NPWT in Patients Undergoing Surgical Procedures for Management of GI Malignancies: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for NPWT in Patients Undergoing Surgical Procedures for Management of GI Malignancies (NCT04955730), a randomized phase 2, phase 3 study. The primary outcome is Surgical Site Infection - Superficial Incisional.

2. Clinical Question

The clinical question is framed around a postoperative wound outcome, rather than a broader measure of cancer control or recovery. The trial’s brief summary describes measuring surgical site infection rates in participants with gastrointestinal neoplasms. The registry record names superficial incisional surgical site infection as the primary outcome and specifies a 30-day timeframe. This endpoint therefore concerns infection at the superficial incision during the stated period; it should not be read as covering every possible wound complication or infection beyond that definition.

The trial also considers whether participants return to intended oncologic therapy and how long it takes to initiate planned oncologic therapy. These are distinct outcomes from wound infection: they describe aspects of the postoperative treatment course, not the primary wound endpoint itself. The posted registry results do not include a numerical result for time to initiation of planned oncologic therapy.

3. Trial Design

The registry record describes a randomized, parallel-group trial with quadruple masking and lists the study as phase 2 and phase 3. The sponsor is H. Lee Moffitt Cancer Center and Research Institute. Enrollment is recorded as 290, and the status is completed. The listed study dates are a start date of 2021-08-05 and primary completion date of 2025-04-30.

Participants were assigned to one of two wound-care approaches after surgery. In the NPWT arm, negative pressure wound therapy was continued through postoperative day 3, replaced with a new NPWT dressing, and removed on postoperative day 7. In the standard-care arm, dressings were removed on postoperative day 3, with new sterile dressings applied if needed. The comparison therefore concerns these assigned postoperative wound-care strategies as described in the registry, not an isolated device feature detached from the treatment schedule.

The primary outcome was superficial incisional surgical site infection, measured as a count of participants with an event within 30 days after operation. The outcome description says all participants were evaluated. Posted primary outcome denominators are 183 in the NPWT group and 94 in the standard-care group. These outcome denominators do not account for all 290 participants listed as enrolled; the reasons for that difference are not reported in the registry record.

Two secondary outcomes are identified: return to intended oncologic therapy (RIOT) and time to initiation of planned oncologic therapy. The record includes numerical results for RIOT, but a numerical result for time to initiation is not reported in the registry record. The registry record does not report the randomization method, allocation concealment procedures, the roles covered by quadruple masking, or the protocol details behind the phase labels. Those details should not be inferred from the design labels alone.

The record lists five outcome measures, while the posted analysis count is zero. This means the registry does not list a count of formal analyses in that field; it does not establish that investigators performed no analyses. The trial’s original sample-size rationale and original statistical design assumptions 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

Analysis population for the primary outcome, as defined in the registry: All participants were evaluated

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 Surgical Site Infection - Superficial Incisional, measured over 30 days post operation.

The primary endpoint counts participants with superficial incisional surgical site infection within 30 days after operation. It is reported as a binary outcome: each participant either had a recorded event during the specified period or did not. The registry description identifies the population as all participants evaluated and gives the unit as participants.

This kind of endpoint is used to describe how often an event occurs in each assigned group. Comparing group proportions allows the result to be expressed on an absolute scale as a risk difference, as well as on relative scales such as a risk ratio or odds ratio. These scales answer related but different questions. An absolute difference describes the contrast in event probability, while relative measures describe the contrast as a ratio. Neither scale, by itself, establishes why an observed group difference occurred.

Superficial incisional infection is a clinically relevant postoperative outcome because it directly characterizes an event at the surgical incision. The defined 30-day period makes the time window explicit, but it also limits what the endpoint can establish: it does not describe infections occurring outside that window or other dimensions of postoperative recovery. The registry record does not provide further diagnostic criteria or adjudication procedures for identifying these infections.

The posted counts are 18 participants with an event among 183 in the NPWT group and 8 among 94 in the standard-care group. These counts describe the observed endpoint data, not a complete account of every possible complication. Interpretation depends on the outcome definition, how complete follow-up was, and how the comparison’s uncertainty is considered alongside the point estimate.

7. Results Posted in the Registry

• NPWT - Negative Pressure Wound Therapy: 9.8% (18/183) versus 8.5% (8/94) on control; risk difference 1.3 percentage points (95% CI -5.8 to 8.4), risk ratio 1.16 (0.52–2.56); unadjusted two-proportion z-test p = 0.720.

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.

Return to Intended Oncologic Therapy (RIOT)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • NPWT - Negative Pressure Wound Therapy: 89.1% (163/183) versus 87.2% (82/94) on control; risk difference 1.8 percentage points (95% CI -6.3 to 10.0), risk ratio 1.02 (0.93–1.12); unadjusted two-proportion z-test p = 0.651.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NPWT - Negative Pressure Wound Therapy and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes concern the postoperative oncology-treatment pathway rather than the primary wound-infection endpoint. The registry record lists return to intended oncologic therapy and time to initiation of planned oncologic therapy. The posted numerical RIOT comparison has a positive point estimate for NPWT, but its confidence interval includes zero and its unadjusted p-value is 0.651. A numerical result for time to initiation is not reported in the registry record.

At a broad level, the secondary result does not provide a statistically clear contrast between groups, and it does not overturn or resolve the uncertainty in the primary infection comparison. These outcomes address different questions, so concordance or divergence across them would not automatically establish a common treatment effect. Wound infection and return to cancer therapy may be related in clinical context, but the registry results do not establish that a difference in one outcome causes a difference in the other.

Secondary outcomes generally carry less evidential weight than a prespecified primary outcome, especially when several outcomes or analyses are considered. Testing multiple outcomes increases the opportunity for apparently notable results to arise by chance if no adjustment or hierarchy is specified. The registry record does not report a multiplicity strategy, a hierarchy for interpreting secondary outcomes, or a detailed analysis plan. The posted unadjusted secondary result should therefore be treated as descriptive and exploratory rather than as confirmatory evidence.

The missing numerical result for time to initiation also limits any overall reading of the secondary outcome pattern. The record identifies the outcome, but does not give a group estimate, uncertainty interval, or inferential result for it. No conclusion about whether the groups differed on that outcome can be drawn from its listing alone. Taken together, the secondary information offers limited context alongside the primary result; it does not establish a consistent advantage or disadvantage across all postoperative treatment outcomes.

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

• Return to Intended Oncologic Therapy (RIOT)
• Time to Initiation of Planned Oncologic Therapy

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the observed group summaries from what can be inferred about the populations from which participants were drawn. The primary outcome is binary, so each participant contributes an event status for the specified period. Group proportions describe the observed fraction with an event. A comparison then estimates how those proportions differ or relate, while an uncertainty interval describes the range of effects reasonably compatible with the data under the method used.

What does the risk difference describe?

The risk difference is the event proportion in the NPWT group minus the event proportion in the standard-care group. For the primary outcome, its estimate is 0.013. A positive value represents a higher observed event proportion in the NPWT group; a negative value represents a lower one. Zero represents equal proportions. The 95% confidence interval, -0.058 to 0.084, includes zero, so the data do not clearly establish the direction of the underlying difference. The interval also shows that effects of more than one size remain compatible with the observed data.

Risk difference is an absolute measure. It retains the scale of the event probability and can be useful when the practical meaning of an outcome depends on how much the event probability changes. It is not interchangeable with relative measures. A small absolute difference can coexist with a different-looking ratio, depending on the baseline event frequency. Interpretation should therefore keep the scale and the clinical context in view rather than treating one measure as a complete account.

How do relative measures differ?

The risk ratio compares event probabilities by division; a value of one is the null value, indicating equal probabilities. The odds ratio compares event odds rather than probabilities, and its null value is also one. The posted primary risk ratio is 1.156 and its confidence interval is 0.522 to 2.559. The posted odds ratio is 1.173 and its confidence interval is 0.49 to 2.807. These intervals include one, corresponding to no relative difference. Relative effects can be less intuitive when events are not common, and odds should not be read as probabilities. The absolute contrast remains useful alongside them.

What does the p-value add?

The unadjusted primary p-value is 0.72. A p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of effect size. A relatively large p-value does not prove there is no difference; it indicates that these data do not provide strong evidence against the null under the stated, unadjusted comparison. The registry record does not report a full statistical analysis plan or enough detail to reconstruct all testing decisions.

Confidence intervals and p-values are related summaries of uncertainty, but confidence intervals offer a range of effect estimates and make direction and scale more visible. A 95% confidence interval is produced by a procedure that, under its assumptions, would cover the true effect in 95% of repeated samples. It is not a statement that there is a 95% probability the fixed true effect lies within this particular interval. The interval’s width reflects both the amount of information and the variability inherent in the outcome.

Why are event counts and denominators important?

The primary counts are 18 of 183 in the NPWT arm and 8 of 94 in the standard-care arm. Counts alone cannot be compared without considering their denominators, because the group sizes differ. Conversely, proportions without counts can hide how much information supports them. Both are useful: counts establish the observed number of events, while denominators make the group proportions interpretable. The outcome denominators differ from the overall enrollment of 290, and the reasons are not reported in the registry record.

Binary-outcome analyses rely on assumptions about how participants enter the analysis and how outcomes are recorded. Random allocation helps balance prognostic characteristics on average, but it does not guarantee balance in every realized sample. Follow-up losses, deviations from assigned care, or outcome misclassification can affect interpretation. The registry record says all participants were evaluated for the primary endpoint, but it does not describe missing-data handling, whether the analysis followed intention-to-treat principles, or how outcome ascertainment was standardized.

What is the role of the planning illustrations?

The planning figures use the observed effect as a reference and illustrate participant requirements under stated assumptions. They are not the trial’s original design calculation. For an effect set to 100% of the observed effect, the illustration gives 7,444 participants per arm for 80% power and 9,965 per arm for 90% power. For 75% of the observed effect, it gives 13,020 per arm for 80% power and 17,429 per arm for 90% power. For 50% of the observed effect, it gives 28,809 per arm for 80% power and 38,566 per arm for 90% power. These are planning illustrations, not observed power.

The stated calculation assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. The planning description specifies that non-time-to-event figures are participants per arm; the primary binary outcome therefore uses participants per arm. Original sample-size assumptions for the trial itself are not reported in the registry record. Such illustrations depend on their assumptions and should not be interpreted as evidence that the trial was adequately or inadequately designed.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.013, and its 95% confidence interval extends from -0.058 to 0.084. This interval is wide enough to include effects in either direction, including no difference. It therefore conveys more than the point estimate alone: the direction and magnitude of the underlying difference remain uncertain. The unadjusted p-value of 0.72 is consistent with the interval’s inclusion of the null value, but it does not quantify the probability that the groups are the same.

Precision depends in part on how much information is available. The primary comparison includes 183 participants in the NPWT group and 94 in the standard-care group, with 18 and 8 events, respectively. Binary outcomes with relatively few events can yield substantial uncertainty, especially when group sizes are unequal. The registry record does not give a precision target or a prespecified clinically important difference, so the interval cannot be judged against such a benchmark from the record alone.

The secondary RIOT estimate is 0.018, with a 95% confidence interval from -0.063 to 0.100. It also spans zero and allows effects in either direction. The interval’s width means the point estimate should not be treated as a precise estimate of the underlying difference. No numerical result for time to initiation of planned oncologic therapy is reported in the registry record, so its precision cannot be evaluated.

A confidence interval does not correct for limitations in outcome measurement, follow-up, or analysis choices. Nor does a narrow interval by itself establish clinical importance. Precision is about statistical uncertainty around an estimate; clinical meaning also depends on the outcome and on what magnitude of difference would matter. Since the registry record does not report a threshold for meaningful difference, the results support describing uncertainty rather than classifying a difference as important or unimportant.

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 describe participants per arm for the binary outcomes, not total events. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is expressed as a fraction of the observed effect. These are illustrations based on the observed effect, not the trial’s original sample-size calculation; the trial’s original design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm under which a study would have an 80% chance of detecting the specified effect, assuming the planning model is correct and the effect is real. The 90% power column represents a higher chance of detecting that effect under those same assumptions and therefore requires more participants per arm. For 100% of the observed effect, the illustrations are 7,444 participants per arm for 80% power and 9,965 per arm for 90% power. For 75% of the observed effect, they are 13,020 and 17,429 per arm, respectively. For 50% of the observed effect, they are 28,809 and 38,566 per arm, respectively.

The pattern reflects a general statistical principle: smaller effects are harder to distinguish from random variation, so detecting them typically requires more participants. The effect fractions are planning scenarios, not claims that any one of those effect sizes is the true effect. Because the observed estimate is itself uncertain, calculations anchored to it inherit that uncertainty. These figures are not observed power; observed power is not a useful substitute for interpreting the confidence interval and estimate after a study has been completed.

The planning assumptions also include equal allocation, although the posted primary outcome denominators are unequal. The illustration is therefore a generic planning exercise under its stated assumptions, not a reconstruction of actual enrollment or the analysis conducted. It should be read as indicating how sample requirements change across assumed effects and desired power, not as evidence about the quality of the trial’s original planning.

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 = 0.085; treatment proportion p₁ = 0.098; average p̄ = 0.092.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4082 = 0.8001.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4081 = 0.3435.
4. n = (0.8001 + 0.3435)² / (0.0133)² = 7,443.9, rounded up to 7,444 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 <- 0.0851063829787234                          # control proportion
p1 <- 0.0983606557377049                          # 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(4955730)
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 = 7,444 (80% power), 9,965 (90% power)
 75% of observed effect: n per arm = 13,020 (80% power), 17,429 (90% power)
 50% of observed effect: n per arm = 28,809 (80% power), 38,566 (90% power)
power.prop.test: 7443.9 
Simulated power at n = 7,444 per arm: 0.799 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses more than one outcome or performs multiple comparisons. Even when each individual test uses the same significance threshold, the chance of at least one false-positive result across a family of tests can increase. Common approaches include prespecifying a primary outcome, defining a testing sequence, or adjusting inference across outcomes. The registry record identifies a primary endpoint and secondary outcomes, but does not report whether or how multiplicity was handled. The posted p-values are described as unadjusted, so secondary findings should not be treated as confirmatory without further information.

The primary endpoint is clearly named as superficial incisional surgical site infection within 30 days after operation. The record also lists RIOT and time to initiation of planned oncologic therapy as secondary outcomes. However, it does not report a formal statistical analysis plan, a prespecified outcome hierarchy, or an adjustment method for testing multiple outcomes. It is therefore not possible to determine from the registry record whether the analyses followed a prespecified multiplicity strategy.

Missing-data handling is another important uncertainty. The primary outcome description says all participants were evaluated, but the posted denominators are 183 and 94, while overall enrollment is 290. Reasons for the denominator difference are not reported in the registry record. The record does not describe how missing or unavailable outcome data were handled, whether any participants were excluded after randomization, or whether sensitivity analyses assessed the consequences of missingness. No missing-data assumption should be inferred from the statement that all participants were evaluated.

The analysis population is also not fully specified. The record does not state whether the primary comparison used an intention-to-treat population, a per-protocol population, or another definition. It does not report how crossovers, treatment discontinuation, or deviations from assigned wound care were addressed. These details matter because analysis choices can change the interpretation of a randomized comparison, particularly if post-randomization exclusions or incomplete follow-up differ between groups.

The record says the study was randomized and quadruple-masked, but does not explain the randomization process, allocation concealment, who was masked, or whether outcome assessors remained unaware of assignment. It also does not report interim analyses or stopping rules. These omissions do not show that procedures were absent; they mean those procedures cannot be evaluated from the registry record. Complete protocol and analysis documentation would be needed to assess these issues more fully.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ileus (4.2%), fever (3.1%), sepsis (3.1%), atelectasis (3.1%), pleural effusion (3.1%).

The registry’s adverse-event summaries use safety-group denominators that differ from the primary outcome denominators. Serious adverse events affected 36 of 194 participants in the NPWT safety group and 18 of 96 in the standard-care safety group. Other adverse events affected 62 of 194 and 29 of 96, respectively. Deaths are listed as 3 in the NPWT group and 4 in the standard-care group.

These figures describe counts of participants affected, not necessarily the total number of individual events. The registry record does not provide detail about event timing, severity grading beyond the serious-event classification, relatedness to the intervention, or how repeat events were counted. It also does not report statistical comparisons or uncertainty intervals for these safety summaries. They should therefore be read descriptively rather than as evidence of a reliable between-group difference.

The most frequently listed serious-event terms include ileus at 4.2%, fever at 3.1%, sepsis at 3.1%, atelectasis at 3.1%, pleural effusion at 3.1%, and wound infection at 2.6%. These percentages provide registry summaries of reported serious-event terms; the record does not give further detail needed to interpret them as comparative risks between groups. The safety figures are distinct from the primary endpoint, which specifically counts superficial incisional surgical site infection within 30 days after operation.

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

The posted results describe a randomized comparison of postoperative wound-care approaches and show the observed frequency of superficial incisional surgical site infection in each group. The estimated primary risk difference is 0.013, with a confidence interval that extends from -0.058 to 0.084. This means the observed data do not precisely determine whether the underlying event probability was lower or higher with NPWT, or how large a difference might be. The unadjusted p-value does not provide evidence of a statistically clear difference, but it does not prove equivalence.

The result does not establish that the two approaches have identical effects. A study can fail to detect a difference when effects are truly equal, but also when the data are too imprecise to distinguish a meaningful effect from chance variation. Demonstrating equivalence would require an equivalence margin and an analysis designed for that purpose. A noninferiority conclusion would likewise require a prespecified margin and suitable methods. Neither is reported in the registry record.

The findings also do not establish that either approach changes the risk of infection for every patient or in every surgical setting. The posted estimate pertains to the enrolled population, the recorded endpoint definition, and the stated follow-up window. The registry record does not provide detailed participant characteristics, operative subgroups, infection ascertainment procedures, or missing-data analyses that would support broader conclusions about particular subgroups or settings.

RIOT has a separate, uncertain comparison, and the numerical result for time to initiation of planned oncologic therapy is not reported. Those secondary data do not establish a clear difference in the postoperative treatment pathway. They should not be used as a substitute for the primary endpoint or as proof of a broader clinical benefit.

In practical statistical terms, the central message is uncertainty: the estimated primary contrast is small on the risk-difference scale, but its interval allows effects in either direction and of a range of sizes. Interpretation should retain both the observed counts and the uncertainty around the estimated contrast. No medical recommendation follows from these registry summaries alone.

17. Why This Trial Matters Statistically

This trial is statistically informative because it places a randomized comparison around a specific postoperative event and provides both event counts and an estimated contrast. Reporting the number of participants with superficial incisional surgical site infection alongside each group denominator helps readers understand the observed data rather than relying on a p-value alone. The risk difference and its confidence interval then show how uncertain the between-group contrast remains.

The comparison also illustrates why a non-significant result is not synonymous with no effect. The primary interval includes zero but also extends to values on either side, so it does not tightly constrain the possible direction or magnitude. Without a prespecified equivalence or noninferiority framework, similarity of point estimates cannot establish equivalence. This distinction is important in clinical trials, where readers may be tempted to treat a lack of statistical significance as proof that two strategies are interchangeable.

Another statistical lesson is that a trial’s observed sample and a planning illustration answer different questions. The registry’s planning figures show how assumed effect size and desired power relate to participants required under specified assumptions. They do not reveal the original design rationale, nor do they establish what the completed study was powered to detect. Their interpretation depends on the stated model and on the uncertainty of the observed effect used as a reference.

Finally, the secondary outcomes and safety summaries require careful separation from the primary endpoint. Multiple outcomes can broaden the clinical picture but also create multiplicity concerns, and the registry record does not describe an adjustment strategy. Together, these features make the record a useful example of reading estimates, intervals, outcomes, and design assumptions as distinct pieces of evidence rather than reducing a trial to a single significance test.

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.

Several trial-specific details needed for a fuller appraisal are not reported in the registry record. Although the study is described as randomized and quadruple-masked, the method of sequence generation, allocation concealment, and identities of the masked groups are not specified. The record also does not describe the criteria used to diagnose superficial incisional infection or how outcomes were adjudicated.

The outcome denominators differ from overall enrollment, and reasons for this difference are not reported. The registry does not explain missing-data procedures, the analysis population, or handling of deviations from assigned wound care. It is consequently not possible to determine from the posted record whether exclusions or incomplete follow-up could have influenced the estimates. The description that all participants were evaluated does not supply these missing details.

The registry includes a numerical RIOT result but no numerical result for time to initiation of planned oncologic therapy. It does not report a multiplicity strategy, detailed statistical analysis plan, original sample-size justification, interim analysis procedures, or stopping rules. These absent details limit assessment of whether analyses followed prespecified methods and how secondary findings should be weighted.

Safety summaries are descriptive and use denominators different from those in the primary outcome comparison. The record does not provide comparative uncertainty estimates for the adverse-event summaries, nor does it describe event attribution or timing in sufficient detail. The serious-event term percentages also lack further context about group-specific occurrence in the posted record.

Finally, outcome follow-up is limited by the stated endpoint windows: the primary infection outcome is defined at 30 days after operation, while RIOT is listed up to 12 months after surgery. The registry record does not provide detailed baseline characteristics or subgroup results to support broader generalization. These limitations do not imply that procedures were inadequate; they mark what cannot be evaluated from the available record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: NPWT in Patients Undergoing Surgical Procedures for Management of GI Malignancies — NCT04955730.
• Registry record last updated 2026-06-09; status last verified 2026-05.
• Results first posted 2026-03-02.
• 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

NCT04955730 is a completed randomized, parallel-group phase 2 and phase 3 trial sponsored by H. Lee Moffitt Cancer Center and Research Institute. It enrolled 290 participants undergoing surgical procedures for gastrointestinal malignancies and compared negative pressure wound therapy with standard wound care.

The primary endpoint was superficial incisional surgical site infection within 30 days after operation. The posted event counts were 18 of 183 in the NPWT group and 8 of 94 in the standard-care group. The estimated risk difference was 0.013, with a 95% confidence interval from -0.058 to 0.084 and an unadjusted p-value of 0.72.

RIOT is also reported, while a numerical result for time to initiation of planned oncologic therapy is not reported in the registry record. The record does not report the original sample-size rationale, detailed analysis plan, multiplicity handling, or missing-data procedures. The primary estimate is uncertain and should not be interpreted as proof of equivalence or as a medical recommendation.