about important aspects of analysis and conduct. They are not a complete account of all possible outcomes or a basis for individual treatment decisions.

No treatment recommendation follows from these statistics. They describe the trial’s posted outcomes and their precision, not what any individual should choose. The registry also does not report enough adverse-event detail to support a comprehensive safety comparison.

17. Why This Trial Matters Statistically

This trial illustrates why endpoint definition and analysis method need to be read together. The primary outcome is a mean drainage volume at discharge, while the registry-reported inferential test is Wilcoxon (Mann-Whitney). The mean-based recalculation provides an intuitive contrast in milliliters and a confidence interval, but it does not reproduce the rank-based analysis. Keeping estimand and method aligned prevents a recalculated p-value from being mistaken for the trial’s reported test.

The large standard deviations relative to the group averages make variability an important part of interpretation. A point estimate can appear clear while the individual observations remain widely dispersed. Confidence intervals help express uncertainty around a mean contrast, but they do not replace distributional information or solve reporting gaps in the analysis population and missing-data handling.

The trial also demonstrates why planning illustrations must be separated from original design assumptions. The registry mentions a power calculation in connection with the number analyzed, but does not report its details. The displayed planning scenarios are calculations based on observed effects and specified assumptions, so they cannot be used to infer the study’s original target or its achieved power.

Finally, consistency in direction across a primary and related secondary endpoint can be informative, but unadjusted secondary tests need cautious interpretation when the multiplicity plan is unknown. A coherent reading considers effect size, uncertainty, variability, analytic method, outcome hierarchy, and record completeness rather than relying on a p-value alone.

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’s reported analysis does not include an effect estimate or confidence interval for either Wilcoxon comparison. That makes it difficult to assess the magnitude and precision of the sponsor-reported rank-based findings directly. The mean-difference estimates and intervals are unadjusted recalculations from summary statistics and do not replace those missing quantities.

Variability is substantial in both outcomes, and the drainage-volume standard deviations differ between groups. The registry does not provide individual observations, distribution plots, medians, or ranges, so the shape of the outcomes and the influence of extreme values cannot be assessed. This is particularly relevant when comparing a mean-based summary with a rank-based test.

The group sizes are unequal, with 38 participants in the ultrasonic group and 56 in the conventional group. The registry does not explain how allocation led to those group counts or report allocation concealment details. Although the study is described as randomized, the record does not give enough information to assess all features of randomization and implementation.

Important analysis details are absent: the original sample-size assumptions, analysis population, missing-data approach, protocol deviations, multiplicity handling, and adjustment strategy are not reported in the registry record. The single-masking designation is not accompanied by information about who was masked. The primary endpoint is measured at discharge and does not alone capture total drainage duration or the full postoperative course.

Adverse-event entries list zero participants at risk and zero affected in both groups, and no serious-event terms are listed; death counts are not reported in the registry record. These entries do not provide enough detail for a broad assessment of safety. The limitations reflect what the registry record documents and do not establish which procedures were used but left unreported.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Use of a High-frequency Ultrasonic Knife in Breast Cancer Surgery — NCT00996632.
• Registry record last updated 2009-11-11; status last verified 2009-11.
• Results first posted 2009-10-16.
• 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

NCT00996632 is a completed randomized, parallel-group trial comparing an ultrasonic knife with a conventional diathermy knife in breast cancer surgery. The registry lists 94 participants: 38 in the ultrasonic group and 56 in the conventional group. The primary outcome was axillary drainage volume at discharge; time of discharge was the secondary outcome.

The registry reports Wilcoxon (Mann-Whitney) analyses for both outcomes. Separate unadjusted recalculations estimate mean differences and confidence intervals from the posted group summaries. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence over those recalculations. The registry does not report several details needed for a fuller assessment, including the original design assumptions, missing-data handling, analysis population, and multiplicity plan.