Fast-track Surgery After Gynecological Oncology Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Fast-track Surgery After Gynecological Oncology Surgery (NCT02687412), a randomized na study. The primary outcome is Length of Hospitalization Post-operation.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. The study is marked completed and lists enrollment of 107. The fast-track surgery group had 50 participants in the primary outcome results, and the traditional surgery group had 57. The registry does not report the allocation ratio, the randomization sequence method, allocation concealment, or whether any procedures were used to protect the assignment process.

The study is titled “Fast-track Surgery After Gynecological Oncology Surgery.” Its stated aim concerns discharge after major gynecological or gynecological oncologic surgery and analysis of postoperative complications. The registry describes fast-track surgery as a multidisciplinary pathway and lists several preoperative and postoperative care elements. The comparator is described as traditional surgery. These descriptions do not establish which components were delivered to each participant or whether adherence to the pathways was assessed.

The registry lists the start date as 2016-11-21 and primary completion as 2017-09-02. The phase is recorded as NA. Participant eligibility criteria, recruitment setting, baseline clinical characteristics, the planned duration of follow-up for each outcome, and the original design assumptions are not reported in the registry record. The listed outcome timeframe is up to 12 months, while the primary outcome itself is defined as days from operation date to discharge date.

The primary outcome is continuous: mean postoperative hospital stay, with standard deviation as the measure of spread. Secondary outcomes listed include CRP and counts of participants with complications and specified postoperative events. Detailed registry results are available for only some of those outcomes. The trial record also reports adverse-event counts, but this does not by itself provide a complete account of all aspects of safety or clinical course.

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.

Population: Patients scheduled for gynaecological oncology surgery (including radical hysterectomy and lymphadenectomy, hysterectomy and lymphadenectomy, and cytoreductive procedures for both open and laparoscopic surgery)

6. Primary Endpoint

The registry lists the primary outcome as Length of Hospitalization Post-operation, measured over up to 12 months.

The primary endpoint is length of hospitalization after the operation, measured in days from operation date to discharge date. The registry reports the mean and standard deviation for each randomized group. A mean describes the average observed stay in a group, while the standard deviation describes how dispersed individual stays were around that group average. These summaries address the duration of postoperative hospitalization, rather than time to recovery in every broader sense.

Hospital stay is used as an outcome because discharge timing is directly relevant to the stated fast-track objective of earlier discharge. The study summary also frames the pathway around recovery, complications, readmission, and patient safety, but the primary endpoint alone does not capture all those dimensions. A shorter average stay would not, by itself, establish that discharge was appropriate, that recovery was otherwise better, or that readmission and safety outcomes were unchanged. Those questions require outcome data and analyses that address them directly.

The registry lists the primary outcome timeframe as up to 12 months, but describes the measurement as the interval from operation to discharge. It does not report further details about how discharge decisions were made, whether discharge criteria were standardized, or how the endpoint was handled for participants whose discharge information was unavailable.

7. Results Posted in the Registry

• Traditional Surgery: mean 9.67 versus 8.92 on control; difference 0.75 (95% CI -0.24 to 1.74), standardized effect d = 0.28; z-test p = 0.136.

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.

CRP

• 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:
  • Traditional Surgery: mean 62.50 versus 42.12 on control; difference 20.37 (95% CI 7.79 to 32.96), standardized effect d = 0.60; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Traditional Surgery than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Complications

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Traditional Surgery: 22.8% (13/57) versus 6.0% (3/50) on control; risk difference 16.8 percentage points (95% CI 4.1 to 29.5), risk ratio 3.80 (1.15–12.58); unadjusted two-proportion z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Traditional Surgery than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Infection,

• 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:
  • Traditional Surgery: 21.1% (12/57) versus 4.0% (2/50) on control; risk difference 17.1 percentage points (95% CI 5.2 to 28.9), risk ratio 5.26 (1.24–22.39); unadjusted two-proportion z-test p = 0.009.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Traditional Surgery than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results show a broadly similar direction across the outcomes with numerical comparisons available: group summaries for CRP and the reported event counts are lower in the fast-track group than in the traditional-surgery group. This pattern is consistent with the direction of the primary mean comparison, where the observed average stay is also lower in the fast-track arm. It does not make the secondary measures interchangeable with length of stay; CRP and event counts capture different aspects of postoperative outcomes.

The registry lists additional secondary outcomes, but detailed numerical results for all listed outcomes are not reported in the registry record. The available results therefore do not establish a complete pattern across every planned or listed postoperative measure. In particular, a coherent direction among the outcomes with results does not answer whether unreported outcomes had similar, different, or inconclusive findings.

Unadjusted secondary results carry less weight than a prespecified primary analysis because multiple outcomes create multiple opportunities for a nominally small p-value. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary endpoints. Without such a plan, each secondary p-value should be treated cautiously and in context, rather than as independent confirmation of an overall treatment effect. The number of comparisons and the selective availability of detailed results also affect how confidently the pattern can be generalized.

Secondary outcomes can help describe the breadth of observed differences and generate questions for further study. They do not override the primary result, and they cannot by themselves establish that the fast-track pathway caused the observed differences. The registry does not report an integrated analysis combining the primary and secondary outcomes.

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

• CRP
• Number of Participants With Complications
• Number of Participants With Infection,
• Number of Participants With Postoperative Nausea and Vomiting (PONV)
• Number of Participants With Ileus
• Number of Participants With Postoperative Haemorrhage
• Number of Participants With Postoperative Thrombosis
• PCT Calcitonin Postoperative

9. Statistical Interpretation

10. Statistical Methods Explained

Continuous outcomes are summarized by a mean and standard deviation. The mean is the arithmetic average of the observed values within a group. The standard deviation describes how spread out those values are around the mean; it is not the standard error and it is not a confidence interval. A standard error instead describes the sampling uncertainty of an estimated statistic, such as a group mean.

What does the mean difference express?

For the primary outcome, the comparison is expressed as the mean in traditional surgery minus the mean in fast-track surgery. With that direction, a positive estimate means the traditional-surgery group had the larger observed mean stay; a negative estimate means the fast-track group had the larger observed mean. The recalculated estimate is 0.75 days. This is an unadjusted comparison based on the posted group summaries, not an estimate adjusted for baseline characteristics or other covariates.

A mean difference retains the original measurement scale, which makes it directly interpretable in days for length of stay and mg/L for CRP. A standardized effect, such as the reported d of 0.281 for the primary comparison, expresses the contrast relative to a pooled standard deviation. Standardized effects can help compare contrasts measured on different scales, but they do not retain the original units and should not be treated as measures of clinical importance by themselves.

What does the t-test assess?

The sponsor reports a two-sided t-test for the primary comparison. In general, a two-sided test assesses evidence against a null hypothesis of no difference in either direction. The t-test uses the observed group means and their uncertainty to evaluate whether a difference as large as the observed one would be unusual under that null model. A p-value is not the probability that the null hypothesis is true, nor does it measure the probability that the finding is due to chance. It is a measure of how compatible the observed data are with the test’s null model and assumptions.

The recalculation uses an unadjusted comparison of the posted summary statistics. The registry’s reported p-value is the sponsor’s own analysis result. The two p-values are close, but the registry does not report the sponsor’s full primary effect estimate or an interval for that estimate. The recalculated estimate and interval therefore add a summary based on the posted group means and standard deviations; they do not replace details that the registry does not report.

How should an interval be read?

A confidence interval describes a range of effect values compatible with the data under the method used to construct it. In general, wider intervals indicate less precision than narrower intervals. The primary recalculated interval runs from -0.236 to 1.736 days. Because it spans zero, the data are compatible with no mean difference as well as with a positive or negative difference within the stated range. The confidence level for this primary recalculated interval is not reported in the registry record, so it should not be assigned a level based on assumption.

How are the binary outcomes summarized?

For an outcome recorded as whether a participant experienced an event, the record gives event counts and group denominators. A risk difference compares the event proportions by subtracting one group’s proportion from the other’s. Its sign depends on the order of subtraction; the comparisons in the posted recalculations use traditional surgery relative to fast-track surgery. The registry’s analyses for the participant-count outcomes use a chi-squared test. In general, that test assesses whether the observed distribution of event counts across groups is compatible with equal event proportions under its assumptions.

Risk differences are absolute contrasts on the probability scale, whereas relative measures such as risk ratios or odds ratios compare groups on a relative scale. Relative measures can appear large when events are uncommon, and their intervals may be wide when the amount of event information is limited. These measures are not interchangeable, and none removes uncertainty in the underlying observations. The registry does not report adjusted binary-outcome analyses.

Why can dispersion matter?

General statistical explanation: if observations vary more than a model assumes, standard errors and intervals based on that model can be too optimistic. For continuous outcomes, the reported standard deviations help describe observed spread. For count outcomes, over-dispersion means that counts vary more than expected under a chosen count model; it can make standard errors too small if ignored. The posted primary endpoint is a continuous measure analyzed with a t-test, and the reported secondary binary outcomes use chi-squared tests. The registry does not report a count regression model or an over-dispersion assessment.

All recalculated comparisons are simple unadjusted re-calculations from posted summary statistics. The registry does not report details sufficient to assess every analytical choice, including missing-data handling, baseline adjustment, or sensitivity analyses. Results should be interpreted as summaries of the analyses that are reported, not as evidence that unreported methods were or were not used.

11. Confidence Intervals and Precision

The primary recalculated interval for the mean difference extends from -0.236 to 1.736 days. Its endpoints indicate that the observed data are compatible with a range that includes a small difference in the opposite direction and a larger difference in the direction of the traditional-surgery group having a longer mean stay. The interval crosses zero, so it does not isolate a difference in one direction. The registry does not report the confidence level for this primary recalculated interval.

Precision concerns the range of effect values that remain compatible with the data, not only whether a p-value crosses a conventional threshold. The interval’s span indicates that the primary comparison does not pin down the mean difference very narrowly. A p-value alone cannot show this range. Likewise, the group standard deviations describe participant-level variation and should not be read as the uncertainty around the mean difference.

The sponsor reports p = 0.141 for the primary two-sided t-test, while the unadjusted recalculation gives p = 0.136. Both are consistent with the interval’s inclusion of zero. The record does not report a sponsor-derived primary confidence interval or effect estimate, so the primary interval is the recalculated one. The confidence interval reported for CRP is a secondary-outcome result and should not be mistaken for the primary endpoint’s interval.

More precise estimation would generally require more information, but precision alone does not establish that an effect is meaningful or that the trial’s design was adequate for a particular target. The original sample-size justification and design assumptions are not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s own original design assumptions. For continuous and binary outcomes, the figures are participants per arm. They are not total sample sizes. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. For time-to-event outcomes, figures would refer to total events using the Schoenfeld method, but the posted outcomes are not presented as time-to-event outcomes.

The 80% power column gives the illustrative number of participants per arm under which the stated effect would be detected in 80% of repetitions under the planning assumptions, if the assumed effect and model were correct. The 90% power column uses a higher target probability of detecting that effect and therefore generally calls for more participants per arm. The rows for 100%, 75%, and 50% of the observed effect explore how the planning figure changes when the target effect is smaller than the observed estimate.

Smaller effects are harder to distinguish from random variation, so the planning figures rise as the effect used for planning becomes smaller. These calculations are not a reconstruction of the trial’s original design: the registry does not report the original sample-size assumptions or justification. The calculations are based on the observed effect and chosen planning assumptions, and they are not observed power. They do not measure the probability that the trial’s result is true or guarantee that another study will obtain the same result.

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 = 0.750; pooled standard deviation σ = 2.666.
2. n = 2 × (1.96 + 0.842)² × 2.666² / 0.750² = 198.4, rounded up to 199 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 <- 0.75                      # observed difference in means
sigma <- 2.66637300466383                     # 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(2687412)
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 = 199 (80% power), 266 (90% power)
 75% of observed effect: n per arm = 353 (80% power), 473 (90% power)
 50% of observed effect: n per arm = 794 (80% power), 1,063 (90% power)
power.t.test: 199.4 
Simulated power at n = 199 per arm: 0.802 (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

For the primary endpoint, the registry reports the sponsor’s two-sided t-test with p = 0.141. The unadjusted recalculation from the posted group summaries gives a mean difference of 0.75 days, an interval from -0.236 to 1.736, and p = 0.136. The two p-values are close, and both indicate that the reported primary comparison does not provide clear statistical evidence of a difference under the respective analyses.

The registry does not report a sponsor-derived primary effect estimate or confidence interval alongside that p-value. The recalculation supplies an unadjusted estimate and interval from the posted means, standard deviations, and group sizes. It is not an alternative sponsor analysis, and it does not establish what other modeling or data-handling decisions may have been made.

The sponsor’s reported results are also available for the secondary outcomes with analyses posted. Where both a recalculation and sponsor analysis are listed, they are separate presentations of the comparison, with the sponsor’s test and p-value identifying the registry-reported analysis. The registry does not report a discrepancy flag for this trial. Any differences between a recalculation and a reported result should be understood in light of the fact that recalculations use summary statistics and may not reproduce every detail of the original analysis.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes or comparisons are tested. Even if each test is conducted at a conventional significance level, testing more outcomes increases the chance that at least one result will appear statistically significant by chance under a set of null effects. This is a general statistical concern, not a claim that any particular reported finding is false.

The registry reports a primary endpoint and several secondary outcomes, including CRP and participant counts for postoperative events. It does not report a multiplicity adjustment, a prespecified testing hierarchy, or a strategy for deciding which secondary results should be considered confirmatory. Consequently, the secondary p-values should be read as unadjusted evidence and given less inferential weight than the primary outcome. The registry also does not report whether additional analyses were conducted but not posted.

Missing-data handling is not reported in the registry record. There is no outcome-specific account of missing observations, reasons for missingness, or methods used to address missing values. The primary outcome group summaries list 50 participants for fast-track surgery and 57 for traditional surgery, but the record does not clarify whether these are all randomized participants, all participants with available endpoint data, or another analysis set. The corresponding analysis-population definitions are not reported.

The registry does not report whether analyses followed intention-to-treat principles, whether participants were excluded after randomization, or whether sensitivity analyses were conducted. Randomized allocation can support a fair comparison when the analysis preserves the randomized groups and missing data are handled appropriately, but the record does not contain enough detail to evaluate those conditions. The absence of reported details should not be interpreted as evidence that a particular method was or was not used.

Baseline adjustment, subgroup analyses, interim analyses, and the statistical analysis plan are not reported in the registry record. Without those details, readers cannot assess whether the posted results correspond to a prespecified analysis or how decisions about outcomes and analyses were made.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

The adverse-event record reports zero serious adverse events in the fast-track group and zero in the traditional-surgery group. The reported numbers at risk for the serious-event summaries are 50 and 57, respectively. The record also reports zero other adverse events and zero deaths in both groups, with the same group-specific numbers at risk.

These figures describe what is recorded in the registry; they are not proof that no adverse events occurred outside the definitions or reporting procedures used. The registry does not provide serious-event terms, event definitions, event ascertainment methods, severity breakdowns beyond the serious and other categories, or further detail about timing and relatedness. It also does not report enough information to assess whether adverse-event capture was complete or comparable across groups.

Zero reported events in these summaries should therefore be read narrowly. They do not establish that the pathways have identical safety profiles or that the risk of an event is absent. The registry’s adverse-event figures are a limited safety account and should be considered alongside the outcome definitions and the reporting limitations.

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

The registry’s primary result describes a lower observed mean postoperative stay in the fast-track group than in the traditional-surgery group. The unadjusted recalculated mean difference is 0.75 days, but its interval includes zero and the sponsor-reported primary p-value is 0.141. The evidence in the registry record therefore does not establish a clear difference in mean length of stay between the groups.

This is not the same as demonstrating that the pathways are equivalent. Equivalence requires a prespecified margin defining what range of differences would count as acceptably similar, and the registry does not report such a margin. Nor does the result establish non-inferiority, because no non-inferiority margin or corresponding analysis is reported. An inconclusive comparison should not be converted into proof of no effect.

The primary endpoint concerns days from operation to discharge. It does not by itself establish the quality of recovery, patient satisfaction, complication severity, readmission, healthcare costs, or whether discharge was earlier than expected. Although the study summary discusses several of these motivations, the primary endpoint cannot answer all of them. Secondary outcomes provide additional information, but their interpretation is limited by multiple comparisons and the absence of reported adjustment or a testing hierarchy.

The results also do not prove that the pathway itself caused the observed group differences. Randomization is a design strength, but the registry does not report participant flow, baseline characteristics, analysis populations, missing-data methods, or adherence to the pathways. Those details matter when evaluating how well the comparison was conducted and how broadly the findings apply.

The appropriate reading is therefore descriptive and measured: the posted group summaries show observed differences, while the primary analysis leaves substantial uncertainty about the size and direction of the underlying mean contrast. The registry record does not support a broader claim that the fast-track pathway is effective, ineffective, safe, unsafe, equivalent, or superior across all outcomes.

18. Why This Trial Matters Statistically

This trial is statistically informative because it places a randomized comparison around a practical and clearly defined outcome: days from operation to discharge. Reporting group means and standard deviations makes the primary outcome interpretable in its original units, while an unadjusted difference and interval help distinguish the observed contrast from the uncertainty around it.

The result illustrates why a group mean difference, a p-value, and an interval answer related but distinct questions. The observed mean is lower in one group, the sponsor’s test does not provide clear statistical evidence of a difference, and the recalculated interval spans zero while allowing a range of possible contrasts. Treating these as complementary pieces of evidence is more informative than relying on the direction of the means or a significance label alone.

The secondary results also illustrate the need to interpret a family of outcomes cautiously. A similar direction across several reported measures can be notable, but multiple unadjusted tests and incomplete reporting of detailed secondary results limit the strength of that pattern. Prespecification, transparent analysis populations, missing-data reporting, and a stated multiplicity strategy would help readers distinguish confirmatory evidence from exploratory findings.

Finally, the planning illustrations connect observed effects to the amount of information that future studies might require under stated assumptions. They are not evidence that the trial was adequately powered or that its observed effects will recur. The registry does not report the original design justification, which remains important context for evaluating whether the study was intended to estimate a particular effect with a chosen degree of precision.

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.

Important design and reporting details are not reported in the registry record. These include eligibility criteria, recruitment setting, baseline characteristics, the randomization and allocation-concealment procedures, participant flow, and whether the analysis retained participants in their assigned groups. Without these details, it is difficult to assess the comparability of the groups as analyzed or the population to which the results may apply.

The registry does not describe the original sample-size justification or the statistical analysis plan. It also does not report whether interim analyses, baseline-adjusted models, or sensitivity analyses were used. The planning figures based on observed effects cannot substitute for the trial’s original design rationale.

The primary outcome is days from operation to discharge, but discharge criteria and decision-making procedures are not reported. Because discharge timing can depend on clinical practice and local arrangements, the record does not show whether those factors were standardized across groups. Details about pathway implementation and participant adherence are also not reported, so the comparison does not establish which components were received or how consistently they were applied.

Missing-data methods and outcome-specific missingness are not reported. The registry’s detailed secondary results cover only some of the outcomes listed, and the record does not describe a multiplicity strategy. These gaps constrain interpretation of the secondary pattern. The serious and other adverse-event summaries contain no reported events, but event definitions, ascertainment methods, and completeness of reporting are not described. These limitations apply to interpretation of this registry record and do not establish that the unreported procedures or information were absent from the study itself.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Fast-track Surgery After Gynecological Oncology Surgery — NCT02687412.
• Registry record last updated 2019-09-26; status last verified 2019-08.
• Results first posted 2019-09-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed randomized, unmasked, parallel-group trial comparing fast-track surgery with traditional surgery after gynecological oncology surgery. Enrollment is listed as 107. The primary endpoint is mean length of hospitalization after operation, defined as days from operation to discharge.

The observed mean stay was 8.92 days in the fast-track group and 9.67 days in the traditional-surgery group. The recalculated unadjusted difference is 0.75 days, with an interval from -0.236 to 1.736; the sponsor-reported two-sided t-test gives p = 0.141. These results do not establish a clear primary-outcome difference. Secondary results are reported for selected outcomes, but their interpretation is limited by unadjusted testing and incomplete reporting. The registry does not report several design, analysis, and missing-data details needed for a fuller assessment.